Reviewer #1 (Public Review):

While CRISPR/Cas technology has greatly facilitated the ability to perform precise genome edits in Leishmania spp., the lack of a non-homologous DNA end-joining (NHEJ) pathway in Leishmania has prevented researchers from performing large-scale Cas-based perturbation screens. With the introduction of base editing technology to the Leishmania field, the Beneke lab has begun to address this challenge (Engstler and Beneke, 2023).

In this study, the authors build on their previously published protocols and develop a strategy that:

(1) allows for very high editing efficiency. The cell editing frequency of 1 edit per 70 cells reported in this study represents a 400-fold improvement over the previously published protocol,<br /> (2) reduces the negative effects of high sgRNA levels on parasite growth by using a weaker T7 promoter to drive sgRNA transcription.

The combination of these two improvements should open the door to exciting large-scale screens and thus be of great interest to researchers working with Leishmania and beyond.

Reviewer #2 (Public Review):

Summary:

Previously, the authors published a Leishmania cytosine base editor (CBE) genetic tool that enables the generation of functionally null mutants. This works by utilising a CAS9-cytidine deaminase variant that is targeted to a genetic locus by a small guide RNA (sgRNA) and causes cytosine to thymine conversion. This has the potential to generate a premature stop codon and therefore a loss of function mutant.

CBE has advantages over existing CAS-based knockout tools because it allows the targeting of multicopy gene families and, potentially, the easier generation of pooled loss of function mutants in complex population experiments. Although successful, the first generation of this genetic tool had several limitations that may have prevented its wider adoption, especially in complex genome-wide screens. These include nonspecific toxicity of the sgRNAs, low transfection efficiencies, low editing efficiencies, a proportion of transfectants that express multiple different sgRNAs, and insufficient effectivity in some Leishmania species.

Here, the authors set out to systematically solve each of these limitations. By trialling different transfection conditions and different CAS12a cut sites to promote sgRNA expression cassette integration, they increase the transfection efficiency 400-fold and ensure that only a single sgRNA expression cassette integrates that edits with high efficiencies. By trialling different T7 promoters, they significantly reduce the non-specific toxicity of sgRNA expression whilst retaining high editing efficiencies in several Leishmania species (Leishmania major, L. mexicana and L. donovani). By improving the sgRNA design, the authors predict that null mutants will be more efficiently produced after editing.

This tool will find adoption for producing null mutants of single-copy genes, multicopy gene families, and potentially genome-wide mutational analyses.

Strengths:

This is an impressive and thorough study that significantly improves the previous iteration of the CBE. The approach is careful and systematic and reflects the authors' excellent experience developing CRISPR tools. The quality of data and analysis is high and data are clearly presented.

Weaknesses:

Figure 4 shows that editing of PF16 is 'reversed' between day 6 and day 16 in L. mexicana WTpTB107 cells. The authors reasonably conclude that in drug-selected cells there is a mixed population of edited and non-edited cells, possibly due to mis-integration of the sgRNA expression construct, and non-edited cells outcompete edited cells due to a growth defect in PF16 loss of function mutants. However, this suggests that the CBE tool will not work well for producing mutants with strong fitness phenotypes without incorporating a limiting dilution cloning step (at least in L. mexicana and quite possibly other Leishmania species). Furthermore, it suggests it will not be possible to incorporate genes associated with a growth defect into a pooled drop-out screen as described in the paper. This issue is not well explored in the paper and the authors have not validated their tool on a gene associated with a severe growth defect, or shown that their tool works in a mixed population setting.

Although welcome, the improvements to the crRNA CBE design tool are hypothetical and untested.

The Sanger and Oxford Nanopore Technology analyses on integration sites of the sgRNA expression cassette integration will not detect the mis-integration of the sgRNA expression construct into an entirely different locus.

Reviewer #3 (Public Review):

Genetic manipulation of Leishmania has some challenges, including some limitations in the DNA repair strategies that are present in the organism and the absence of RNA interference in many species. The senior author has contributed significantly to expanding the available routes towards Leishmania genetic manipulation by developing and adapting CRISPR-Cas9 tools to allow gene manipulation via DNA double-strand break repair and, more recently, base modification. This work seeks to improve on some limitations in the tools previously described for the latter approach of base modification leading to base change.

The work in the paper is meticulously described, with solid evidence for most of the improvements that are claimed: Figure1 clearly describes reduced impairment in the growth of parasites expressing sgRNAs via changes in promoters; Figures 2 and 3 compellingly document the usefulness of using AsCas12a for integration after transformation; and Figures 1 and 4 demonstrate the capacity of the combined modifications to efficiently edit a gene in three different Leishmania species. There is little doubt these new tools will be adopted by the Leishmania community, adding to the growing arsenal of approaches for genetic manipulation.

There are two weaknesses the authors may wish to address, one smaller and one larger.

(1) The main advance claimed here is in this section title: 'Integration of CBE sgRNA expression cassettes via AsCas12a ultra-introduced DSBs increase editing rates', with the evidence for this presented in Figure 4. It is hard work in the submission to discern what direct evidence there is for editing rates being improved relative to earlier, Cas9-based approaches. Did they directly compare the editing by the new and old approach? If not, can they more clearly explain how they are able to make this claim, either by adding text or a new figure? A side-by-side comparison would emphasise the advance of the new approach more clearly.

(2) The ultimate, stated goal of this work is (abstract) to 'enable a variety of loss-of-function screens', as the older approach had some limitations. This goal is not tested for the new tools that have been developed here; the experiment in Figure 5 merely shows that they can, not unexpectedly, make a gene mutant, which was already possible with available tools. Thus, to what extent is this paper describing a step forward? Why have the authors not run an experiment - even the same one that was described previously in Engstler and Beneke (2023) - to show that the new approach improves on previous tools in such a screen, either in scale or accuracy?

Author response:

We would like to thank all reviewers and editors for their thorough peer review and valuable suggestions. In these provisional responses, we summarize the main concerns raised by the reviewers and outline our planned revisions to address them in the manuscript.

Overall, we are pleased to note that the reviewers agree on the potential value of our updated toolbox for gene editing, highlighting its various applications. However, they also raised several valid concerns, which we have summarized and responded to as follows:

(1) Mutant phenotypes in transfected populations can be occasionally reversed or escaped. This suggests it will not be possible to detect growth-associated phenotypes in pooled screens. An experiment with a pooled loss-of-function screen to test this is missing.

Escapes or reversals of mutant phenotypes have been observed with other genetic tools used for loss-of-function screening, including lentiviral CRISPR approaches in mammalian systems and RNAi in Trypanosoma brucei. Cells can escape phenotypes through various mechanisms, such as promoter silencing or selection of non-deleterious mutations. Additionally, not every CRISPR guide is efficient in generating a mutant phenotype, and RNAi constructs can also vary in their effectiveness. Despite these challenges, genome-wide loss-of-function screens have been successfully carried out in mammalian cells and Trypanosoma parasites. Therefore, we believe that the observed escape of one mutant phenotype does not preclude the detection of growth-associated or other phenotypes in pooled screens. Moreover, we did not observe a reversal of the mutant phenotype in L. mexicana, L. donovani, and L. major parasites expressing tdTomato from an expression cassette integrated into the 18S rRNA SSU locus (Figure 4). However, the reviewers are rightfully requesting a pooled loss-of-function screen to validate this. Since submitting this manuscript, we have conducted multiple pooled loss-of-function screens, which have confirmed the ability of our here presented method to detect a range of mutant phenotypes in pooled screening formats. We will include these results in our revised manuscript.

(2) The possibility of mis-integration of the CBE sgRNA expression construct into an entirely different locus is not explored.

We plan to reanalyze our ONT sequencing data to verify if the CBE sgRNA expression construct was integrated into an unintended loci. If we detect any mis-integration events, we will evaluate their potential negative impacts and discuss these findings in the revised manuscript.

(3) The achieved increase in editing efficiency compared to the previous base editing method could be more clearly presented.

We have directly compared our improved method to our previous base editing method in Figures 1E and 4, demonstrating higher editing rates in a much shorter time. In the revised manuscript, we will present and describe the increase in editing rate more clearly.

(4) The improvements on CBE sgRNA guide design are hypothetical and untested.

We agree that the improvements to the CBE sgRNA design are currently hypothetical. We plan to systematically test our guide design principles in future studies. Since this will require testing hundreds of guides to draw robust conclusions, we believe that this aspect is beyond the scope of the current study. However, we will discuss our plans for future validation in the revised manuscript.

Overall, we appreciate the reviewers' insights and are committed to addressing their concerns thoroughly. We believe that the planned revisions and additional experiments will significantly strengthen our manuscript and provide a more comprehensive evaluation of our updated gene editing toolbox.

Reviewer #1 (Public Review):

Summary:

Moir, Merheb et al. present an intriguing investigation into the pathogenesis of Pol III variants associated with neurodegeneration. They established an inducible mouse model to overcome developmental lethality, administering 5 doses of tamoxifen to initiate the knock-in of the mutant allele. Subsequent behavioral assessments and histological analyses revealed potential neurological deficits. Robust analyses of the tRNA transcriptome, conducted via northern blotting and RNA sequencing, suggested a selective deleterious effect of the variant on the cerebrum, in contrast to the cerebellum and non-cerebral tissues. Through this work, the authors identified molecular changes caused by Pol III mutations, particularly in the tRNA transcriptome, and demonstrated its relative progression and selectivity in brain tissue. Overall, this study provides valuable insights into the neurological manifestations of certain genetic disorders and sheds light on transcripts/products that are constitutively expressed in various tissues.

Strengths:

The authors utilize an innovative mouse model to constitutively knock in the gene, enhancing the study's robustness. Behavioral data collection using a spectrometer reduces experimenter bias and effectively complements the neurological disorder manifestations. Transcriptome analyses are extensive and informative, covering various tissue types and identifying stress response elements and mitochondrial transcriptome patterns. Additionally, metabolic studies involving pancreatic activity and glucose consumption were conducted to eliminate potential glucose dysfunction, strengthening the histological analyses.

Weaknesses:

The study could have explored identifying the extent of changes in the tRNA transcriptome among different cell types in the cerebrum. Although the authors attempted to show the temporal progression of tRNA transcriptome changes between P42 and P75 mice, the causal link was not established. A subsequent rescue experiment in the future could address this gap.

Nonetheless, the claims and conclusions are supported by the presented data.

Reviewer #2 (Public Review):

Summary:

The study "Molecular basis of neurodegeneration in a mouse model of Polr3 related disease" by Moir et.al. showed that how RNA Pol III mutation affects production, maturation and transport of tRNAs. Furthermore, their study suggested that RNA pol III mutation leads to behavioural deficits that are commonly observed in neurodegeneration. Although, this study used a mouse model to establish theses aspects, the study seems to lack a clear direction and mechanism as to how the altered level of tRNA affects locomotor behaviour. They should have used conditional mouse to delete the gene in specific brain area to test their hypothesis. Otherwise, this study shows a more generalized developmental effect rather than specific function of altered tRNA level. This is very evident from their bulk RNA sequencing study. This study provides some discrete information rather than a coherent story.

Strengths:

The study created a mouse model to investigate role of RNA PolIII transcription. Furthermore, the study provided RNA seq analysis of the mutant mice and highlighted expression specific transcripts affected by the RNA PolIII mutation.

Weaknesses:

1) The abstract is not clearly written. It is hard to interpret what is the objective of the study and why they are important to investigate. For example: "The molecular basis of disease pathogenesis is unknown." Which disease? 4H leukodystrophy? All neurodegenerative disease?

2) How cerebral pathology and exocrine pancreatic atrophy are related? How altered tRNA level connects these two axes?

3) Authors mentioned that previously observed reduction mature tRNA level also recapitulated in their study. Why this study is novel then?

4) It is very intuitive that deficit in Pol III transcription would severely affect protein synthesis in all brain areas as well as other organs. Hence, growth defect observed in Polr3a mutant mice is not very specific rather a general phenomenon.

5) Authors observed specific myelination defect in cortex and hippocampus but not in cerebellum. This is an interesting observation. It is important to find the link between tRNA removal and myelin depletion in hippocampus or cortex? Why is myelination not affected in cerebellum?

6) How was the locomotor activity measured? The detailed description is missing. Also, locomotion is primarily cerebellum dependent. There is no change in term of growth rate and myelination in cerebellar neurons. I do not understand why locomotor activity was measured.

7) The correlation with behavioural changes and RNA seq data is missing. There a number of transcripts are affected and mostly very general factors for cellular metabolism. Most of them are RNA Pol II transcribed. How a Pol III mutation influences RNA Pol II driven transcription? I did not find differential expression of any specific transcripts associated with behavioural changes. What is the motivation for transcriptomics analysis? None of these transcripts are very specific for myelination. It is rather a general cellular metabolism effect that indirectly influences myelination.

8) What genes identified by transcriptomics analysis regulates maturation of tRNA? Authors should at least perform RNAi study to identify possible factor and analyze their importance in maturation of tRNA.

9) What factors are influencing tRNA transport to cytoplasm? It may be possible that Polr3a mutation affect cytoplasmic transport of tRNA. Authors should study this aspect using an imaging experiment.

10) Does alteration of cytoplasmic level of tRNA affects translation? Author should perform translation assay using bio-orthoganal amino acid (AHA) labelling.

eLife assessment

This important chronobiological study in mice suggests that light modulated activity of Cdk5 activity on the PKA-CaMK-CREB signaling pathway provides missing molecular mechanistic details to understand light- induced circadian clock phase delays during the early night, but not for phase advances in the morning. The authors provide overall convincing evidence bridging from behavioral to molecular/cellular experiments to neural activity imaging.

Reviewer #1 (Public Review):

In the manuscript "Cyclin-dependent kinase 5 (Cdk5) activity is modulated by light and gates rapid phase shifts of the circadian clock", Brenna et al study the role of Cdk5 on circadian rhythms and they conclude that the CDK5 gates the activity of light on phase shifts at ZT by showing that the behavioural shifts to light as a result of CDK5 silencing only affect light-induced phase shifts at ZT/CT 14 but not at other times.

Further, they delineate the mechanism behind this phenotype and demonstrate that 1) CDK5 activity is downregulated following a light pulse via a loss of interaction with p35 and demonstrate this via an activity assay. 2) knock-down of CDK5: increases CREB, CAMK-ii/iv phosphorylation, likely via increasing calcium levels along with alterations to the localisation of Cav3.1, 3) reduces: light-induced response in vivo at ZT14 in the SCN.

They suggest this mechanism involves light 'silencing' CDK5-pathway (possibly by disrupting P35 interaction and dysregulating this pathway) which under basal conditions phosphorylates DARP32 leading to PKA inhibition and by extension reduction in activation of the calcium-calmodulin kinase activity and leading to reduced CREB activity. The authors finally evaluate gene expression changes of previously described light-responsive-genes in at ZT14 and the SCN.

This is an interesting piece of work that explains how circadian responses to light could be gated and is generally well supported by a wealth of data. Whilst I found the overall involvement of CDK5 in gating light response interesting and convincing, I have some concerns about their interpretation of the data surrounding the mechanism, which I have detailed below. I also think this manuscript could be improved with a slightly different structure and concise discussion for the benefit of a broader scientific audience.

Reviewer #2 (Public Review):

Summary:

Definition of the role of CdK5 in circadian locator activity and light induced neural activity in the mouse SCN in-vivo revealing its mode of action through PKA-CaMK-CREB signaling pathway.

Strengths:

The experimental approaches are carried from in-vivo, to cellular and molecular level and provide first evidence for the specific involvement of CdK5 in light-induced phase advance of the free-running rhythm.

Weaknesses:

The behavioral analyses are limited to some selected parameters.<br /> Downstream effects on circadian oscillation of gene expression and physiological functions in other brain regions, and organs is missing.

Author response:

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

Reviewer #2 (Public Review):

Weaknesses:

The comparison of affinity predictions derived from AlphaFold2 and H3-opt models, based on molecular dynamics simulations, should have been discussed in depth. In some cases, there are huge differences between the estimations from H3-opt models and those from experimental structures. It seems that the authors obtained average differences of the real delta, instead of average differences of the absolute value of the delta. This can be misleading, because high negative differences might be compensated by high positive differences when computing the mean value. Moreover, it would have been good for the authors to disclose the trajectories from the MD simulations.

Thanks for your careful checks. We fully understand your concerns about the large differences when calculating affinity. To understand the source of these huge differences, we carefully analyzed the trajectories of the input structures during MD simulations. We found that the antigen-antibody complex shifted as it transited from NVT to NPT during pre-equilibrium, even when restraints are used to determine the protein structure. To address this issue, we consulted the solution provided on Amber's mailing list (http://archive.ambermd.org/202102/0298.html) and modified the top file ATOMS_MOLECULE item of the simulation system to merge the antigen-antibody complexes into one molecule. As a result, the number of SOLVENT_POINTERS was also adjusted. Finally, we performed all MD simulations and calculated affinities of all complexes.

We have corrected the “Afterwards, a 25000-step NVT simulation with a time step of 1 fs was performed to gradually heat the system from 0 K to 100 K. A 250000-step NPT simulation with a time step of 2 fs was carried out to further heat the system from 100 K to 298 K.” into “Afterwards, a 400-ps NVT simulation with a time step of 2 fs was performed to gradually heat the system from 0 K to 298 K (0–100 K: 100 ps; 100-298 K: 200 ps; hold 298 K: 100 ps), and a 100-ps NPT simulation with a time step of 2 fs was performed to equilibrate the density of the system. During heating and density equilibration, we constrained the antigen-antibody structure with a restraint value of 10 kcal×mol-1×Å-2.” and added the following sentence in the Method section of our revised manuscript: “The first 50 ns restrains the non-hydrogen atoms of the antigen-antibody complex, and the last 50 ns restrains the non-hydrogen atoms of the antigen, with a constraint value of 10 kcal×mol-1×Å-2”

In addition, we have corrected the calculation of mean deltas using absolute values and have demonstrated that the average affinities of structures predicted by H3-OPT were closer to those of experimentally determined structures than values obtained through AF2. These results have been updated in the revised manuscript. However, significant differences still exist between the estimations of H3-OPT models and those derived from experimental structures in few cases. We found that antibodies moved away from antigens both in AF2 and H3-OPT predicted complexes during simulations, resulting in RMSDbackbone (RMSD of antibody backbone) exceeding 20 Å. These deviations led to significant structural changes in the complexes and consequently resulted in notable differences in affinity calculations. Thus, we removed three samples (PDBID: 4qhu, 6flc, 6plk) from benchmark because these predicted structures moved away from the antigen structure during MD simulations, resulting in huge energy differences from the native structures.

Author response table 1.

We also appreciate your reminder, and we have calculated all RMSDbackbone during production runs (SI Fig. 5).

Author response image 1.

Reviewer #3 (Public Review):

Weaknesses:

The proposed method lacks of a confidence score or a warning to help guiding the users in moderate to challenging cases.

We were sorry for our mistakes. We have updated our GitHub code and added following sentences to clarify how we train this confidence score module in Method Section: “Confidence score prediction module

We apply an MSE loss for confidence prediction, label error was calculated as the Cα deviation of each residue after alignment. The inputs of this module are the same as those used for H3-OPT, and it generates a confidence score ranging from 0 to 100. The dropout rates of H3-OPT were set to 0.25. The learning rate and weight decay of Adam optimizer are set to 1 × 10−5 and 1 × 10−4, respectively.”

Reviewer #2 (Recommendations For The Authors):

I would strongly suggest that the authors deepen their discussion on the affinity prediction based on Molecular Dynamics. In particular, why do the authors think that some structures exhibit huge differences between the predictions from the experimental structure and the predicted by H3-opt? Also, please compute the mean deltas using the absolute value and not the real value; the letter can be extremely misleading and hidden very high differences in different directions that are compensating when averaging.

I would also advice to include graphical results of the MD trajectories, at least as Supp. Material.

We gratefully thank you for your feedback and fully understand your concerns. We found the source of these huge differences and solved this problem by changing method of MD simulations. Then, we calculated all affinities and corrected the mean deltas calculation using the absolute value. The RMSDbackbone values were also measured to enable accurate affinity predictions during production runs (SI Fig. 5). There are still big differences between the estimations of H3-OPT models and those from experimental structures in some cases. We found that antibodies moved away from antigens both in AF2 and H3-OPT predicted complexes during simulations, resulting in RMSDbackbone exceeding 20 Å. These deviations led to significant structural changes in the complexes and consequently resulted in notable differences in affinity calculations. Thus, we removed three samples (PDBID: 4qhu, 6flc, 6plk) from benchmark.

Thanks again for your professional advice.

Reviewer #3 (Recommendations For The Authors):

(1) I am pleased with the most of the answers provided by the authors to the first review. In my humble opinion, the new manuscript has greatly improved. However, I think some answers to the reviewers are worth to be included in the main text or supporting information for the benefit of general readers. In particular, the requested statistics (i.e. p-values for Cα-RMSD values across the modeling approaches, p-values and error bars in Fig 5a and 5b, etc.) should be introduced in the manuscript.

We sincerely appreciate your advice. We have added the statistics values to Fig. 4 and Fig. 5 to our manuscript.

Author response image 2.

Author response image 3.

(2) Similarly, authors state in the answers that "we have trained a separate module to predict the confidence score of the optimized CDR-H3 loops". That sounds a great improvement to H3-OPT! However, I couldn't find any reference of that new module in the reviewed version of the manuscript, nor in the available GitHub code. That is the reason for me to hold the weakness "The proposed method lacks of a confidence score".

We were really sorry for our careless mistakes. Thank you for your reminding. We have updated our GitHub code and added following sentences to clarify how we train this confidence score module in Method Section:

“Confidence score prediction module

We apply an MSE loss for confidence prediction, label error was calculated as the Cα deviation of each residue after alignment. The inputs of this module are the same as those used for H3-OPT, and it generates a confidence score ranging from 0 to 100. The dropout rates of H3-OPT were set to 0.25. The learning rate and weight decay of Adam optimizer are set to 1 × 10−5 and 1 × 10−4, respectively.”

(3) I acknowledge all the efforts made for solving new mutant/designed nanobody structures. Judging from the solved structures, mutants Y95F and Q118N seems critical to either crystallographic or dimerization contacts stabilizing the CDR-H3 loop, hence preventing the formation of crystals. Clearly, solving a molecular structure is a challenge, hence including the following comment in the manuscript is relevant for readers to correctly asset the magnitude of the validation: "The sequence identities of the VH domain and H3 loop are 0.816 and 0.647, respectively, comparing with the best template. The CDR-H3 lengths of these nanobodies are both 17. According to our classification strategy, these nanobodies belong to Sub1. The confidence scores of these AlphaFold2 predicted loops were all higher than 0.8, and these loops were accepted as the outputs of H3-OPT by CBM."

We appreciate your kind recommendations and have revised “Although Mut1 (E45A) and Mut2 (Q14N) shared the same CDR-H3 sequences as WT, only minor variations were observed in the CDR-H3. H3-OPT generated accurate predictions with Cα-RMSDs of 1.510 Å, 1.541 Å and 1.411 Å for the WT, Mut1, and Mut2, respectively.” into “Although Mut1 (E45A) and Mut2 (Q14N) shared the same CDR-H3 sequences as WT (LengthCDR-H3 = 17), only minor variations were observed in the CDR-H3. H3-OPT generated accurate predictions with Cα-RMSDs of 1.510 Å, 1.541 Å and 1.411 Å for the WT, Mut1, and Mut2, respectively (The confidence scores of these AlphaFold2 predicted loops were all higher than 0.8, and these loops were accepted as the outputs of H3-OPT by CBM). ”. In addition, we have added following sentence in the legend of Figure 4 to ensure that readers can appropriately evaluate the significance and reliability of our validations: “The sequence identities of the VH domain and H3 loop are 0.816 and 0.647, respectively, comparing with the best template.”.

(4) As pointed out in the first review, I think the work https://doi.org/10.1021/acs.jctc.1c00341 is worth acknowledging in section "2.2 Molecular dynamics (MD) simulations could not provide accurate CDR-H3 loop conformations" of supplementary material, as it constitutes a clear reference (and probably one of the few) to the MD simulations that authors pretend to perform. Similarly, the work https://doi.org/10.3390/molecules28103991 introduces a former benchmark on AI algorithms for predicting antibody and nanobody structures that readers may find interest to contrast with the present work. Indeed, this later reference is used by authors to answer a reviewer comment.

Thanks a lot for your valuable comments. We have added these references in the proper positions in our manuscript.

eLife assessment

This paper presents H3-OPT, a deep learning method that effectively combines existing techniques for the prediction of antibody structure. This work, supported by convincing experiments for validation, is important because the method can aid in the design of antibodies, which are key tools in many research and industrial applications.

Reviewer #2 (Public Review):

This work provides a new tool (H3-Opt) for the prediction of antibody and nanobody structures, based on the combination of AlphaFold2 and a pre-trained protein language model, with a focus on predicting the challenging CDR-H3 loops with enhanced accuracy than previously developed approaches. This task is of high value for the development of new therapeutic antibodies. The paper provides an external validation consisting of 131 sequences, with further analysis of the results by segregating the test sets in three subsets of varying difficulty and comparison with other available methods. Furthermore, the approach was validated by comparing three experimentally solved 3D structures of anti-VEGF nanobodies with the H3-Opt predictions

Strengths:

The experimental design to train and validate the new approach has been clearly described, including the dataset compilation and its representative sampling into training, validation and test sets, and structure preparation. The results of the in silico validation are quite convincing and support the authors' conclusions.

The datasets used to train and validate the tool and the code are made available by the authors, which ensures transparency and reproducibility, and allows future benchmarking exercises with incoming new tools.

Compared to AlphaFold2, the authors' optimization seems to produce better results for the most challenging subsets of the test set.

Weaknesses:

None

Reviewer #3 (Public Review):

Summary:

The manuscript introduces a new computational framework for choosing 'the best method' according to the case for getting the best possible structural prediction for the CDR-H3 loop. The authors show their strategy improves on average the accuracy of the predictions on datasets of increasing difficulty in comparison to several state-of-the-art methods. They also show the benefits of improving the structural predictions of the CDR-H3 in the evaluation of different properties that may be relevant for drug discovery and therapeutic design.

Strengths:

The authors introduce a novel framework, which can be easily adapted and improved. Authors use a well-defined dataset to test their new method. A modest average accuracy gain is obtained in comparison to other state-of-the art methods for the same task, while avoiding testing different prediction approaches. Although the accuracy gain is mainly ascribed to easy cases, the accuracy and precision for moderate to challenging cases is comparable to the best PLM methods (see Fig. 4b and Extended Data Fig. 2), reflecting the present methodological limit in the field. The proposed method includes a confidence score for guiding users about the accuracy of the predictions.

eLife assessment

This important study, using three bioactive compounds as a model, demonstrates that estimating the intake of food components based on food composition databases and self-reported dietary data is highly unreliable. The authors present convincing data showing the differences in the estimated quantile of intake of three bioactive compounds between biomarker and 24-hour dietary recall with food-composition database. The work will be of broad interest to the clinical nutrition research community.

Joint Public Review:

Identifying dietary biomarkers, in particular, has become a main focus of nutrition research in the drive to develop personalized nutrition.

The aim of this study was to determine the accuracy of using food composition databases to assess the association between dietary intake and health outcomes. The authors found that using food composition data to assess dietary intake of specific bioactives and the impact consumption has on systolic blood pressure provided vastly different outcomes depending on the method used. These findings demonstrate the difficulty in elucidating the relationship between diet and health outcomes and the need for more stringent research in the development of dietary biomarkers.

The primary strength of the study is the use of a large cohort in which dietary data and the measurement of three specific bioactives and blood pressure were collected on the same day. The bioactives selected have been extensively researched for their health effects. Another strength is that the authors controlled for as many variables as possible when running the simulations to get a more accurate account of how the variability in food composition can impact research findings that associate the intake of certain food components with health outcomes.

Author response:

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

We would like to thank the editors and reviewers for their encouraging comments. Reviewer 1 raises an important question regarding the translation of biomarker derived data into dietary recommendations, taking the high variability in food composition into consideration. Unfortunately, there is no straightforward answer as the high variability in food composition means that the number of cups of tea for 200mg of flavan-3-ols will depend on the flavanol content of the tea. A probabilistic modelling approach, as we have used to investigate the impact of food content variability on estimated associations with health outcomes, would be a possible solution. This could provide food based recommendations that would meet a defined intake with a certain probability. However, developing and exploring such models is beyond the scope of this manuscript and we have therefore decided not to include this in our response. We have stated in the manuscript that such a method needs to be developed.

We have addressed the typographical errors and the other comments as follows:

•   Line 126 - this is the first mention of DR-FCT and as such it needs to be defined. This was a typo and it was corrected throughout the manuscript. The actual abbreviation is DD-FCT and it is defined in line 78.

•   Figure 4 - what exactly is this figure trying to convey to the reader? A better explanation about this figure is needed. Figure legend was updated and extent hoping to increase clarity.

•   Figure 5 - Why are the graphs presented differently, meaning why are the data for the flavan-3-ols and epicatechin differentiated for men and women and not nitrate. The sample size for nitrate was too small to stratify in the same way as for flavan-3-ols.

•   Line 365 - more information is needed, I am assuming the authors are stating ”The tableone package for R ...”. As requested by the reviewer, additional details are now included.

We have also revised the abstract, the conclusion and the discussion of limitations of the biomarker approach to improve readabilty of the manuscript.

eLife assessment

This useful article provides evidence of the potential neuropathogenicity of Bacillus cereus serovar anthracis in wild chimpanzees. The authors provide an extensive characterization of four chimpanzees that died acutely from anthrax. The study provides incomplete traditional histopathologic evidence of neuroinvasion since the meninges could not be evaluated, which weakens the authors' conclusions. The work will be of interest to infectious disease researchers.

Reviewer #1 (Public Review):

Summary:

Gräßle et al. provide a series of four post-mortem cases of chimpanzees with PCR-proven Bacillus cereus biovar anthracis (Bcbva), who reportedly died of this infection. One control case is also provided. Compelling post-mortem Magnetic resonance imaging scans of the highest technical standards are presented. Last, the authors provide some histopathology of the brains aiming at showing the neuroinfective potential of Bcbva.

Strengths:

The merits of this study are highly acknowledged. This reviewer deems it very important to implement the latest methodology in such veterinary observational studies, in order to investigate what is going on in wildlife regarding zoonoses. The scans of five whole post-mortem chimpanzee brains with exquisite MRI technology (extremely good scan quality) represent such an implementation.

Weaknesses:

The conclusions from the necropsies are, unfortunately, on weak grounds:

(1) The authors claim that all 4 infected individuals have suffered from meningitis. However, I do not see evidence for that, neither in the gross macroscopical images provided in Figure 1. The authors claim congestion of superficial veins, at least in cases 1-3, and interpret this as pointing towards meningitis. I do not see major superficial vein congestion in any of the cases. Furthermore, vessel congestion here would rather indicate brain swelling and subsequent inhibition of venous blood outflow from the skull, which would relate to brain edema. Bacterial meningitis would itself display as clouding of the meninges, while the meninges presented in all 4 cases are perfectly translucent and gracile.

(2) The authors show a bacterial overgrowth, of brains, which was most severe in cases 1 and 2, less so in case 3, and least in case 4 (Table 1). This correlates very well with post-mortem intervals (Supplementary Table 1). The amount of bacteria is remarkable, while there is practically no brain inflammation, only moderate microglia activation. Also, the authors do not convincingly prove the proposed meningitis at the histological level, since Figure 6 does not show it in a convincing manner. Also, moderate superficial gliosis shown in Figure 6 g+h is for me not evidence of meningitis. I would expect masses of granulocytes and lymphocytes, given the amount of bacteria shown.

(3) The pattern of bacterial invasion, i.e. first confined to vessels as in case 4 with short post-mortem interval, and then overgrowing the brain with practically no glial or inflammatory reaction, is very typical of post-mortem putrefication. It is conceivable that the chimpanzees had severe bacteremia, which, after death, quickly led to bacterial invasion into the brain parenchyma. While authors state the post-mortem intervals in hours, they do not state whether bodies were immediately cooled after death.

(4) I find it difficult to see evidence of superficial siderosis in any of the images. In particular, case 2 in Figure 1 does not convincingly display leptomeningeal hemorrhage. Dark granules, e.g. shown in Figure 4 e, are very typical of so-called formalin pigment. If that would be hemosiderin or some other form of iron, it would be expected that it displays much stronger in the DAB-enhanced perls stain (Figure 4 c).

Reviewer #2 (Public Review):

In "Neuroinfectiology of an atypical anthrax-causing pathogen in wild chimpanzees" Tobias et.al. provide a detailed histologic characterization of B.cereus biovar anthracis in the brain of four wild chimpanzees in comparison to an uninfected age-matched chimp. The authors present a combination of special stains, radiography (MRI), bacterial culture, and immunohistochemistry including some quantitative image analysis to support the assessment of the neuropathogenicity of Bcbva. However, the study has major limitations that detract from the conclusions presented regarding the neurovirulence of this strain. Namely, there is a near complete lack of traditional histopathological and radiographic interpretation by qualified experts in which to frame the detailed tissue studies. The authors mention that facultative anaerobes are capable of post-mortem replication. Pathologists use comprehensive pathological assessments to determine the extent of disease caused by the primary infection, none of which is mentioned in this study (spleen, heart, lungs), which makes it difficult to determine if the findings in the brain align with the rest of the post-mortem assessment. If these were not included due to severe post-mortem autolysis, it heightens the risk of post-mortem bacterial replication in the CNS. The most important limitation is the fact that the meninges were removed and were not available for assessment therefore any comparisons with existing data on neuropathogenicity of B. anthracis is not possible. An advantage of the study is the inclusion of the control age-matched chimp, but the controls are not shown for many of the IHC and special stains - limiting interpretations. In general, the article is difficult to follow with the figures since many panels are only discussed and interpreted in the figure legends and not the text. In some cases, the results are overly technical with limited clinical insight which makes the article less easy to interpret next to human clinical reports.

Author response:

We are thankful to the expert reviewers and the editorial team for their assessment of our manuscript and valuable comments, which will help us to improve our manuscript. While Reviewer #1 appreciated the comprehensive assessment using advanced methods, Reviewer #2 asked for an extension of traditional neuropathological and neuroradiological assessments. Both reviewers identified limitations of the study like the inability to provide direct histopathological evidence for meningitis due to missing meninges tissue, resulting in the conclusions being based on indirect evidence. The reviewers raised concerns about potential post mortem penetration of bacteria into the brain parenchyma. Reviewer #1 also questioned the evidence for cortical siderosis based on the intensity of histological stains.

We agree with both reviewers and the editorial comment that a traditional neuropathological assessment of meningeal status would have strongly boosted the study's conclusions. Please note that the opportunistic sampling approach after a wild animal’s “natural” death, which is the only ethical method to study infection biology in great apes, is intrinsically accompanied by some limitations such as the lack of standardized post mortem intervals or incomplete sampling. In the revised version of the manuscript, we will complement the advanced MRI and histology already presented by extended traditional neuroradiological and neuropathological assessments as recommended by Reviewer #2, including a report on the status of other organs. However, it is important to note that the interpretation of post mortem MRI of brain material collected in the field differs substantially from conventional in vivo MRI and requires tailored analysis and interpretation. Below we comment on three aspects addressed by reviewers:

* Missing meninges *: The meninges and associated vessels had to be removed to reduce blood-related artifacts in previously performed MRI measurements. We are aware that this poses a major limitation of this study, and thus rely on the evidence derived from the material at hand. Neuropathological assessment is in agreement with the reviewer's comments that no overt acute bacterial meningitis with e.g. turbid appearance, purulent exudates or frank hemorrhages is apparent in the macroscopic inspection of the presented material. However, the macroscopic changes should be evaluated in the light of the brief time interval between bacterial colonization and death. Meningeal bacterial invasion was visualized on a few meningeal residues we found in case 1, proofing the invasion of the subarachnoid space. Based on the reviewer's suggestions, the microscopic neuropathological evaluation will be expanded with the aim to identify further regions with meningeal residues to include more regions to 1) reduce potential sampling bias and 2) to better characterize the leptomeningeal infiltrates focusing on early inflammatory markers.<br />  However, an extensive assessment of the histopathological inflammatory status must be clarified in future studies on specimens with remaining meninges.

*Putrefaction/Post mortem bacterial proliferation*:<br /> Reviewers raised important points by remarking  that the tissue alterations could be due to putrefaction/post mortem effects. Classical bacterial putrefaction is unlikely, since no mixed flora of opportunistic bacteria was detected, suggesting that time before fixation was sufficient to prevent secondary bacterial invasion in the presented specimens. Moreover, it has been shown that for the post mortem interval of <24 hours bacterial invasion of the brain is rare even at higher temperatures (Ith et al 2011, https://doi.org/10.1002/nbm.1623). The possibility of post mortem tissue propagation of Bcbva must be considered, since there is a lack of experimental data on the pathogen’s growth after host death, which has been discussed by us in the "Limitations" section in the original manuscript. Although it seems plausible that post mortem multiplication in the brain does occur to a certain extent, several observations suggest that this is not the only mechanism at play in the presented cases. We observed early  microglial activation and astrogliosis indicating a beginning inflammatory reaction in the brain parenchyma. Taken together, the data presented suggest a short time interval between bacterial colonization and death. Under this premise, further analyses for the revision of the manuscript will more closely investigate pathological in vivo tissue alterations.

*Siderosis* Signs of cortical siderosis were evident in the MRI images of all adult cases (1, 3, and 4), appearing as a hyperintense rim in quantitative R2* maps, indicating substantially elevated levels of iron on the brain surface. These findings were confirmed by Perls’s stain for iron. Such rims in R2* are a typical sign of cortical iron deposition due to siderosis, as observed in conditions like angiopathies. Meningeal bleedings are the most probable source of the elevated iron levels in the cortex. Importantly, such signs were never observed in the post mortem brains of chimpanzees not infected with Anthrax (about 30 cases analyzed so far). Reviewer #1 noted that the intensity of the Perls’s stain seemed too low for siderosis. However, this intensity can vary depending on staining procedure and may be lower for the acute and short disease course of Bcbva-induced Anthrax compared to the chronic human cases Reviewer #1 may be referring to. Taken together, we believe that the evidence of cortical siderosis is compelling, speaking in favor of pre mortem meningeal hemorrhage.

In summary, in the revised version of the manuscript, we plan to: (1) add a traditional neuroradiological assessment of all scans; (2) present an extended traditional neuropathological assessment of all cases; (3) report results on the status of early inflammatory markers; and (4) discuss the limitations of the study in more detail.

eLife assessment

This valuable biomechanical analysis of kangaroo kinematics and kinetics across a range of hopping speeds and masses is a step towards understanding a long-standing problem in locomotion biomechanics: the mechanism for how, unlike other mammals, kangaroos are able to increase hopping speed without a concomitant increase in metabolic cost. Based on their suggestion that kangaroo posture changes with speed increase tendon stress/strain and hence elastic energy storage/return, the authors imply (but do not show quantitatively or qualitatively) that the greater tendon elastic energy storage/return counteracts the increased cost of generating muscular force at faster speeds and allows for the invariance in metabolic cost. The methods are impressive, but there is currently only limited evidence for increased tendon stress/strain at faster speeds, and the support for any conclusion metabolic energy expenditure is inadequate.

Reviewer #1 (Public Review):

Summary:

The study explored the biomechanics of kangaroo hopping across both speed and animal size to try and explain the unique and remarkable energetics of kangaroo locomotion.

Strengths:

The study brings kangaroo locomotion biomechanics into the 21st century. It is a remarkably difficult project to accomplish. There is excellent attention to detail, supported by clear writing and figures.

Weaknesses:

The authors oversell their findings, but the mystery still persists. The manuscript lacks a big-picture summary with pointers to how one might resolve the big question.

General Comments

This is a very impressive tour de force by an all-star collaborative team of researchers. The study represents a tremendous leap forward (pun intended) in terms of our understanding of kangaroo locomotion. Some might wonder why such an unusual species is of much interest. But, in my opinion, the classic study by Dawson and Taylor in 1973 of kangaroos launched the modern era of running biomechanics/energetics and applies to varying degrees to all animals that use bouncing gaits (running, trotting, galloping and of course hopping). The puzzling metabolic energetics findings of Dawson & Taylor (little if any increase in metabolic power despite increasing forward speed) remain a giant unsolved problem in comparative locomotor biomechanics and energetics. It is our "dark matter problem".

This study is certainly a hop towards solving the problem. But, the title of the paper overpromises and the authors present little attempt to provide an overview of the remaining big issues. The study clearly shows that the ankle and to a lesser extent the mtp joint are where the action is. They clearly show in great detail by how much and by what means the ankle joint tendons experience increased stress at faster forward speeds. Since these were zoo animals, direct measures were not feasible, but the conclusion that the tendons are storing and returning more elastic energy per hop at faster speeds is solid. The conclusion that net muscle work per hop changes little from slow to fast forward speeds is also solid. Doing less muscle work can only be good if one is trying to minimize metabolic energy consumption. However, to achieve greater tendon stresses, there must be greater muscle forces. Unless one is willing to reject the premise of the cost of generating force hypothesis, that is an important issue to confront. Further, the present data support the Kram & Dawson finding of decreased contact times at faster forward speeds. Kram & Taylor and subsequent applications of (and challenges to) their approach supports the idea that shorter contact times (tc) require recruiting more expensive muscle fibers and hence greater metabolic costs. Therefore, I think that it is incumbent on the present authors to clarify that this study has still not tied up the metabolic energetics across speed problems and placed a bow atop the package. Fortunately, I am confident that the impressive collective brain power that comprises this author list can craft a paragraph or two that summarizes these ideas and points out how the group is now uniquely and enviably poised to explore the problem more using a dynamic SIMM model that incorporates muscle energetics (perhaps ala' Umberger et al.). Or perhaps they have other ideas about how they can really solve the problem.

I have a few issues with the other half of this study (i.e. animal size effects). I would enjoy reading a new paragraph by these authors in the Discussion that considers the evolutionary origins and implications of such small safety factors. Surely, it would need to be speculative, but that's OK.

Reviewer #2 (Public Review):

Summary

This is a fascinating topic that has intrigued scientists for decades. I applaud the authors for trying to tackle this enigma. In this manuscript, the authors primarily measured hopping biomechanics data from kangaroos and performed inverse dynamics. While these biomechanical analyses were thorough and impressively incorporated collected anatomical data and an Opensim model, I'm afraid that they did not satisfactorily address how kangaroos can hop faster and not consume more metabolic energy, unique from other animals. Noticeably, the authors did not collect metabolic data nor did they model metabolic rates using their modelling framework. Instead, they performed a somewhat traditional inverse dynamics analysis from multiple animals hopping at a self-selected speed. Within these analyses, the authors largely focused on ankle EMA, discussing its potential importance (because it affects tendon stress, which affects tendon strain energy, which affects muscle mechanics) on the metabolic cost of hopping. However, EMA was roughly estimated (CoP was fixed to the foot, not measured) and did not detectibly associate with hopping speed (see results). Yet, the authors interpret their EMA findings as though it systematically related with speed to explain their theory on how metabolic cost is unique in kangaroos vs. other animals. These speed vs. biomechanics relationships were limited by comparisons across different animals hopping at different speeds and could have been strengthened using repeated measures design. There are also multiple inconsistencies between the authors' theory on how mechanics affect energetics and the cited literature, which leaves me somewhat confused and wanting more clarification and information on how mechanics and energetics relate. My apologies for the less-than-favorable review, I think that this is a neat biomechanics study - but am unsure if it adds much to the literature on the topic of kangaroo hopping energetics in its current form.

Reviewer #3 (Public Review):

Summary:

The goal of this study is to understand how, unlike other mammals, kangaroos are able to increase hopping speed without a concomitant increase in metabolic cost. They use a biomechancial analysis of kangaroo hopping data across a range of speeds to investigate how posture, effective mechanical advantage, and tendon stress vary with speed and mass. The main finding is that a change in posture leads to increasing effective mechanical advantage with speed, which ultimately increases tendon elastic energy storage and returns via greater tendon strain. Thus kangaroos may be able to conserve energy with increasing speed by flexing more, which increases tendon strain.

Strengths:

The approach and effort invested into collecting this valuable dataset of kangaroo locomotion is impressive. The dataset alone is a valuable contribution.

Weaknesses:

Despite these strengths, I have concerns regarding the strength of the results and the overall clarity of the paper and methods used (which likely influences how convincingly the main results come across).

(1) The paper seems to hinge on the finding that EMA decreases with increasing speed and that this contributes significantly to greater tendon strain estimated with increasing speed. It is very difficult to be convinced by this result for a number of reasons:<br /> • It appears that kangaroos hopped at their preferred speed. Thus the variability observed is across individuals not within. Is this large enough of a range (either within or across subjects) to make conclusions about the effect of speed, without results being susceptible to differences between subjects? In the literature cited, what was the range of speeds measured, and was it within or between subjects?<br /> • Assuming that there is a compelling relationship between EMA and velocity, how reasonable is it to extrapolate to the conclusion that this increases tendon strain and ultimately saves metabolic cost? They correlate EMA with tendon strain, but this would still not suggest a causal relationship (incidentally the p-value for the correlation is not reported). Tendon strain could be increasing with ground reaction force, independent of EMA. Even if there is a correlation between strain and EMA, is it not a mathematical necessity in their model that all else being equal, tendon stress will increase as ema decreases? I may be missing something, but nonetheless, it would be helpful for the authors to clarify the strength of the evidence supporting their conclusions.<br /> • The statistical approach is not well-described. It is not clear what the form of the statistical model used was and whether the analysis treated each trial individually or grouped trials by the kangaroo. There is also no mention of how many trials per kangaroo, or the range of speeds (or masses) tested. Related to this, there is no mention of how different speeds were obtained. It seems that kangaroos hopped at a self-selected pace, thus it appears that not much variation was observed. I appreciate the difficulty of conducting these experiments in a controlled manner, but this doesn't exempt the authors from providing the details of their approach.<br /> • Some figures (Figure 2 for example) present means for one of three speeds, yet the speeds are not reported (except in the legend) nor how these bins were determined, nor how many trials or kangaroos fit in each bin. A similar comment applies to the mass categories. It would be more convincing if the authors plotted the main metrics vs. speed to illustrate the significant trends they are reporting.

(2) The significance of the effects of mass is not clear. The introduction and abstract suggest that the paper is focused on the effect of speed, yet the effects of mass are reported throughout as well, without a clear understanding of the significance. This weakness is further exaggerated by the fact that the details of the subject masses are not reported.

(3) The paper needs to be significantly re-written to better incorporate the methods into the results section. Since the results come before the methods, some of the methods must necessarily be described such that the study can be understood at some level without turning to the dedicated methods section. As written, it is very difficult to understand the basis of the approach, analysis, and metrics without turning to the methods.

Author response:

Public Reviews:

We thank the reviewers for their overall positive assessments and constructive feedback

Reviewer #1 (Public Review):

Summary:

The study explored the biomechanics of kangaroo hopping across both speed and animal size to try and explain the unique and remarkable energetics of kangaroo locomotion.

Strengths:

The study brings kangaroo locomotion biomechanics into the 21st century. It is a remarkably difficult project to accomplish. There is excellent attention to detail, supported by clear writing and figures.

Weaknesses:

The authors oversell their findings, but the mystery still persists.

The manuscript lacks a big-picture summary with pointers to how one might resolve the big question.

General Comments

This is a very impressive tour de force by an all-star collaborative team of researchers. The study represents a tremendous leap forward (pun intended) in terms of our understanding of kangaroo locomotion. Some might wonder why such an unusual species is of much interest. But, in my opinion, the classic study by Dawson and Taylor in 1973 of kangaroos launched the modern era of running biomechanics/energetics and applies to varying degrees to all animals that use bouncing gaits (running, trotting, galloping and of course hopping). The puzzling metabolic energetics findings of Dawson & Taylor (little if any increase in metabolic power despite increasing forward speed) remain a giant unsolved problem in comparative locomotor biomechanics and energetics. It is our "dark matter problem".

Thank you for the kind words

This study is certainly a hop towards solving the problem. But, the title of the paper overpromises and the authors present little attempt to provide an overview of the remaining big issues.

We will modify the title to reflect this comment.  

The study clearly shows that the ankle and to a lesser extent the mtp joint are where the action is. They clearly show in great detail by how much and by what means the ankle joint tendons experience increased stress at faster forward speeds.

Since these were zoo animals, direct measures were not feasible, but the conclusion that the tendons are storing and returning more elastic energy per hop at faster speeds is solid.

The conclusion that net muscle work per hop changes little from slow to fast forward speeds is also solid.

Doing less muscle work can only be good if one is trying to minimize metabolic energy consumption. However, to achieve greater tendon stresses, there must be greater muscle forces. Unless one is willing to reject the premise of the cost of generating force hypothesis, that is an important issue to confront.

Further, the present data support the Kram & Dawson finding of decreased contact times at faster forward speeds. Kram & Taylor and subsequent applications of (and challenges to) their approach supports the idea that shorter contact times (tc) require recruiting more expensive muscle fibers and hence greater metabolic costs. Therefore, I think that it is incumbent on the present authors to clarify that this study has still not tied up the metabolic energetics across speed problems and placed a bow atop the package.

Fortunately, I am confident that the impressive collective brain power that comprises this author list can craft a paragraph or two that summarizes these ideas and points out how the group is now uniquely and enviably poised to explore the problem more using a dynamic SIMM model that incorporates muscle energetics (perhaps ala' Umberger et al.). Or perhaps they have other ideas about how they can really solve the problem.

You have raised important points, thank you for this feedback. We will add a paragraph discussing the limitations of our study and ensure the revised manuscript makes it clear which mysteries remain. We intend to address muscle forces, contact time, and energetics in future work when we have implemented all hindlimb muscles within the musculoskeletal model.  

I have a few issues with the other half of this study (i.e. animal size effects). I would enjoy reading a new paragraph by these authors in the Discussion that considers the evolutionary origins and implications of such small safety factors. Surely, it would need to be speculative, but that's OK.

We will integrate this into the discussion.

Reviewer #2 (Public Review):

Summary

This is a fascinating topic that has intrigued scientists for decades. I applaud the authors for trying to tackle this enigma. In this manuscript, the authors primarily measured hopping biomechanics data from kangaroos and performed inverse dynamics.

While these biomechanical analyses were thorough and impressively incorporated collected anatomical data and an Opensim model, I'm afraid that they did not satisfactorily address how kangaroos can hop faster and not consume more metabolic energy, unique from other animals.

Noticeably, the authors did not collect metabolic data nor did they model metabolic rates using their modelling framework. Instead, they performed a somewhat traditional inverse dynamics analysis from multiple animals hopping at a self-selected speed.

We aimed to provide a joint-level explanation, but we will address the limitations of not modelling the energy consumers themselves (the skeletal muscles) in the revised manuscript. We plan to expand upon muscle level energetics in the future with a more detailed MSK model.

Within these analyses, the authors largely focused on ankle EMA, discussing its potential importance (because it affects tendon stress, which affects tendon strain energy, which affects muscle mechanics) on the metabolic cost of hopping. However, EMA was roughly estimated (CoP was fixed to the foot, not measured)…

As noted in our methods, EMA was not calculated from a fixed centre of pressure (CoP). We did fix the medial-lateral position, owing to the fact that both feet contacted the force plate together, but the anteroposterior movement of the CoP was recorded by the force plate and thus allowed to move. We report the movement (or lack of movement) in our results. The anterior-posterior axis is the most relevant to lengthening or shortening the distance of the ‘out-lever’ R, and thereby EMA.

It is necessary to assume fixed medial-lateral position because a single force trace and CoP is recorded when two feet land on the force plate. The medial-lateral forces on each foot cancel out so there is no overall medial-lateral movement if the forces are symmetrical (e.g. if the kangaroo is hopping in a straight path and one foot is not in front of the other). We only used symmetrical trials so that the anterior-posterior movement of the CoP would be reliable.

and did not detectibly associate with hopping speed (see results).

Yet, the authors interpret their EMA findings as though it systematically related with speed to explain their theory on how metabolic cost is unique in kangaroos vs. other animals.

Indeed, the relationship between R and speed (and therefore EMA and speed) was not significant. However, the significant change in ankle height with speed, combined with no systematic change in COP at midstance, demonstrates that R would get longer at faster speeds. If we consider the nonsignificant relationship between R and speed to indicate that there is no change in R, then these two results conflict. We could not find a flaw in our methods, so instead concluded that the nonsignificant relationship between R and speed may be due to a small change in R being undetectable in our data. Taking both results into account, we think it is more likely that there is a non-detectable change in R, rather than no change in R with speed, but we presented both results for transparency.

These speed vs. biomechanics relationships were limited by comparisons across different animals hopping at different speeds and could have been strengthened using repeated measures design.

There is significant variation in speed within individuals, not just between individuals. The preferred speed of kangaroos is 2-4.5 m/s, but most individuals show a wide range within this. Eight of our 16 kangaroos had a maximum speed that was between 1-2m/s faster than their slowest trial. Repeated measures of these eight individuals comprises 78 out of the 100 trials.

It would be ideal to collect data across the full range of speeds for all individuals, but it is not feasible in this type of experimental setting. Interference such as chasing is dangerous to kangaroos as they are prone to strong adverse reactions to stress.

There are also multiple inconsistencies between the authors' theory on how mechanics affect energetics and the cited literature, which leaves me somewhat confused and wanting more clarification and information on how mechanics and energetics relate.

We will ensure that this is clearer in the revised manuscript.

My apologies for the less-than-favorable review, I think that this is a neat biomechanics study - but am unsure if it adds much to the literature on the topic of kangaroo hopping energetics in its current form.

Reviewer #3 (Public Review):

Summary:

The goal of this study is to understand how, unlike other mammals, kangaroos are able to increase hopping speed without a concomitant increase in metabolic cost. They use a biomechancial analysis of kangaroo hopping data across a range of speeds to investigate how posture, effective mechanical advantage, and tendon stress vary with speed and mass. The main finding is that a change in posture leads to increasing effective mechanical advantage with speed, which ultimately increases tendon elastic energy storage and returns via greater tendon strain. Thus kangaroos may be able to conserve energy with increasing speed by flexing more, which increases tendon strain.

Strengths:

The approach and effort invested into collecting this valuable dataset of kangaroo locomotion is impressive. The dataset alone is a valuable contribution.

Thank you!

Weaknesses:

Despite these strengths, I have concerns regarding the strength of the results and the overall clarity of the paper and methods used (which likely influences how convincingly the main results come across).

(1) The paper seems to hinge on the finding that EMA decreases with increasing speed and that this contributes significantly to greater tendon strain estimated with increasing speed. It is very difficult to be convinced by this result for a number of reasons:

• It appears that kangaroos hopped at their preferred speed. Thus the variability observed is across individuals not within. Is this large enough of a range (either within or across subjects) to make conclusions about the effect of speed, without results being susceptible to differences between subjects?

Apologies, this was not clear in the manuscript. Kangaroos hopping at their preferred speed means we did not chase or startle them into high speeds to comply with ethics and enclosure limitations. Thus we did not record a wide range of speed within the bounds of what kangaroos are capable of (up to 12 m/s), but for the range we did measure (~2-4.5 m/s), there is variation hopping speed within each individual kangaroo. Out of 16 individuals, eight individuals had a difference of 1-2m/s between their slowest and fastest trials, and these kangaroos accounted for 78 out of 100 trials. Of the remainder, six individuals had three for fewer trials each, and two individual had highly repeatable speeds (3 out of 4, and 6 out of 7 trials were within 0.5 m/s). We will ensure this is clear in the revised manuscript.

In the literature cited, what was the range of speeds measured, and was it within or between subjects?

For other literature, to our knowledge the highest speed measured is ~9.5m/s (see supplementary Fig1b) and there were multiple measures for several individuals (see methods Kram & Dawson 1998).

• Assuming that there is a compelling relationship between EMA and velocity, how reasonable is it to extrapolate to the conclusion that this increases tendon strain and ultimately saves metabolic cost?

They correlate EMA with tendon strain, but this would still not suggest a causal relationship (incidentally the p-value for the correlation is not reported).

We will add supporting literature on the relationship between metabolic cost and tendon stress (or strain), to elaborate on why the correlation between EMA and stress is important.

Tendon strain could be increasing with ground reaction force, independent of EMA.

Even if there is a correlation between strain and EMA, is it not a mathematical necessity in their model that all else being equal, tendon stress will increase as ema decreases? I may be missing something, but nonetheless, it would be helpful for the authors to clarify the strength of the evidence supporting their conclusions.

Yes, GRF also contributes to the increase in tendon stress in the mechanism we propose. We have illustrated this in Fig 6, however we will make this clearer in the revised discussion.

• The statistical approach is not well-described. It is not clear what the form of the statistical model used was and whether the analysis treated each trial individually or grouped trials by the kangaroo. There is also no mention of how many trials per kangaroo, or the range of speeds (or masses) tested.

The methods include the statistical model with the variables that we used, as well as the kangaroo masses (13.7 to 26.6 kg, mean: 20.9 ± 3.4 kg). We will move the range of speeds from the supplementary material to the results or figure captions. We will add information on the number of trials per kangaroo to the methods.

We did not group the data e.g. by using an average speed per individual for all their trials, or by comparing fast to slow groups (this was for display purposes in our figures, which we will make clearer in the methods).

Related to this, there is no mention of how different speeds were obtained. It seems that kangaroos hopped at a self-selected pace, thus it appears that not much variation was observed. I appreciate the difficulty of conducting these experiments in a controlled manner, but this doesn't exempt the authors from providing the details of their approach.

• Some figures (Figure 2 for example) present means for one of three speeds, yet the speeds are not reported (except in the legend) nor how these bins were determined, nor how many trials or kangaroos fit in each bin. A similar comment applies to the mass categories. It would be more convincing if the authors plotted the main metrics vs. speed to illustrate the significant trends they are reporting.

Thank you for this comment. The bins are used only for display purposes and not within the analysis. In the revised manuscript, we will ensure this is clear.

(2) The significance of the effects of mass is not clear. The introduction and abstract suggest that the paper is focused on the effect of speed, yet the effects of mass are reported throughout as well, without a clear understanding of the significance. This weakness is further exaggerated by the fact that the details of the subject masses are not reported.

Indeed, the primary aim of our study was to explore the influence of speed, given the uncoupling of energy from hopping speed in kangaroos. We included mass to ensure that the effects of speed were not driven by body mass (i.e.: that larger kangaroos hopped faster).  

(3) The paper needs to be significantly re-written to better incorporate the methods into the results section. Since the results come before the methods, some of the methods must necessarily be described such that the study can be understood at some level without turning to the dedicated methods section. As written, it is very difficult to understand the basis of the approach, analysis, and metrics without turning to the methods.

We agree, and in the revised manuscript will incorporate some of the methodological details within the results.

Author response image 1.

Reviewer #1 (Public Review):

Summary:

Major findings or outcomes include a genome for the wasp, characterization of the venom constituents and teratocyte and ovipositor expression profiles, as well as information about Trichopria ecology and parasitism strategies. It was found that Trichopria cannot discriminate among hosts by age, but can identify previously parasitized hosts. The authors also investigated whether superparasitism by Trichopria wasps improved parasitism outcomes (it did), presumably by increasing venom and teratocyte concentrations/densities. Elegant use of Drosophila ectopic expression tools allowed for functional characterization of venom components (Timps), and showed that these proteins are responsible for parasitoid-induced delays in host development. After finding that teratocytes produce a large number of proteases, experiments showed that these contribute to digestion of host tissues for parasite consumption.<br /> The discussion ties these elements together by suggesting that genes used for aiding in parasitism via different parts of the parasitism arsenal arise from gene duplication and shifts in tissue of expression (to venom glands or teratocytes).

Strengths:

The strength of this manuscript is that it describes the parasitism strategies used by Trichopria wasps at a molecular and behavioral level with broad strokes. It represents a large amount of work that in previous decades might have been published in several different papers. Including all of these data in a manuscript together makes for a comprehensive and interesting study.

Weaknesses:

The weakness is that the breadth of the study results in fairly shallow mechanistic or functional results for any given facet of Trichopria's biology. Although none of the findings are especially novel given results from other parasitoid species in previous publications, integrating results together provides significant information about Trichopria biology.

Reviewer #2 (Public Review):

Summary:

Key findings of this research include the sequencing of the wasp's genome, identification of venom constituents and teratocytes, and examination of Trichopria drosophilae (Td)'s ecology and parasitic strategies. It was observed that Td doesn't distinguish between hosts based on age but can recognize previously parasitized hosts. The study also explored whether multiple parasitisms by Td improved outcomes, which indeed it did, possibly by increasing venom and teratocyte levels. Utilizing Drosophila ectopic expression tools, the authors functionally characterized venom components, specifically tissue inhibitors of metalloproteinases (Timps), which were found to cause delays in host development. Additionally, experiments revealed that teratocytes produce numerous proteases, aiding in the digestion of host tissues for parasite consumption. The discussion suggests that genes involved in different aspects of parasitism may arise from gene duplication and shifts in tissue expression to venom glands or teratocytes.

Strengths:

This manuscript provides an in-depth and detailed depiction of the parasitic strategies employed by Td wasps, spanning both molecular and behavioral aspects. It consolidates a significant amount of research that, in the past, might have been distributed across multiple papers. By presenting all this data in a single manuscript, it delivers a comprehensive and engaging study that could help future developments in the field of biological control against a major insect pest.

Weaknesses:

While none of the findings are particularly groundbreaking, as similar results have been reported for other parasitoid species in prior research, the integration of these results into one comprehensive overview offers valuable biological insights into an interesting new potential biocontrol species.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Major findings or outcomes include a genome for the wasp, characterization of the venom constituents and teratocyte and ovipositor expression profiles, as well as information about Trichopria ecology and parasitism strategies. It was found that Trichopria cannot discriminate among hosts by age, but can identify previously parasitized hosts. The authors also investigated whether superparasitism by Trichopria wasps improved parasitism outcomes (it did), presumably by increasing venom and teratocyte concentrations/densities. Elegant use of Drosophila ectopic expression tools allowed for functional characterization of venom components (Timps), and showed that these proteins are responsible for parasitoid-induced delays in host development. After finding that teratocytes produce a large number of proteases, experiments showed that these contribute to digestion of host tissues for parasite consumption.<br /> The discussion ties these elements together by suggesting that genes used for aiding in parasitism via different parts of the parasitism arsenal arise from gene duplication and shifts in tissue of expression (to venom glands or teratocytes).

Strengths:

The strength of this manuscript is that it describes the parasitism strategies used by Trichopria wasps at a molecular and behavioral level with broad strokes. It represents a large amount of work that in previous decades might have been published in several different papers. Including all of these data in a manuscript together makes for a comprehensive and interesting study.

Weaknesses:

The weakness is that the breadth of the study results in fairly shallow mechanistic or functional results for any given facet of Trichopria's biology. Although none of the findings are especially novel given results from other parasitoid species in previous publications, integrating results together provides significant information about Trichopria biology.

We thank the reviewer for appreciating the importance of our study.

Reviewer #2 (Public Review):

Summary:

Key findings of this research include the sequencing of the wasp's genome, identification of venom constituents and teratocytes, and examination of Trichopria drosophilae (Td)'s ecology and parasitic strategies. It was observed that Td doesn't distinguish between hosts based on age but can recognize previously parasitized hosts. The study also explored whether multiple parasitisms by Td improved outcomes, which indeed it did, possibly by increasing venom and teratocyte levels. Utilizing Drosophila ectopic expression tools, the authors functionally characterized venom components, specifically tissue inhibitors of metalloproteinases (Timps), which were found to cause delays in host development. Additionally, experiments revealed that teratocytes produce numerous proteases, aiding in the digestion of host tissues for parasite consumption. The discussion suggests that genes involved in different aspects of parasitism may arise from gene duplication and shifts in tissue expression to venom glands or teratocytes.

Strengths:

This manuscript provides an in-depth and detailed depiction of the parasitic strategies employed by Td wasps, spanning both molecular and behavioral aspects. It consolidates a significant amount of research that, in the past, might have been distributed across multiple papers. By presenting all this data in a single manuscript, it delivers a comprehensive and engaging study that could help future developments in the field of biological control against a major insect pest.

Weaknesses:

While none of the findings are particularly groundbreaking, as similar results have been reported for other parasitoid species in prior research, the integration of these results into one comprehensive overview offers valuable biological insights into an interesting new potential biocontrol species.

We thank the reviewer for appreciating the importance of our study and for the suggestions on how to improve it.

Reviewer #1 (Recommendations For The Authors):

No additional comments

Reviewer #2 (Recommendations For The Authors):

Minor comments:

Line 68 : would be better to spell out the name of the genus at first mention of the species

It has been corrected as suggested.

Lines 90-92 : This statement does to coincide with the figure. Could you please explain this better?

We have carefully checked the statement and the corresponding figure panels, but failed to find the disparity between them. Perhaps, the similar and neighboring labels of Dsuz and Dsan might cause confusion of the emergence rates. To further avoid this potential, we have modified fig.1b and 1c by highlighting the focal host Dsuz.

Lines 124: could you tell the mention of these genes (Piwi) is important in this context, particularly, for non- full-on experts in this field?

A previous study has revealed the relationship between the expansion of piwi and large genome, we meant to report a different pattern in our focal genome. We understand your confusion might be caused by the inserted statement regarding the repeat that separated them. Thus, we have moved the citation of previous finding to the place immediately precedent to the conclusion.

Line 233: "...composition remains largely unknown.." for Td or in general? Not clear..

Thank you. To make it clear, we have modified this sentence as “Although teratocytes have been reported in several other parasitoids, their molecular composition remains largely unknown in general”.

Line 286: "at a certain time".. confusing, please rephrase.

We have rephrased it as “After a certain time (2 or 4 hours for oviposition choice)”.

Line 293-294: I find this sentence quite hard to follow. Could you please rephrase it and/or expand this concept to make it clearer?

We have modified this sentence as “The parasitic success of Td largely relies on locating a young host; however, Td does not have the ability to discriminate between young and old hosts. Whether Td has evolved any adaptive strategies to compensate for this disadvantage?”

Line 314: "it would be interesting".. this is too weak of an argument. Please corroborate your motivation more soundly.

We have changed this statement as “Because Td allows conditional intraspecific competition, the next compelling question would be whether Td allows interspecific competition with larval parasitoids.”

Line 391: Divergent evolution is too of a big word in this context. I would tune it down to something like: "Studying ecological niche differentiation ".

Thank you. It has been corrected as suggested.

Reviewer #1 (Public Review):

Summary:

In this manuscript, Huang et al have investigated the exercise mimetic role of Eugenol (a natural product) in skeletal muscle and whole-body fitness. The authors report that Eugenol facilitates skeletal muscle remodeling to a slower/oxidative phenotype typically associated with endurance. Eugenol also remodels the fat driving browning the WAT. In both skeletal muscle and fat Eugenol promotes oxidative capacity and mitochondrial biogenesis markers. Eugenol also improves exercise tolerance in a swimming test. Through a series of in vitro studies the authors demonstrate that eugenol may function through the trpv1 channel, Ca mobilization, and activation of CaN/NFAT signaling in the skeletal muscle to regulate slow-twitch phenotype. In addition, Eugenol also induces several myokines but mainly IL-15 through which it may exert its exercise mimetic effects. Overall, the manuscript is well-written, but there are several mechanistic gaps, physiological characterization is limited, and some data are mostly co-relative without vigorous testing (e.g. link between Eugenol, IL15 induction, and endurance). Specific major concerns are listed below.

Strengths:

A natural product activator of the TRPV1 channel that could elicit exercise-like effects through skeletal muscle remodeling. Potential for discovering other mechanisms of action of Eugenol.

Weaknesses:

(1) Figure 1: Histomorphological analysis using immunostaining for type I, IIA, IIX, and IIB should be performed and quantified across different muscle groups and also in the soleus. Fiber type switch measured based on qPCR and Westerns does not sufficiently indicate the extent of fiber type switch. Better images for Fig. 1c should be provided.

(2) Figure 2: Histomorphological analysis for SDH and NADH-TR should be performed and quantified in different muscle groups. Seahorse or oroborous respirometry experiments should be performed to determine the actually increase in mitochondrial respiratory capacity either in isolated mitochondria or single fibers from vehicle and Eugenol-treated mice. Em for mitochondrial should be added to determine the extent of mitochondrial remodeling. The current data is insufficient to indicate the extent of mitochondrial or oxidative remodeling.

(3) Figure 2: Gene expression analysis is limited to a few transcriptional factors. A thorough analysis of gene expression through RNA-seq should be performed to get an unbiased effect of Eugenol on muscle transcriptome. This is especially important because eugenol is proposed to work through CaN/NFAT signaling, major transcriptional regulators of muscle phenotype.

(4) I suggest the inclusion of additional exercise or performance testing including treadmill running, wheel running, and tensiometry. Quantification with a swimming test and measurement of the exact intensity of exercise, etc. is limited.

(5) In addition to muscle performance, whole-body metabolic/energy homeostatic effects should also be measured to determine a potential increase in aerobic metabolism over anaerobic metabolism.

(6) For the swimming test and other measurements, only 4 weeks of vehicle vs. Eugenol treatment was used. For this type of pharmacological study, a time course should be performed to determine the saturation point of the effect. Does exercise tolerance progressively increase with time?

(7) The authors should also consider measuring adaptation to exercise training with or without Eugenol.

(8) Histomorphological analysis of Wat is also lacking. EchoMRI would give a better picture of lean and fat mass.

(9) The experiments performed to demonstrate that Eugenol functions through trpv1 are mostly correlational. Some experiments are needed with trpv1 KO or KD instead of inhibitor. Similarly, KD for other trpv channels should be tested (at least 1-4 that seem to be expressed in the muscle). Triple KO or trpv null cells should be considered to demonstrate that eugenol does not have another biological target.

(10) Eugenol + trpv1 inhibition studies are performed in c2c12 cells and only looks at myofiber genes expression. This is incomplete. Some studies in mitochondrial and oxsphos genes should be done.

(11) The experiments linking Eugenol to ca handling, and calcineurin/nfat activation are all performed in c2c12 cells. There seems to be a link between Eugenol activation and CaN/NFAT activation and fiber type regulation in cells, however, this needs to be tested in mouse studies at the functional level using some of the parameters measured in aims 1 and 2.

(12) The myokine studies are incomplete. The authors show a link between Eugenol treatment and myokines/IL-15 induction. However, this is purely co-relational, without any experiments performed to show whether IL-15 mediates any of the effects of eugenol in mice.

(13) An additional major concern is that it cannot be ruled out that Engenol is uniquely mediating its effects through trpv1. Ideally, muscle-specific trpv1 mice should be used to perform some experiments with Eugenol to confirm that this ion channel is involved in the physiological effects of eugenol.

Comments on revised version:

Unfortunately, in the revision the authors have not addressed any of my comments with new experimental data. For example, some of the histological experiments I suggested are quite easy to do or standardize. Other in vitro experiments could also be conducted to show direct mechanistic link. The current revision does not further improve the manuscript from the 1st submission.

Reviewer #2 (Public Review):

Summary:

The authors examined the hypothesis that eugenol promotes myokines release and f skeletal muscles remoulding by activating the TRPV1-Ca2+-calcineurin-NFATc1 signalling pathway. They first showed that eugenol promotes skeletal muscle transformation and metabolic functions in adipose tissues by analysing changes in the expression of mRNA and proteins of relevant representative protein markers. With similar methodologies, they further found that eugenol increases the expression of mRNA and/or proteins of TRPV1, CaN, NFATC1 and IL-15 in muscle tissues. These processes were, however, prevented by inhibiting TRPV1 and CaN. Similar expression changes were also triggered by increasing intracellular Ca2+ with A23187, suggesting a Ca2+-dependent process.

Strengths:

Different proteins markers were used as a readout of the functions of muscles and adipose tissues and mitochondria and analysed at both mRNA and protein levels. The results were mostly consistent. Although the signaling pathway of TRPV1-Ca2+-CaN-NFAT is not new and well documented, they identified IL-15 as a new downstream target of this pathway combined with use of TRPV1 and CaN inhibitors.

Weaknesses:

Most of the evidence is limited to the molecular level lacking direct functional assays and system analysis. It will be interesting to examine the effect of eugenol on metabolic rate in animals and the role of TRPV1 in this process, as eugenol enhanced food intake without effect on body weight. TRPV1 and CaN inhibition prevented IL-15 expression in C2C12 cells (Fig.9). It remain unknown whether the effect is reproducible in native muscle tissues.

It is also unknown how eugenol enhances TRPV1/CaN expression and alters the expression of many other protein markers in muscle and adipose tissues. Are these effects mediated by activated NFAT or by released IL-15 forming a positive feedback loop? It should at least be discussed.

Many protein blots were presented but no molecular weight markers were shown. It is thus difficult to convince others that the protein bands are the right anticipated positions.

Author response:

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

Reviewer #1 (Public Review):

Weaknesses:

(1) Figure 1: Histomorphological analysis using immunostaining for type I, IIA, IIX, and IIB should be performed and quantified across different muscle groups and also in the soleus. Fiber type switch measured based on qPCR and Westerns does not sufficiently indicate the extent of fiber type switch. Better images for Fig. 1c should be provided.

Thanks for your suggestion. In fact, we attempted immunofluorescent staining for Slow MyHC and Fast MyHC in GAS muscle. However, for the majority of our results, we only observed positive expression of Slow MyHC in a small portion of the muscle sections (as shown in the figure below), so we did not present this result.

In addition, due to the size limitations on uploading image files to Biorxiv, we had to compress the images, resulting in lower resolution pictures. We have attempted to submit clearer images in Fig. 1C

Author response image 1.

Green: Slow MyHC; Red: Fast MyHC

(2) Figure 2: Histomorphological analysis for SDH and NADH-TR should be performed and quantified in different muscle groups. Seahorse or oroborous respirometry experiments should be performed to determine the actually increase in mitochondrial respiratory capacity either in isolated mitochondria or single fibers from vehicle and Eugenol-treated mice. Em for mitochondrial should be added to determine the extent of mitochondrial remodeling. The current data is insufficient to indicate the extent of mitochondrial or oxidative remodeling.

That's a good suggestion. However, we regret to inform you that we are unable to present these results due to a lack of relevant experimental equipment and samples.

(3) Figure 2: Gene expression analysis is limited to a few transcriptional factors. A thorough analysis of gene expression through RNA-seq should be performed to get an unbiased effect of Eugenol on muscle transcriptome. This is especially important because eugenol is proposed to work through CaN/NFAT signaling, major transcriptional regulators of muscle phenotype.

Thanks for your suggestion. Indeed, we believe that in terms of reliability and accuracy, RNA-seq is not as good as RT-qPCR. The advantage of RNA-seq lies in its high throughput, making it suitable for screening unknown transcription factor regulatory mechanisms. In this study, the signaling pathways regulating myokines and muscle fiber type transformation are known and limited, with only the CaN/NFATc1 and the AMPK pathway. Since eugenol mainly acts through the Ca2+ pathway, we primarily focus on the CaN/NFATc1 signaling pathway.

(4) I suggest the inclusion of additional exercise or performance testing including treadmill running, wheel running, and tensiometry. Quantification with a swimming test and measurement of the exact intensity of exercise, etc. is limited.

That's a good suggestion. We apologize for being unable to detect this indicator due to a lack of relevant experimental equipment.

(5) In addition to muscle performance, whole-body metabolic/energy homeostatic effects should also be measured to determine a potential increase in aerobic metabolism over anaerobic metabolism.

That's a good suggestion. We apologize for being unable to detect this indicator due to a lack of relevant experimental equipment.

(6) For the swimming test and other measurements, only 4 weeks of vehicle vs. Eugenol treatment was used. For this type of pharmacological study, a time course should be performed to determine the saturation point of the effect. Does exercise tolerance progressively increase with time?

Thanks for your suggestion. Due to the potential damage that exhaustive swimming tests inflict on mice, the tested mice are subsequently eliminated to avoid potential interference with the experiment. Therefore, this experiment is only suitable for conducting tests at individual time points.

(7) The authors should also consider measuring adaptation to exercise training with or without Eugenol.

Thanks for your suggestion. The purpose of this study is to investigate whether eugenol mimics exercise under standard dietary conditions. In our future research, we will consider exploring the effects of eugenol under HFD and exercise conditions.

(8) Histomorphological analysis of Wat is also lacking. EchoMRI would give a better picture of lean and fat mass.

That's a good suggestion. However, we did not collect the slices of WAT tissue, so we are unable to supplement this result, we feel sorry for it. In addition, we apologize for being unable to detect lean and fat mass due to a lack of EchoMRI equipment.

(9) The experiments performed to demonstrate that Eugenol functions through trpv1 are mostly correlational. Some experiments are needed with trpv1 KO or KD instead of inhibitor. Similarly, KD for other trpv channels should be tested (at least 1-4 that seem to be expressed in the muscle). Triple KO or trpv null cells should be considered to demonstrate that eugenol does not have another biological target.

Thanks for your professional suggestion. AMG-517 is a specific inhibitor of TRPV1, with a much greater inhibitory effect on TRPV1 compared to other TRP channels. AMG-517 inhibits capsaicin (500 nM), acid (pH 5.0), or heat (45°C) induced Ca2+ influx in cells expressing human TRPV1, with IC50 values of 0.76 nM, 0.62 nM, and 1.3 nM, respectively. However, the IC50 values of AMG-517 for recombinant TRPV2, TRPV3, TRPV4, TRPA1, and TRPM8 cells are >20 μM (Gavva, 2008). Therefore, we believe that using AMG-517 instead of TRPV1 KO cells is sufficient to demonstrate the involvement of TRPV1 in the function of eugenol.

While this study did not exclude the possibility of other TRP channels' involvement, it was based on the fact that eugenol does not promote mRNA expression of other TRP channels, as shown in Fig4A-C. Indeed, as far as we know, besides TRPV1, the effects of other TRP channels on myofiber type transformation remain unknown. This is an aspect that we plan to investigate in the future.

Reference

Gavva NR, Treanor JJ, Garami A, et al. Pharmacological blockade of the vanilloid receptor TRPV1 elicits marked hyperthermia in humans. Pain. 2008;136(1-2):202-210.

(10) Eugenol + trpv1 inhibition studies are performed in c2c12 cells and only looks at myofiber genes expression. This is incomplete. Some studies in mitochondrial and oxsphos genes should be done.

Thanks for your suggestion. In the inhibition experiment, we additionally examined the expression of mitochondrial complex proteins as shown in Figure 5C. And the relevant description has been added in lines 178-183 and 764-765.

(11) The experiments linking Eugenol to ca handling, and calcineurin/nfat activation are all performed in c2c12 cells. There seems to be a link between Eugenol activation and CaN/NFAT activation and fiber type regulation in cells, however, this needs to be tested in mouse studies at the functional level using some of the parameters measured in aims 1 and 2.

Thank you for your professional suggestion. We will attempt to continue these experiments in future studies.

(12) The myokine studies are incomplete. The authors show a link between Eugenol treatment and myokines/IL-15 induction. However, this is purely co-relational, without any experiments performed to show whether IL-15 mediates any of the effects of eugenol in mice.

Indeed, previous studies have adequately demonstrated the regulation of skeletal muscle oxidative metabolism by IL-15. The initial aim of this experiment was to investigate the mechanism by which eugenol promotes IL-15 expression. Through inhibition assays, EMSA, and dual luciferase reporter gene experiments, we have thoroughly demonstrated that eugenol promotes IL-15 expression via the CaN/NFATc1 signaling pathway, thus establishing a novel link between CaN/NFATc1 signaling and the myokine IL-15 expression. In the subsequent experiments, we plan to knock out IL-15 in eugenol-treated C2C12 cells to explore whether IL-15 mediates the effects of eugenol. This will be another aspect of our investigation.

(13) An additional major concern is that it cannot be ruled out that Engenol is uniquely mediating its effects through trpv1. Ideally, muscle-specific trpv1 mice should be used to perform some experiments with Eugenol to confirm that this ion channel is involved in the physiological effects of eugenol.

As you suggested, we agree that muscle-specific TRPV1 mice should be used to conduct some experiments with eugenol. In our mice experiments, due to the lack of validation of skeletal muscle-specific TRPV1 knockout, we indeed cannot rule out that eugenol is uniquely mediating its effects through TRPV1. We acknowledge this as a limitation of our study. However, due to limitations in research funding and time, we are currently unable to supplement these experiments. Nevertheless, we believe that our results from in vitro experiments using a TRPV1 inhibitor (which selectively inhibits TRPV1) provide evidence of eugenol's action through TRPV1.

Reviewer #2 (Public Review):

Weaknesses:

(1) Apart from Fig.2A and 2B, they mostly utilised protein expression changes as an index of tissue functional changes. Most of the data supporting the conclusions are thus rather indirect. More direct functional evidence would be more compelling. For example, a lipolysis assay could be used to measure the metabolic function of adipocytes after eugenol treatment in Fig.3. Functional activation of NFAT can be demonstrated by examining the nuclear translocation of NFAT.

Thank you for your professional suggestion. Indeed, as shown in Figure 4G-I, we detected the expression of NFATc1 in the nucleus to illustrate its nuclear translocation.

(2) To further demonstrate the role of TRPV1 channels in the effects of eugenol, TRPV1-deficient mice and tissues could also be used. Will the improved swimming test in Fig. 2B and increased CaN, NFAT, and IL-15 triggered by eugenol be all prevented in TRPV1-lacking mice and tissues?

Thank you for your professional suggestion. We agree that muscle-specific TRPV1 mice should be used to conduct some experiments with eugenol. However, due to limitations in research funding and time, we are currently unable to supplement these experiments.

(3) Direct evidence of eugenol activation of TRPV1 channels in skeletal muscles is also lacking. The flow cytometry assay was used to measure Ca2+ changes in the C2C12 cell line in Fig. 5A. But this assay is rather indirect. It would be more convincing to monitor real-time activation of TRPV1 channels in skeletal muscles not in cell lines using Ca2+ imaging or electrophysiology.

Thank you for your professional suggestion. As you suggested, we initially planned to use patch-clamp technique to detect membrane potential changes in skeletal muscle cells under eugenol treatment. However, due to experimental technical limitations, this experiment was not successfully conducted. Therefore, we were compelled to rely solely on flow cytometry to detect Ca2+ levels.

Reviewer #2 (Recommendations For The Authors):

(1) Most of the mRNA and protein data are consistent with each other. However, some of them are not obvious. For example, PGC1a mRNA was increased by eugenol in Fig. 2C but not seen in protein in Fig. 2D. Similarly, Complex I and V mRNA was increased in Fig. 2C but not obvious at protein levels in Fig. 2D, even though they claimed that Complex I and V were both upregulated by eugenol (see: line 123). Another example: IL-15 mRNA was increased by EUG100 but not by EUG50 in the GAS muscle in Fig. 8A. However, EUG50 increased IL-15 protein expression in Fig. 8B. Similar conflict was also seen in IL-15 expression in the TA muscle in Fig. 8A and 8C.

Thanks for your question. As shown in the table below, by standardizing with β-Actin, our statistical data indeed indicate that eugenol promotes the expression of Complex I and V proteins (although the upregulation is minimal). Additionally, protein and mRNA expression do not always correlate, which may be due to potential post-transcriptional and post-translational regulation.

Author response table 1.

(2) Line 115: Figure 2A should be Figure 2B; Line 119: Figure 2B should be Figure 2A. Alternatively, swap Fig2A with Fig. 2B.

Thanks for your correction, we have revised the relevant content in lines 111-113 and 724-725.

(3) Abbreviations of ADF and ADG in Fig. 3A should be defined.

Thank you for your suggestion. We have defined these abbreviations in lines 123-125.

(4) Line 154: TRPV1 mRNA expression was promoted by 25 and 50uM eugenol, not by 12.5uM.

Thank you for your correction. We have revised it in line 150.

(5) Line 173: Increased expression of NFAT suggests that NFAT is activated. This is a rather weak statement. It is more convincing to show the nuclear translocation of NFAT by eugenol treatment.

Thank you for your correction. We have revised the describtion in line 166.

(6) Line 185: The data showing EUG increased slow MyHC fluorescence intensity in Fig. 5D are not clear at all. Quantification is required.

Thank you for your suggestion. We have attempted to submit clearer images in Figure 5E, and the quantification have been provided.

(7) Line 235: IL-15 expression is positively correlated with MyHC IIa, suggesting IL-15 is a slow muscle myokine (See line 2398). However, MyHC IIa is a marker of fast muscle fibres (see line 50).

Thank you for your correction. As you pointed, MyHC IIa is fast-twitch oxidative muscle fiber. We have replaced ‘slow’ with ‘oxidative’ in line 235.

(8) Fig.9C and 9D show that inhibition of TRPV1 and CaN attenuated the upregulation of IL-15 mRNA and protein by eugenol in C2C12 cell line. This result is important in demonstrating the link of TRPV1 and CaN to IL-15. It will be more interesting and physiologically relevant to perform this experiment in primary skeletal muscle cells isolated from mice.

Thank you for your suggestion. This is indeed an interesting idea. We will attempt to continue our experiments in mice and primary porcine muscle cells in future studies.

(9) It is concerning that 4-week-old male mice were used for the study. The 4-week-old mice are immature. Adult mice over 8 weeks should be used. It is thus unknown whether the findings are broadly applicable to adult age.

Thanks for your professional question. Age indeed has an impact on the muscle fiber type in mammals. Based on previously observed patterns of muscle fiber changes with age in various mammals (Katsumata et al., 2021; Pandorf et al., 2012; Hill et al., 2020), we believe that changes in muscle fiber types occur more frequently in juvenile mammals, mainly manifesting as a sharp increase in fast muscle fibers. Therefore, interventions during the juvenile stage might be more effective in promoting the transformation of fast to slow muscle fibers. As a result, in most of our group's research using nutritional interventions to regulate muscle fiber types, we tend to start interventions from the age of 4 weeks in mice. If we began intervention at 8 weeks, we speculate that the effectiveness would not be as potent as starting at 4 weeks. Below are the patterns of muscle fiber changes with age in various mammalian models, provided for reference:

(1) Changes in muscle fiber types with age in pigs:

As shown in the following figure, there is a dramatic change in the muscle fiber types 12 days post birth in pigs, especially with a sharp increase in fast muscle fibers, which continues until day 45. After 45 days of age, the changes in muscle fiber types become relatively gradual.

Author response table 2.

Developmental change Of proportions Of muscle fiber types in Longissimus dorsi muscle determined by histochemical analysis for myosin adenosine triphosphatase activity (%)

Least squares means and pooled standard errors (n = 3). MHC, myosin heavy chain; ND, not detected. *P<0.10, **P<0.01 Least square means followed by different letters on the same row are significantly different (P < 0.05).

Reference:

Katsumata, M., Yamaguchi, T., Ishida, A., & Ashihara, A. (2017). Changes in muscle fiber type and expression of mRNA of myosin heavy chain isoforms in porcine muscle during pre- and postnatal development. Animal science journal, 88(2), 364–371.

(2) Changes in muscle fiber types with age in rats:

As illustrated in the subsequent figure, the muscle fiber types in rats undergo significant changes before 20 days of age (3-week-old), notably with a pronounced increase in type IIb fast-twitch fibers. After reaching 20 days of age, the changes in type IIb muscle fibers tend to stabilize and become more gradual.

Author response image 2.

Reference:

Pandorf, C. E., Jiang, W., Qin, A. X., Bodell, P. W., Baldwin, K. M., & Haddad, F. (2012). Regulation of an antisense RNA with the transition of neonatal to IIb myosin heavy chain during postnatal development and hypothyroidism in rat skeletal muscle. American journal of physiology. 302(7), R854–R867.

(3) Changes in muscle fiber types with age in mice:

As depicted in the following figure, when comparing 10-week-old mice to 78-week-old aged mice, there are no significant changes in muscle fiber types.

Author response image 3.

Reference:

Hill, C., James, R. S., Cox, V. M., Seebacher, F., & Tallis, J. (2020). Age-related changes in isolated mouse skeletal muscle function are dependent on sex, muscle, and contractility mode. American journal of physiology. Regulatory, integrative and comparative physiology, 319(3), R296–R314.

eLife assessment

This important manuscript follows up on previous findings from the same lab supporting the idea that deficits in learning due to enhanced synaptic plasticity are due to saturation effects. Compelling evidence is presented that behavioral learning deficits associated with enhanced synaptic plasticity in a transgenic mouse model can be rescued by manipulations designed to reverse the saturation of synaptic plasticity. In particular, the finding that a previously FDA-approved therapeutic can rescue learning could provide new insights for biologists, psychologists, and others studying learning and neurodevelopment.

Reviewer #1 (Public Review):

Summary:

Shakhawat et al., investigated how enhancement of plasticity and impairment could result in the same behavioral phenotype. The authors tested the hypothesis that learning impairments result from saturation of plasticity mechanisms and had previously tested this hypothesis using mice lacking two class I major histocompatibility molecules. The current study extends this work by testing the saturation hypothesis in a Purkinje-cell (L7) specific Fmr1 knockout mouse mice, which have enhanced parallel fiber-Purkinje cell LTD. The authors found that L7-Fmr1 knockout mice are impaired on an oculomotor learning task and both pre-training, to reverse LTD, and diazepam, to suppress neural activity, eliminated the deficit when compared to controls.

Strengths:

This study tests the "saturation hypothesis" to understand plasticity in learning using a well-known behavior task, VOR, and an additional genetic mouse line with a cerebellar cell-specific target, L7-Fmr1 KO. This hypothesis is of interest to the community as it evokes novel inquisition into LTD that has not been examined previously.

Utilizing a cell-specific mouse line that has been previously used as a genetic model to study Fragile X syndrome is a unique way to study the role of Purkinje cells and the Fmr1 gene. This increases the understanding in the field in regards to Fragile X syndrome and LTD.

The VOR task is a classic behavior task that is well understood, therefore using this metric is very reliable for testing new animal models and treatment strategies. The effects of pretraining are clearly robust and this analysis technique could be applied across different behavior data sets.

The rescue shown using diazepam is very interesting as this is a therapeutic that could be used in clinical populations as it is already approved.

All previous comments have been addressed with additional studies, explanations, or analyses. These additions strengthen a very impactful study.

The authors achieved their study objectives and the results strongly support their conclusion and proposed hypothesis. This work will be impactful on the field as it uses a new Purkinje-cell specific mouse model to study a classic cerebellar task. The use of diazepam could be further analyzed in other genetic models of neurodevelopmental disorders to understand if effects on LTD can rescue other pathways and behavior outcomes.

Reviewer #2 (Public Review):

This manuscript explores the seemingly paradoxical observation that enhanced synaptic plasticity impairs (rather than enhances) certain forms of learning and memory. The central hypothesis is that such impairments arise due to saturation of synaptic plasticity, such that the synaptic plasticity required for learning can no longer be induced. A prior study provided evidence for this hypothesis using transgenic mice that lack major histocompatibility class 1 molecules and show enhanced long-term depression (LTD) at synapses between granule cells and Purkinje cells of the cerebellum. The study found that a form of LTD-dependent motor learning-increasing the gain of the vestibulo-ocular reflex (VOR)-is impaired in these mice and can be rescued by manipulations designed to "unsaturate" LTD. The present study extends this line of investigation to another transgenic mouse line with enhanced LTD, namely, mice with the Fragile X gene knocked out. The main findings are that VOR gain increase learning is selectively impaired in these mice but can be rescued by specific manipulations of visuomotor experience known to reverse cerebellar LTD. Additionally, the authors show that a transient global enhancement of neuronal inhibition also selectively rescues gain increase learning. This latter finding has potential clinical relevance since the drug used to boost inhibition, diazepam, is FDA-approved and commonly used in the clinic. The evidence provided for the saturation is somewhat indirect because directly measuring synaptic strength in vivo is technically difficult. Nevertheless, the experimental results are solid. In particular, the specificity of the effects to forms of plasticity previously shown to require LTD is remarkable.

Author response:

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

eLife assessment<br /> This important manuscript follows up on previous findings from the same lab supporting the idea that deficits in learning due to enhanced synaptic plasticity are due to saturation effects. Compelling evidence is presented that behavioral learning deficits associated with enhanced synaptic plasticity in a transgenic mouse model can be rescued by manipulations designed to reverse the saturation of synaptic plasticity. In particular, the finding that a previously FDA-approved therapeutic can rescue learning could provide new insights for biologists, psychologists, and others studying learning and neurodevelopment.

eLife assessment, Significance of findings

This valuable manuscript follows up on previous findings from the same lab supporting the idea that deficits in learning due to enhanced synaptic plasticity are due to saturation effects. 

According to the eLife criteria for assessing significance, the “valuable” assessment indicates “findings that have theoretical or practical implications for a subfield.” We have revised the manuscript to emphasize the “theoretical and practical implications beyond a single subfield” which “substantially advance our understanding of major research questions”, with “profound implications” and the potential for “widespread influence,” the eLife criteria for a designation of “landmark” significance.   

The most immediate implications of our results are for the two major neuroscience subfields of cerebellar research and autism research. However, as recognized by Reviewer 2, the implications are much broader than that: “the finding that a previously FDA-approved therapeutic can rescue learning could provide important new insights for biologists, psychologists, and others studying learning and neurodevelopment.” We have substantially revised the Discussion section of the manuscript to more explicitly lay out how the central idea of our manuscript-- that the capacity for learning at any given moment is powerfully influenced by dynamic, activity- and plasticity-dependent changes in the threshold for synaptic plasticity over short timescales of tens of minutes to hours --has implications for scientific thinking and experiments on plasticity and learning throughout the brain, as well as clinical practice for a wide array of brain disorders associated with altered plasticity and learning impairment. 

To emphasize the broad conceptual implications of our research, we have reframed our conclusions in terms of metaplasticity rather than saturation of plasticity throughout the revised manuscript. In our previous submission, we had used the “saturation “ terminology for continuity with our previous NguyenVu et al 2017 eLife paper, and mentioned the related idea of threshold metaplasticity in a single sentence: “Similarly, the aberrant recruitment of LTD before training may lead, not to its saturation per se, but to some other kind of reduced availability, such as an increased threshold for its induction (Bienenstock, Cooper, and Munro, 1982; Leet, Bear, and Gaier, 2022).” However, we now appreciate that metaplasticity is a more general conceptual framework for our findings, and therefore emphasize this concept in the revised manuscript, while still making the conceptual link with the “saturation” idea presented in NguyenVu et al 2017 (lines 236-238). 

The concept of a sliding threshold for synaptic plasticity (threshold metaplasticity) was proposed four decades ago by Bienenstock, Cooper and Munro (1982) as a mechanism for countering an instability inherent in Hebbian plasticity whereby correlated pre- and post-synaptic activity strengthens a synapse, which leads to an increase in correlated activity, which in turn leads to further strengthening. To counter this, BCM proposed a sliding threshold whereby increases in neural activity increase the threshold for LTP and decreases in activity decrease the threshold for LTP, thereby providing a mechanism for stabilizing firing rates and synaptic weights. This BCM sliding threshold model has been highly influential in theoretical and computational neuroscience, but experimental evidence for whether and how such a mechanism functions in vivo has been quite limited.  

Our work extends the previous, limited experimental evidence for a BCM-like sliding threshold in vivo in several significant ways, which we now discuss in the revised manuscript:

First, we analyze threshold metaplasticity at synapses where the plasticity is not Hebbian and lacks the inherent instability that inspired the BCM model. The synapses onto cerebellar Purkinje cells have been described as “anti-Hebbian” because the associative form of plasticity is synaptic LTD of excitatory inputs. This anti-Hebbian associative plasticity lacks the instability inherent in Hebbian plasticity. Moreover, a BCM-like sliding threshold that increases the threshold for associative LTD with increased firing rates and decreases threshold for LTD with decreased firing rates would tend to oppose rather than support the stability of firing rates, nevertheless we find evidence for this in our experimental results. Thus, for cerebellar LTD, the central function of the sliding threshold may not be the stabilization of firing rates, but rather to limit plasticity in order to suppress the overwrite of new memories or to allocate different memories to the synapses of different Purkinje cells. 

Second, we analyze the influence of a BCM-like sliding threshold for plasticity on behavioral learning. Most previous evidence for the BCM model in vivo has derived from studies of the effects of sensory deprivation (e.g., monocular occlusion) on the functional connectivity of sensory circuits (Kirkwood et al., 1996; Desai et al. 2002; Fong et al., 2021) rather than on learning per se.  

Third, our results provide evidence for major changes in the threshold for plasticity over short time scales and with more subtle manipulations of neural activity than used in previous studies, with practical implications for clinical application. Previously, metaplasticity has been demonstrated with sensory deprivation over multiple days (Kirkwood et al., 1996; Desai et al. 2002) or with drastic changes in neural activity, such as with TTX in the retina (Fong et al, 2021), TMS (Hamada et al 2008), or high frequency electrical stimulation in vitro (Holland & Wagner 1998; Montgomery & Madison 2002) or in vivo (Abraham et al 2001). In contrast, we provide evidence for metaplasticity induced by 30 min of behavioral manipulation (pre-training) and by the relatively subtle pharmacological manipulation of activity with systemic administration of diazepam, a drug approved for humans. Thus, our work contributes not only conceptually to understanding the function of threshold metaplasticity in vivo, but also offers practical observations that could pave the way for novel therapeutic interventions.  

Fourth, whereas efforts to enhance plasticity and learning have largely focused on increasing the excitability of neurons during learning to help cross the threshold for plasticity (e.g., Albergaria et al., 2018; Yamaguchi et al., 2020; Le Friec et al., 2017), we take the opposite, somewhat counterintuitive approach of inhibiting the excitability of neurons during a period before learning to reset the threshold for plasticity to a state compatible with new learning. To our knowledge, the only other application of such an approach in an animal model of a brain disorder has been inhibiting peripheral (retinal) activity with TTX for treatment of amblyopia (Fong et al, 2021). Our findings from CNS inhibition with a single systemic dose of diazepam greatly expands the potential applications, which could readily be tested in other mouse models of human disorders, and other learning deficits. Even in cases where the specific synaptic impairments and circuitry are less fully understood, the impact of suppressing neural activity during a period before training to reduce the threshold for plasticity could be empirically tested.  

Fifth, our work extends the consideration of a BCM-like sliding threshold for plasticity to the cerebellum, whereas previous work has focused on models and experimental studies of forebrain circuits. Currently there is a surge of interest in the contribution of the cerebellum to functions and brain disorders previously ascribed to forebrain, hence we anticipate broad interest in this work. 

Sixth, our results suggest that the history of plasticity rather than the history of firing rates may be the homeostat controlling the threshold for plasticity, at least at the synapses under consideration. Diazepam pre-treatment only enhanced learning in the L7-Fmr1 KO mice with a low “baseline” threshold for plasticity, as measured in vitro, and not WT mice. This suggests it is not the neural activity per se that drives the change in threshold for plasticity, but the interaction of activity with the plasticity mechanism.

In the revised Discussion, we make all of the above points, to make the implications more clear to readers.  

The broad interest in this topic is illustrated by two concrete examples. First, an abstract of this work was honored with selection for oral presentation at the November 2023 Symposium of the Molecular and Cellular Cognition Society, a conceptually wide-ranging organization with thousands of members worldwide. Second, the most closely related published work on activity-dependent metaplasticity in vivo, the Fong et al 2021 eLife paper demonstrating reversal of amblyopia by suppression of activity in the retina by TTX, attracted such broad interest, not just of professional scientists, but also the general public, as to be reported on National Public Radio’s All Things Considered, with an audience of 11.9 million people worldwide.  

In considering the potential of this work for widespread influence, it is important to note that activitydriven changes in the threshold for plasticity could very well be a general property of most if not all synapses, yet very little is known about its function in vivo, especially during learning.  Therefore, the seminal conceptual and practical advances described above have the potential for profound implications throughout neuroscience, psychiatry, neurology and computer science/AI, the eLife criterion for designation as “landmark” in significance. We respectfully request that the reviewers and editor reassess the significance of our findings in light of our much-improved discussion of the broad significance of the work.

eLife assessment, Strength of support

Convincing evidence is presented that behavioral learning deficits associated with enhanced synaptic plasticity in a transgenic mouse model can be rescued by manipulations designed to reverse the saturation of synaptic plasticity. In particular, the finding that a previously FDA-approved therapeutic can rescue learning could provide important new insights for biologists, psychologists, and others studying learning and neurodevelopment.

The designation of “Convincing” indicates “methodology in line with current state-of the-art.” In the revised Discussion, we more clearly highlight that our evidence is “more rigorous than current state-ofthe-art” in several respects, thereby meeting the eLife criterion for “Compelling”:

(1) Comparison of learning deficits and effects of behavioral and pharmacological pretreatment across five closely related oculomotor learning tasks, which all depend on the same region of the cerebellum (the flocculus), but which previous work has found to vary in their dependence on LTD at the cerebellar parallel fiber-to-Purkinje cell synapses. 

The “state-of-the-art” behavioral standard in the field of learning is assessment of a single learning task that depends on a given brain area, with the implicit or explicit assumption that the task chosen is representative of “cerebellum-dependent learning” or hippocampus-, amygdala-, basal ganglia-, cortex- dependent learning, etc. Sometimes there is a no-learning behavioral control. 

Our study exceeds this standard by comparing across many different closely related learning tasks, which all depend on the cerebellar flocculus and other shared vestibular, visual, and oculomotor circuitry, but vary in their dependence on LTD at the cerebellar parallel fiber-to-Purkinje cell synapses. In the original submission, we reported results for high-frequency VOR-increase learning that were dramatically different than for three other VOR learning tasks for which there is less evidence for a role of LTD. Reviewer 2 noted, “the specificity of the effects to forms of plasticity previously shown to require LTD is remarkable.” In the revised manuscript, we provide new data for a second oculomotor learning task in which LTD has been implicated, OKR adaptation, with very similar results as for high-frequency VORincrease learning. The remarkable specificity of both the learning deficits and the effects of pre-training manipulations, in two different lines of mice, for the two specific learning tasks in which LTD has been most strongly implicated, and not the other three oculomotor learning tasks, substantially strengthens the evidence for the conclusion that the learning deficits and effects of pre-training are related specifically to the lower threshold for LTD, rather than the result of some other effect of the gene KO or pre-treatment on the cerebellar or oculomotor circuitry (discussed on lines 270-290 of revised manuscript). 

(2) Replication of findings in more than one line of mice, targeting distinct signaling pathways, with a common impact of enhancing LTD at the cerebellar PF-Purkinje cell synapses.  

State-of-the-art is to report the effects of one specific molecular signaling pathway on behavior. 

In the first part of this Research Advance, we replicate the findings of Nguyen-Vu et al 2017 for a completely different line of mice with enhanced LTD at the parallel fiber-to-Purkinje cell synapses. Like the comparison across LTD-dependent and LTD-independent oculomotor learning tasks, the comparison across completely different lines of mice with enhanced LTD strengthens the evidence that the shared behavioral phenotypes are a reflection of the state of LTD rather than other “off-target” effects of each mutation (discussed on lines 291-309 of revised manuscript).

(3) Reversal of learning impairments with more than one type of treatment. 

State-of-the-art is to be able to reverse a learning deficit or other functional impairment in an animal model of a brain disorder with a single treatment; indeed, success in this respect is viewed as wildly exciting, as evidenced by the reception by the scientific and lay communities of the Fong et al, 2021 eLife report of reversal of amblyopia by TTX treatment of the retina. 

In the current work, we demonstrate reversal of learning deficits with two different types of treatment during the period before training, one behavioral and one pharmacological. The current diazepam pretreatment results provide a fundamentally new type of evidence for the hypothesis that the threshold for LTD and LTD-dependent learning varies with the recent history of activity in the circuit, complementing the evidence from behavioral and optogenetic pre-training approaches used previously in Nguyen-Vu et al, 2017 (discussed on lines 151-158 and 246-255 of revised manuscript).

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Shakhawat et al., investigated how enhancement of plasticity and impairment could result in the same behavioral phenotype. The authors tested the hypothesis that learning impairments result from saturation of plasticity mechanisms and had previously tested this hypothesis using mice lacking two class I major histocompatibility molecules. The current study extends this work by testing the saturation hypothesis in a Purkinje-cell (L7) specific Fmr1 knockout mouse mice, which have enhanced parallel fiber-Purkinje cell LTD. The authors found that L7-Fmr1 knockout mice are impaired on an oculomotor learning task and both pre-training, to reverse LTD, and diazepam, to suppress neural activity, eliminated the deficit when compared to controls.

Strengths:

This study tests the "saturation hypothesis" to understand plasticity in learning using a well-known behavior task, VOR, and an additional genetic mouse line with a cerebellar cell-specific target, L7-Fmr1 KO. This hypothesis is of interest to the community as it evokes a novel inquisition into LTD that has not been examined previously.

Utilizing a cell-specific mouse line that has been previously used as a genetic model to study Fragile X syndrome is a unique way to study the role of Purkinje cells and the Fmr1 gene. This increases the understanding in the field in regards to Fragile X syndrome and LTD.

The VOR task is a classic behavior task that is well understood, therefore using this metric is very reliable for testing new animal models and treatment strategies. The effects of pretraining are clearly robust and this analysis technique could be applied across different behavior data sets.

The rescue shown using diazepam is very interesting as this is a therapeutic that could be used in clinical populations as it is already approved.

There was a proper use of controls and all animal information was described. The statistical analysis and figures are clear and well describe the results.

We thank the reviewer for summarizing the main strengths of our original submission. We have further strengthened the revised submission by 

(1) more fully discussing the broad conceptual implications, as outlined above; 

(2) adding additional new data (Fig. 5) showing that another LTD-dependent oculomotor learning task, optokinetic reflex (OKR) adaptation, is impaired in the L7-Fmr1 KO mice and rescued by pre-treatment with diazepam, as we had already shown for high-frequency VOR increase learning;  3) responding to the specific points raised by the reviewers, as detailed below.

Weaknesses:

While the proposed hypothesis is tested using genetic animal models and the VOR task, LTD itself is not measured. This study would have benefited from a direct analysis of LTD in the cerebellar cortex in the proposed circuits.

Our current experiments were motivated by the direct analysis of cerebellar LTD in Fmr1 knock out mice that was already published (Koekkoek et al., 2005). In that previous work, LTD was analyzed in both Purkinje cell selective L7-Fmr1 KO mice (Koekkoek et al., 2005; Fig. 4D), as used in our study, and global Fmr1 knock out mice (Koekkoek et al., 2005; Fig. 4B). Both lines were found to have enhanced LTD, as cited in the Introduction of our manuscript (lines 48-51, 63-64). The goal of our current study was to build on this previous work by analyzing the behavioral correlates of the findings from this previous, direct analysis of LTD. 

Diazepam was shown to rescue learning in L7-Fmr1 KO mice, but this drug is a benzodiazepine and can cause a physical dependence. While the concentrations used in this study were quite low and animals were dosed acutely, potential side-effects of the drug were not examined, including any possible withdrawal. 

In humans, diazepam (valium) is one of the most frequently prescribed drugs in the world, and the side effects and withdrawal symptoms have been extensively studied and documented.1 Withdrawal symptoms are generally not observed with treatments of less than 2 weeks (Brett and Murnion, 2015). After longterm treatments tapering of the dosage is recommended to mitigate withdrawal (Brett and Murnion, 2015 and https://americanaddictioncenters.org/valium-treatment/withdrawal-duration). The extensive data on the safety of diazepam in humans lowers the barrier to potential clinical translation of our basic science findings, although we emphasize that our own expertise is scientific, and translation to Fragile X patients or other patient groups will require additional development of the research by clinicians.

Given the extensive history of research on this drug, we focused on looking for side effects that would reflect an adverse effect of diazepam on the function of the same oculomotor neural circuitry whose ability to support certain oculomotor learning tasks was improved after diazepam. In other words, we assessed whether the pharmacological manipulation was enhancing certain functions of a given circuit at the expense of others. As we note (line 164), “The acute effect of diazepam administration [measured 2 hours after administration] was to impair learning” in both WT and L7-Fmr1 KO mice. One could consider this a side effect. More importantly, we also tested extensively for oculomotor side-effects during the therapeutic period when learning impairments were eliminated in the L7-Fmr1 KOs, 18-24 hours post-administration, and have a full section of the Results describing our findings about this, titled “Specificity of pre-training effects on learning.” As described in the Results and Discussion (lines 184195, 312-318, Figure 3, figure 3-supplement1; figure 4B; figure 5-supplement 1), we found no such adverse side-effects, which is again encouraging with respect to the translational potential of our findings. 

This drug is not specific to Purkinje cells or cerebellar circuits, so the action of the drug on cerebellar circuitry is not well understood for the study presented.

The effects of diazepam are indeed not specific to Purkinje cells, but rather are known to be widespread. Diazepam is a positive allosteric modulator of GABAA receptors, which are found throughout the brain, including the cerebellum. When delivered systemically, as we did in our experiments, diazepam will suppress neural activity throughout the brain by facilitating inhibition, as documented by decades of previous research with this and related benzodiazepines, including dozens of studies of the effects of diazepam in the cerebellum. 

To our knowledge, there is currently no drug that can specifically inhibit Purkinje cells, especially one that can be given systemically to cross the blood-brain barrier. Moreover, if such a drug did exist, we would not predict it to have the same effect as diazepam in reversing the learning deficits of the L7-Fmr1 KO mice, because the latter presumably depends on suppression of activity in the cerebellar granule cells and neurons of the inferior olive, whose axons form the parallel fibers and climbing fibers, and whose correlated activity controls LTD at the parallel fiber-Purkinje cell synapses.  

We have revised the text to clarify the key point that despite its widespread action on the brain, the effects of diazepam on cerebellum-dependent learning were remarkably specific (lines 184-195, 210-228, 312318). During the period 18-24 hours after a single dose of diazepam, the learning deficits of L7-Fmr1 KO mice on two LTD-dependent oculomotor learning tasks were completely reversed, with no effects on the same tasks in WT mice, and no effects (“side-effects”) in L7-Fmr1 KO mice or WT mice on other, LTDindependent oculomotor learning tasks that depend on the same region of the cerebellum, and no effects on baseline performance of visually or vestibularly driven eye movements. 

As described in the revised Discussion (lines 318-323), the non-specific mild suppression of neural activity throughout the brain by diazepam makes it a potentially generalizable approach for inducing BCM-like shifts in the threshold for associative plasticity to facilitate subsequent learning. More specifically, diazepam-mediated reduction of activity throughout the brain has the potential to lower any aberrantly high thresholds for associative plasticity at synapses throughout the brain, and thereby reverse any learning deficits associated with such aberrantly high plasticity thresholds. This approach might even be useful in cases where the neural circuitry supporting a given behavior is not well characterized and the specific synapses responsible for the learning deficit are unknown. On lines 323-327 we compare this generalizable approach with the challenges of designing task- and circuit-specific approaches to reset the threshold for plasticity, particularly in circuits that are less well characterized than the oculomotor circuit.

It was not mentioned if L7-Fmr1 KO mice have behavior impairments that worsen with age or if Purkinje cells and the cerebellar microcircuit are intact throughout the lifespan. 

At the adult ages used in our study (8-22 weeks), the oculomotor circuitry, including the Fmr1-deficient Purkinje cells, appears to be functionally intact because all of the oculomotor performance and learning tasks we tested were either normal, or could be restored to normal with brief behavioral and/or pharmacological pre-treatment.  

Any degeneration of the Fmr1-deficient Purkinje cells or cerebellar microcircuit or additional behavioral impairments at older ages, if they should exist, would not alter our interpretation of the results from 8-22 week old adults regarding history- and activity-dependent changes in the capacity for LTD-dependent learning. Therefore, we leave the question of changes throughout the lifespan to investigators with an interest and expertise in development and/or aging. 

Only a small handful of the scores of previous studies of the Fmr1 KO mouse model have investigated age-dependent effects; the reviewer may be interested in papers such as Tang et al., 2015 (doi: 10.1073/pnas.1502258112) or Martin et al., 2016 (doi: 10.1093/cercor/bhv031). 

Connections between Purkinje cells and interneurons could also influence the behavior results found.

This comment is repeated below in a more general form (Reviewer 1, second to last comment)—please see our response there and lines 270-309 of the revised manuscript for a discussion of how concerns about “off-target” effects are mitigated by the high degree of specificity of the learning deficits and effects of pre-training for the specific learning tasks in which LTD has been previously implicated, and the very similar findings in two different lines of mice with enhanced LTD.

While males and females were both used for the current study, only 7 of each sex were analyzed, which could be underpowered. While it might be justified to combine sexes for this particular study, it would be worth understanding this model in more detail.

We performed additional analyses to address the question of whether there might be sex differences that were not detected because of the sample size.

(1) In a new figure, Fig. 1-figure supplement 1, we break out the results for male and female mice in separate plots, and show that all of the effects of both the KO of Fmr1 from the Purkinje cells and of pretreatment with diazepam that are observed in the full cohort are also statistically significant in just the subset of male mice, and just the subset of female mice (see Fig. 1-figure supplement 1 legend for statistics). In other words, qualitatively, there are no sex differences, and all of the conclusions of our manuscript are statistically valid in both male and female mice. This strengthens the justification for combining sexes for the specific scientific purposes of our study.  

(2) We performed a power analysis to determine how many mice would be needed to determine whether the very, very small quantitative differences between male and female mice are significant. The analysis indicates that this would require upwards of 70 mice of each sex for WT mice (Cohen’s d, 0.6162; power

0.95) and upwards of 2500 mice of each sex for L7-Fmr1 KO mice (Cohen’s d, 0.0989; power 0.95). Since the very small quantitative sex differences observed in our cohorts would not alter our scientific conclusions or the possibility for clinical application to patients of both sexes, even if the small quantitative differences turned out to be significant, the very large number of animals needed did not seem warranted for the current scientific purposes. Researchers focused on sex differences may find a motivation to pursue this issue further.   

Training was only shown up to 30 minutes and learning did not seem to plateau in most cases. What would happen if training continued beyond the 30 minutes? Would L7-Fmr1 KO mice catch-up to WT littermates? Nguyen-Vu

(1) For VOR learning, we used a 30 min training time because in our past (e.g., Boyden et al., 2003; Kimpo and Raymond, 2007; Nguyen-Vu et al., 2013; Nguyen-Vu et al., 2017) and current results, we find that VOR learning does plateau quite rapidly, with little or no additional adaptive change in the VOR observed between the tests of learning after 30 min vs 20 min of VOR-increase training, in WT or L7Fmr1 KO mice (Fig. 1A; WT, p=0.917; L7-Fmr1 KO, p=0.861; 20 vs. 30 min; Tukey). In the L7-Fmr1 KO mice, there is no significant high-frequency VOR-increase learning after 30 min training, and the mean VOR gain is even slightly lower on average (not significant) than before training (Fig. 1A, red). Therefore, we have no reason to expect that the L7-Fmr1 KO mice would catch up to WT after additional VOR-increase training.  

(2) We have added new data on OKR adaptation, induced with 60 min of training (Fig. 5). The L7-Fmr1 KO mice exhibited impaired OKR adaptation, even with 60 min of training (p= 1.27x10-4, Tukey). In our experience, restraint for longer than 60 min produces a behavioral state that is not conducive to learning, as also reported by (Katoh and Yamagiwa, 2018), therefore longer training times were not attempted. 

The pathway discussed as the main focus for VOR in this learning paradigm was connections between parallel fibers (PF) and Purkinje cells, but the possibility of other local or downstream circuitry being involved was not discussed. PF-Purkinje cell circuits were not directly analyzed, which makes this claim difficult to assess.

In the revised manuscript (lines 299-309), we have expanded our discussion of the possibility that loss of expression of Fmr1 from Purkinje cells in the Purkinje cell-specific L7-Fmr1 KO mice might influence other synapses or intrinsic properties of the Purkinje cells (including synapses from interneurons, as raised in this reviewer’s comment above), in addition to enhancing associative LTD at the parallel fiberPurkinje cell synapses. 

It is a very general limitation of all perturbation studies, even cell-type specific perturbation studies as in the current case, that it is never possible to completely rule out “off-target” effects of the manipulation. Because of this, causality cannot be definitively concluded from correlations (e.g., between the effects of a perturbation observed at the cellular and behavioral level), and therefore we make no such claim in our manuscript. Rather, we conclude that our results “provide evidence for,” “support,” “predict,” or “are consistent with” the hypothesis of a history- and activity-dependent change in the threshold for associative LTD at the parallel fiber-Purkinje cells.

That said, perturbation is still one of the major tools in the experimental toolbox, and there are approaches for mitigating concern about off-target effects. We highlight three aspects of our experimental design that accomplish this (lines 184-228, 256-309). First, we show nearly identical learning impairments and effects of behavioral pretreatment in lines of mice with two completely different molecular manipulations that have the common effect of enhancing PF-Purkinje cell LTD, but are likely to have different off-target cellular effects on the Purkinje cells and their synapses. Second, we show that the learning impairments were highly specific to oculomotor learning tasks in which PF-Purkinje cell LTD was previously implicated, with no such effects on three other oculomotor learning tasks that depend on the same region of the cerebellum and oculomotor circuitry. In the original submission, we provided data for one LTDdependent oculomotor learning task, high-frequency VOR-increase learning; in the revised manuscript we provide new data for a second LTD-dependent oculomotor learning task, optokinetic reflex adaptation, with nearly identical results (Fig. 5). Third, we show that the effects of diazepam pre-treatment were highly specific to the same two LTD-dependent oculomotor learning tasks and also highly specific to the L7-Fmr1 KO mice with enhanced LTD and not WT mice. These three features of the experimental design are not common in studies of learning, especially in combination. On lines 256-309, we provide an expanded discussion of how together, these three features of the design strengthen the evidence that the learning impairments and effects of diazepam pre-treatment on learning are related to LTD at the PF-Pk synapses, while acknowledging the possibility of other effects on the circuit. 

The authors mostly achieved their aim and the results support their conclusion and proposed hypothesis. This work will be impactful on the field as it uses a new Purkinje-cell specific mouse model to study a classic cerebellar task. The use of diazepam could be further analyzed in other genetic models of neurodevelopmental disorders to understand if effects on LTD can rescue other pathways and behavior outcomes.

We agree that the present findings are potentially relevant for a very wide array of behavioral tasks, disease models, and brain areas beyond the specific ones in our study, and we make this point on lines 310-338 of the revised manuscript. 

Reviewer #2 (Public Review):

This manuscript explores the seemingly paradoxical observation that enhanced synaptic plasticity impairs (rather than enhances) certain forms of learning and memory. The central hypothesis is that such impairments arise due to saturation of synaptic plasticity, such that the synaptic plasticity required for learning can no longer be induced. A prior study provided evidence for this hypothesis using transgenic mice that lack major histocompatibility class 1 molecules and show enhanced long-term depression (LTD) at synapses between granule cells and Purkinje cells of the cerebellum. The study found that a form of LTD-dependent motor learning-increasing the gain of the vestibulo-ocular reflex (VOR)-is impaired in these mice and can be rescued by manipulations designed to "unsaturate" LTD. The present study extends this line of investigation to another transgenic mouse line with enhanced LTD, namely, mice with the Fragile X gene knocked out. The main findings are that VOR gain increased learning is selectively impaired in these mice but can be rescued by specific manipulations of visuomotor experience known to reverse cerebellar LTD. Additionally, the authors show that a transient global enhancement of neuronal inhibition also selectively rescues gain increases learning. This latter finding has potential clinical relevance since the drug used to boost inhibition, diazepam, is FDA-approved and commonly used in the clinic. The evidence provided for the saturation is somewhat indirect because directly measuring synaptic strength in vivo is technically difficult. Nevertheless, the experimental results are solid. In particular, the specificity of the effects to forms of plasticity previously shown to require LTD is remarkable. The authors should consider including a brief discussion of some of the important untested assumptions of the saturation hypothesis, including the requirement that cerebellar LTD depends not only on pre- and postsynaptic activity (as is typically assumed) but also on the prior history of synaptic activation.

We thank the reviewer for this exceptionally clear and concise assessment of the findings and strengths of the manuscript.

We agree that one of the most “remarkable” aspects of our findings is the specificity of the effects for oculomotor learning tasks for which there is the strongest previous evidence for a role of PF-Purkinje cell LTD. In the original manuscript, we tested just one LTD-dependent oculomotor learning task, highfrequency VOR increase learning; in the revised manuscript, we strengthen the case for LTD-dependent task specificity by adding new data (Fig. 5) showing the same effects for OKR adaptation, an additional LTD-dependent oculomotor learning task.

The reviewer’s suggestion to include discussion of “untested assumptions”, “including the requirement that cerebellar LTD depends not only on pre- and postsynaptic activity (as is typically assumed) but also on the prior history of synaptic activation” prompted us to more deeply consider the broader implications of our results, and extensively revise the Discussion accordingly. We clarify that we consider historydependent changes in the threshold for LTD to be a prediction of the behavioral and pharmacological findings (lines 339-347, 356) rather than an assumption. In addition, we highlight the broader implications of the results by putting them in the context of work in other brain areas on historydependent changes in the threshold for plasticity, i.e., metaplasticity, going back to the seminal Bienenstock-Cooper-Munro (BCM; year) theory (lines 348-378).  

Reviewer #1 (Recommendations for The Authors):

The text and figures are very clear to read, but there are a couple of questions that remain:

The concentrations chosen for diazepam are not well described and it is unclear why the concentrations jump from 2.5 mg/kg to 0.5 mg/kg. Please add an explanation for these concentrations and if any additional behavior outcomes were observed.

Our choice of diazepam concentrations was guided by the concentrations reported in the literature to be effective in mice, which suggest that a higher dose (2 mg/kg) can have additional effects not observed with a lower effective dose (0.5 mg/kg) (Pádua-Reis et al, 2021). Since we did not know how much enhancement of inhibition/suppression of activity might be necessary to substantially reduce the induction of PF-Purkinje cell LTD, we did pilot experiments to test concentrations at the low and high ends of the doses typically used in mice. These pilot experiments revealed that a lower dose of 0.4 or 0.5 mg/kg was comparable to the higher dose of 2.5 mg/kg in suppressing VOR-increase learning 2 hours after administration (Fig. 3 – figure supplement 2). Anecdotally, we observed higher levels of locomotor activity and other abnormal cage behavior during the period immediately after administration of the higher compared to the lower dose. To limit these side effects and any possibility of dependence, we used only the lower dose in all subsequent experiments. We clarify this rationale for using a lower dose in the legend of Fig. 3 – figure supplement 2.   

Figure 4 describes low-frequency VOR, but the paragraph discussing these results (line 191) mentions high-frequency VOR-increase learning. It is unclear where the results are for the high-frequency data. Please include or rephrase for clearer understanding.

In the revised manuscript, we clarify that the 1 Hz vestibular and visual stimuli used in Figs. 1-3 is the

“high” frequency, which yields different results than the “low” frequency of 0.5 Hz (Fig. 4), as also observed in Boyden et al 2006, and Nguyen-Vu et al, 2017. 

Reviewer #2 (Recommendations For The Authors):

The authors should consider including a brief discussion of some of the important untested assumptions of the saturation hypothesis, including the requirement that cerebellar LTD depends not only on pre- and postsynaptic activity (as is typically assumed) but also on the prior history of synaptic activation.

We thank the reviewer for this comment, which, along with your public comments, inspired us to thoroughly reconsider and revise our Discussion. We think this has greatly improved the manuscript, and will substantially increase its appeal to a broad segment of the neuroscience research community, including computational neuroscientists as well as those interested in synaptic physiology, learning and memory, or plasticity-related brain disorders including autism. 

Note that we consider the idea that ”LTD depends not only on pre- and post- synaptic activity but also on the prior history of synaptic activation” to be the central prediction of the threshold metaplasticity hypothesis rather than an assumption, and in the revised manuscript we explicitly refer to this as a prediction (line 339, 356).  We also added a discussion of multiple known cellular phenomena in the Purkinje cells and their synapses that can regulate LTD and thus represent candidate mechanisms for LTD threshold metaplasticity (lines 339-347). Again, sincere thanks for prompting us to write a vastly improved Discussion section.

Editor's note:

Should you choose to revise your manuscript, please include full statistical reporting including exact pvalues wherever possible alongside the summary statistics (test statistic and df) and 95% confidence intervals. These should be reported in the main text for all key questions and not only when the p-value is less than 0.05.

We have added exact p-values throughout the manuscript.  

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eLife assessment

This study conducted fMRI experiments in an inbred rat model of absence seizures. The results provide new information suggesting reduced brain responsiveness during this type of seizure. The reviewers had divergent opinions but on average thought the study was valuable and the conclusions were solid.

Reviewer #1 (Public Review):

In this paper, the effects of two sensory stimuli (visual and somatosensory) on fMRI responsiveness during absence seizures were investigated in GEARS rats with concurrent EEG recordings. SPM analysis of fMRI showed a significant reduction in whole-brain responsiveness during the ictal period compared to the interictal period under both stimuli, and this phenomenon was replicated in a structurally constrained whole-brain computational model of rat brains.

The conclusion of this paper is that whole-brain responsiveness to both sensory stimuli is inhibited and spatially impeded during seizures.

The authors have revised this paper with a lot of detail.

Reviewer #2 (Public Review):

Summary:

This study examined the possible effect of spike-wave discharges (SWDs) on the response to visual or somatosensory stimulation using fMRI and EEG. This is a significant topic because SWDs often are called seizures and because there is non-responsiveness at this time, it would be logical that responses to sensory stimulation are reduced. On the other hand, in rodents with SWDs, sensory stimulation (a noise, for example) often terminates the SWD/seizure.

In humans, these periods of SWDs are due to thalamocortical oscillations. A certain percentage of the normal population can have SWDs in response to photic stimulation at specific frequencies. Other individuals develop SWDs without stimulation. They disrupt consciousness. Individuals have an absent look, or "absence", which is called absence epilepsy.

The authors use a rat model to study the responses to stimulation of the visual or somatosensory systems during and in between SWDs. They report that the response to stimulation is reduced during the SWDs. While some data show this nicely, there is also difficulty knowing the effect of the stimulus, SWD and stimulus + SWD.

The authors also study the hemodynamic response function (HRF) and it is not clear what conclusions can be made from the data. The authors acknowledge this, but it does lessen its significance.

Finally, the authors use a model to analyze the data. This model is novel and while that is a strength, its validation is with a second model rather than empirical data.

Strengths:

Use of fMRI and EEG to study SWDs in rats.

Weaknesses:

The paper has been improved by revisions but there are still parts that are unclear, as described below.

Reviewer #3 (Public Review):

Summary:

This is an interesting paper investigating fMRI changes during sensory (visual, tactile) stimulation and absence seizures in the GAERS model. The results are potentially important for the field and do suggest that sensory stimulation may not activate brain regions normally during absence seizures. However the findings are limited by substantial methodological issues that do not enable fMRI signals related to absence seizures to be fully disentangled from fMRI signals related to the sensory stimuli.

Strengths:

Investigating fMRI brain responses to sensory stimuli during absence seizures in an animal model is a novel approach with potential to yield important insights.

Use of an awake, habituated model is a valid and potentially powerful approach.

The major difficulty with interpreting the results of this study is that the duration of the visual and tactile stimuli were 6 seconds, which is very close to the mean seizure duration per Table 1. Therefore the HRF model looking at fMRI responses to visual or auditory stimuli occurring during seizures was simultaneously weighting both seizure activity and the sensory (visual or auditory) stimuli over the same time intervals on average. The resulting maps and time courses claiming to show fMRI changes from visual or auditory stimulation during seizures will therefore in reality contain some mix of both sensory stimulation-related signals and seizure-related signals. The main claim that the sensory stimuli do not elicit the same activations during seizures as they do in the interictal period may still be true. However the attempts to localize these differences in space or time will be contaminated by the seizure related signals.

In their repeated responses to this comment the authors have stated that some seizures had longer than average duration, and that they have attempted to model the effects of both seizures and sensory stimulation. However these factors do not mitigate the concern because the mean duration of seizures and sensory stimulation remain nearly identical, and the models used therefore will not be able to effectively separate signals related to seizures and related to sensory stimulation. Hemodynamic models can never in reality represent underlying signals in an orthogonal manner, and are only indirectly related to neural activity.

The only way to truly address the important weakness of this study would be to repeat the experiments using stimulus durations that do not match mean seizure duration, e.g. with much shorter duration stimuli.

The authors have clarified and improved the figure images and their description in the text based on previous specific comments. However, the main weakness in the results remains as summarized above.

Minor comments:

Aside from the concerns listed as weaknesses above which were not addressed, most of the more minor comments were addressed by the authors in the resubmissions. However, the comment made twice previously regarding Figure 6-figure supplement 1 was not addressed. It remains impossible to see any firing rate changes elicited by sensory stimuli during the ictal period in parts E and F of the figure vs. parts B and C (interictal), due to the very different scales used. The seizure signals should be removed or accounted for by the model so that any possible sensory stimulus-related signals could be seen, and/or displayed on the same scale as firing rates without seizures. The authors have simply restated their opinion that it is better to include the SWD dynamics in these figures parts, however this makes the figure wholly unconvincing. It is also concerning that part D (ictal), which is in fact shown on the same scale as part A (interictal), actually shows larger firing rates for both excitatory and inhibitory neurons in visual cortex for sensory stimulation during seizures. This contradicts the claims in the rest of the paper that neural activity and fMRI signals are smaller or are even decreased in visual cortex with sensory stimulation during seizures compared to the interictal period.

Author response:

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

eLife assessment

This valuable work performed fMRI experiments in a rodent model of absence seizures. The results provide new information regarding the brain's responsiveness to environmental stimuli during absence seizures. The authors suggest reduced responsiveness occurs during this type of seizure, and the evidence leading to the conclusion is solid, although reviewers had divergent opinions.

Public Reviews:

Reviewer #1 (Public Review):

In this paper, the effects of two sensory stimuli (visual and somatosensory) on fMRI responsiveness during absence seizures were investigated in GEARS rats with concurrent EEG recordings. SPM analysis of fMRI showed a significant reduction in whole-brain responsiveness during the ictal period compared to the interictal period under both stimuli, and this phenomenon was replicated in a structurally constrained whole-brain computational model of rat brains.

The conclusion of this paper is that whole-brain responsiveness to both sensory stimuli is inhibited and spatially impeded during seizures.

Reviewer #2 (Public Review):

Summary:

This study examined the possible affect of spike-wave discharges (SWDs) on the response to visual or somatosensory stimulation using fMRI and EEG. This is a significant topic because SWDs often are called seizures and because there is non-responsiveness at this time, it would be logical that responses to sensory stimulation are reduced. On the other hand, in rodents with SWDs, sensory stimulation (a noise, for example) often terminates the SWD/seizure.

In humans, these periods of SWDs are due to thalamocortical oscillations. A certain percentage of the normal population can have SWDs in response to photic stimulation at specific frequencies. Other individuals develop SWDs without stimulation. They disrupt consciousness. Individuals have an absent look, or "absence", which is called absence epilepsy.

The authors use a rat model to study the responses to stimulation of the visual or somatosensory systems during and in between SWDs. They report that the response to stimulation is reduced during the SWDs. While some data show this nicely, the authors also report on lines 396-8 "When comparing statistical responses between both states, significant changes (p<0.05, cluster-) were noticed in somatosensory auditory frontal..., with these regions being less activated in interictal state (see also Figure 4). That statement is at odds with their conclusion. I do not see that this issue was addressed.

See comments below starting with “We acknowledge the reviewer…”.

They also conclude that stimulation slows the pathways activated by the stimulus. I do not see any data proving this. It would require repeated assessments of the pathways in time. This issue was not addressed.

See comments below starting with “We acknowledge the reviewer…”.

The authors also study the hemodynamic response function (HRF) and it is not clear what conclusions can be made from the data. This is still an issue. No conclusions appear to be possible to make.

See comments below starting with “We acknowledge the reviewer…”.

Finally, the authors use a model to analyze the data. This model is novel and while that is a strength, its validation is unclear. The authors did not add any validation of their model.

See comments below starting with “We acknowledge the reviewer…”.

Strengths:

Use of fMRI and EEG to study SWDs in rats.

Weaknesses:

Several aspects of the Methods and Results were improved but some are still are unclear.

We acknowledge the reviewer for the concerns of we not addressing the comments above. However, we emphasize that most of the comments were addressed in the already sent “Response to Review Comments” and in the updated manuscript. Here we repeat the responses and provide also additional clarifications to some of the comments.

We thank the reviewer for noting the discrepancy in the statement of “less activated in interictal state”. The statement should have been written vice versa. We also address that the direction of activation change between groups can be misinterpreted based on statistical maps itself (Figure 3) where only statistical changes are visible and not the polarity of response (can be seen in Figure 4). Therefore, we have made a following changes in the section 3.3.: “There were more voxels with significant changes of activity during interictal state compared to ictal state (136% more). Comparing the statistical responses between interictal and ictal states revealed significant changes (p<0.05, cluster-level corrected) in the visual, somatosensory, and medial frontal cortices. In the ictal state, these regions showed significant hemodynamic decreases when comparing to interictal state, and these polarity changes can be seen the hemodynamic response functions (Figure 4).”

We agree with the reviewer that there are no data showing slowing of the pathways in response to stimulus. However, we are a bit confused about this comment, as to what part in conclusion section it refers to. We did not intentionally claim that stimulation slows the activated pathways in the manuscript.

Reviewer is right that strong claims cannot be made from HRF by itself. Therefore, we have avoided to such phrasing throughout the manuscript. In the conclusion section, we speculate that HRF decreases “could play a role in decreased sensory perception” but also state that “further studies are required”. The observed HRF decreases (rather than increases) in the cortex when stimulation was applied during SWD, was discussed in section 4.4., where we speculated that neuronal suppression (possible apparent in negative HRFs) caused by SWD can prevent responsiveness. Conclusion now states the following: “Moreover, the detected decreases in the cortical HRF when sensory stimulation was applied during spike-and-wave discharges, could play a role in decreased sensory perception. Further studies are required to evaluate whether this HRF change is a cause or a consequence of the reduced neuronal response.”

We point out that the main validation of the model and its details were provided in the previous answer to the reviewer and added to the manuscript. The model presented in the paper is based on a mean-field formalism that captures neuronal activity at the mesoscale level. This mean-field formalism is derived via a detailed statistical description of the activity of a spiking neuronal population of excitatory and inhibitory with conductance-based synaptic interactions. Thus, the validation of the mean-field model is performed via direct comparison between the dynamics obtained from the mean-field model and the dynamics obtained from the underlying spiking neural network model. This comparison is shown in the supplementary material of the manuscript, where the transition studied in the paper between interictal (asynchronous irregular activity) and ictal (SWD dynamics) activity, which is predicted by the mean-field model, is indeed observed in the underlying spiking neuronal model. The existence of these two types of dynamics and the transition between them is the main component of the model used to build the analysis of the responsiveness performed in the paper (which has been properly validated).

Reviewer #3 (Public Review):

Summary:

This is an interesting paper investigating fMRI changes during sensory (visual, tactile) stimulation and absence seizures in the GAERS model. The results are potentially important for the field and do suggest that sensory stimulation may not activate brain regions normally during absence seizures. But the findings are limited by substantial methodological issues that do not enable fMRI signals related to absence seizures to be fully disentangled from fMRI signals related to the sensory stimuli.

Strengths:

Investigating fMRI brain responses to sensory stimuli during absence seizures in an animal model is a novel approach with potential to yield important insights.

Use of an awake, habituated model is a valid and potentially powerful approach.

Weaknesses:

The major difficulty with interpreting the results of this study is that the duration of the visual and tactile stimuli were 6 seconds, which is very close to the mean seizure duration per Table 1. Therefore the HRF model looking at fMRI responses to visual or auditory stimuli occurring during seizures was simultaneously weighting both seizure activity and the sensory (visual or auditory) stimuli over the same time intervals on average. The resulting maps and time courses claiming to show fMRI changes from visual or auditory stimulation during seizures will therefore in reality contain some mix of both sensory stimulation-related signals and seizure-related signals. The main claim that the sensory stimuli do not elicit the same activations during seizures as they do in the interictal period may still be true. But the attempts to localize these differences in space or time will be contaminated by the seizure related signals.

In their response to this comment the authors state that some seizures had longer than average duration, and that they attempted to model the effects of both seizures and sensory stimulation. However these factors do not mitigate the concern because the mean duration of seizures and sensory stimulation remain nearly identical, and the models used therefore will not be able to effectively separate signals related to seizures and related to sensory stimulation.

Regressors for seizures were formed by including periods of seizures without any stimulation present. In theory, if seizures were perfectly modeled by the regressor, the left variance is completely orthogonal to the main effect of the stimulus. Furthermore, only the cases where the seizures are longer than the stimulus are used to calculate the responsiveness of the stimulus (while the cases where the seizures are shorter than the stimulus are used as nuisance regressors to account for error variance). However, we agree with the reviewer that in practice all effects of the seizure cannot be removed completely from the effect of stimulus. We have addressed this concern in the “physiologic and methodology consideration” section: “We note a caution that presented maps and time courses showing fMRI changes from visual or whisker stimulation during seizures may contain a mixture of both sensory stimulation-related signals and seizure-related signals. To minimize this contamination in the linear model used, we considered both stimulation and seizure-only states as regressors of interest and used seizure-only responses as nuisance regressors to account for error variance. Thereby, the effects caused by the stimulation should be separated as much as possible from the effects caused by the seizure itself.”

The claims that differences were observed for example between visual cortex and superior colliculus signals with visual stim during seizures vs interictal remain unconvincing due to above.

Maps shown in Figure 3 do not show clear changes in the areas claimed to be involved.

In their response the authors enlarged the cross sections. However there are still discrepancies between the images and the way they are described in the text. For example, in the Results text the authors say that comparing the interictal and ictal states revealed less activation in the somatosensory cortex during the ictal than during the interictal state, yet Figure 3 bottom row left shows greater activation in somatosensory cortex in this contrast.

We note that the direction of activation change between groups can be misinterpreted based on statistical maps itself (Figure 3) where only statistical changes are visible and not the polarity of response (can be seen in Figure 4). Therefore, we have made the following changes to the section 3.3.: “There were more voxels with significant changes of activity during interictal state compared to ictal state (136% more). Comparing the statistical responses between interictal and ictal states revealed significant changes (p<0.05, cluster-level corrected) in the visual, somatosensory, and medial frontal cortices. In the ictal state, these regions showed significant hemodynamic decreases when comparing to interictal state, and these polarity changes can be seen the hemodynamic response functions (Figure 4).”

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Authors have revised this paper with a lot of detail. The paper can be accepted for publication in this version.

Reviewer #2 (Recommendations For The Authors):

Reviewer #1

(1) The analysis in this paper does not directly answer the scientific question posed by the authors, which is to explore the mechanisms of the reduced brain responsiveness to external stimuli during absence seizures (in terms of altered information processing), but merely characterizes the spatial involvement of such reduced responsiveness. The same holds for the use of mean-field modeling, which merely reproduces experimental results without explaining them mechanistically as what the authors have claimed at the head of the paper.

We agree with the reviewer that the manuscript does not answer specifically about the mechanisms of reduced brain responsiveness. The main scientific question addressed in the manuscript was to compare whole-brain responsiveness of stimulus between ictal and interictal states. The sentence that can lead to misinterpretations in the manuscript abstract: "The mechanism underlying the reduced responsiveness to external stimulus remains unknown." was therefore modified to the following "The whole-brain spatial and temporal characteristics of reduced responsiveness to external stimulus remains unknown".

This change did not address the issue. The problem is that there is no experimentation to address the underlying mechanisms of the results. I also think the changed language in the abstract is less clear than the original.

We fully agree that this manuscript does not answer or claim to be answering about the mechanisms of reduced brain responsiveness. The main scientific question addressed in the manuscript was to compare whole-brain responsiveness of stimulus between ictal and interictal states, by means of hemodynamics and mean-field simulation.

We have changed the language of the abstract to the following:

“In patients suffering absence epilepsy, recurring seizures can significantly decrease their quality of life and lead to yet untreatable comorbidities. Absence seizures are characterized by spike-and-wave discharges on the electroencephalogram associated with a transient alteration of consciousness. However, it is still unknown how the brain responds to external stimuli during and outside of seizures.

This study aimed to investigate responsiveness to visual and somatosensory stimulation in GAERS, a well-established rat model for absence epilepsy. Animals were maintained in a non-curarized awake state allowing for naturally occurring seizures to be produced inside the magnet. They were imaged continuously using a quiet zero-echo-time functional magnetic resonance imaging (fMRI) sequence. Sensory stimulations were applied during interictal and ictal periods. Whole brain responsiveness and hemodynamic responses were compared between these two states. Additionally, a mean-field simulation model was used to mechanistically explain the changes of neural responsiveness to visual stimulation between interictal and ictal states.

Results showed that, during a seizure, whole-brain responses to both sensory stimulations were suppressed and spatially hindered. In several cortical regions, hemodynamic responses were negatively polarized during seizures, despite the application of a stimulus. The simulation experiments also showed restricted propagation of spontaneous activity due to stimulation and so agreed well with fMRI findings. These results suggest that sensory processing observed during an interictal state is hindered or even suppressed by the occurrence of an absence seizure, potentially contributing to decreased responsiveness during this absence epileptic process.”

The authors also study the hemodynamic response function (HRF) and it is not clear what conclusions can be made from the data.

The response of the authors did not clarify this issue. Instead, they explained why they examined HRF and that they can only speculate what the data means.

Reviewer is right that strong claims cannot be made from HRF by itself. Therefore, we have avoided to such phrasing throughout the manuscript. In the conclusion section, we speculate that HRF decreases “could play a role in decreased sensory perception” but also state that “further studies are required”.

Finally, the authors use a model to analyze the data. This model is novel and while that is a strength, its validation is unclear. The conclusion is that the modeling supports the conclusions of the study, which is useful.

Details about the model were added.

This is not entirely satisfactory because there is still no validation of the model.

We point out that the main validation of the model and its details were provided in the previous answer to the reviewer and added to the manuscript. The model presented in the paper is based on a mean-field formalism that captures neuronal activity at the mesoscale level. This mean-field formalism is derived via a detailed statistical description of the activity of a spiking neuronal population of excitatory and inhibitory with conductance-based synaptic interactions. Thus, the validation of the mean-field model is performed via direct comparison between the dynamics obtained from the mean-field model and the dynamics obtained from the underlying spiking neural network model. This comparison is shown in the supplementary material of the manuscript, where the transition studied in the paper between interictal (asynchronous irregular activity) and ictal (SWD dynamics) activity, which is predicted by the mean-field model, is indeed observed in the underlying spiking neuronal model. The existence of these two types of dynamics and the transition between them is the main component of the model used to build the analysis of the responsiveness performed in the paper (which has been properly validated).

How is ROI defined in this paper? What type of atlas is used?

Anatomical ROIs were drawn based on Paxinos and Watson rat brain atlas 7th edition. Region was selected if there were statistically significant activations detected inside that region, based on activation maps. We clarified the definition of ROI as the following:<br /> "Anatomical ROIs, based on Paxinos atlas (Paxinos and Watson rat brain atlas 7th edition), were drawn on the brain areas where statistical differences were seen in activation maps."

This is helpful, but the unstained brain does not show the borders of the areas. Therefore just saying an atlas was used is not enough. How in an unstained brain can the areas be accurately outlined?

Areas of the brain were differentiated by co-registering the functional MRI images with an T1-weighted anatomical reference brain that was created on site from the same data set that was used for the manuscript. Potential co-registration inaccuracies created by using a reference brain measured in different site, sequence and a rat strain can be thus avoided. T1-images create sufficient contrast to differentiate main brain areas, but for more accurate border definition (e.g., to differentiate different thalamic nuclei), a coordinate system of the atlas and coordinates known in the used anatomical brain, were used to pinpoint exact borders of the brain areas.

Reviewer #2

The following also is not precise:

"Although seizures are initially triggered by hyperactive somatosensory cortical neurons, the majority of neuronal populations are deactivated rather than activated during the seizure, resulting in an overall decrease in neuronal activity during SWD (McCafferty et al. 2023)."

What neuronal populations? Cortex? Which neurons in the cortex? Those projecting to the thalamus? What about thalamocortical relay cells? Thalamic gabaergic neurons?

Please check that these issues were corrected.

The issues were addressed as follows:

“Although SWDs are initially triggered by hyperactive somatosensory cortical neurons, neuronal firing rates, especially in majority of frontoparietal cortical and thalamocortical relay neurons, are decreased rather than increased during SWD, resulting in an overall decrease in activity in these neuronal populations (McCafferty et al., 2023). Previous fMRI studies have demonstrated blood volume or BOLD signal decreases in several cortical regions including parietal and occipital cortex, but also, quite surprisingly, increases in subcortical regions such as thalamus, medulla and pons (David et al., 2008; McCafferty et al., 2023).”

Results

After removing problematic animals and sessions, was there sufficient power? There probably wasn't enough to determine sex differences.

After removing problematic sessions, we found statistically significant results (multiple comparison corrected) results in both activation maps, and hemodynamic responses. To determine sex differences, there were not enough animals for statistical findings (p>0.05).

This is not the question. The question is whether there was sufficient power.

A simple power calculation was performed as follows: considering a t-test, a risk alpha of 0.05, a power of 0.8, matched pairs (seizure/control), we can detect an effect size of 0.37 with our 4 animals, considering repeated measurements (4 sessions/animal x 11 seizure/control pairs per session). This is now mentioned in the manuscript.

Table 1 has no statistical comparisons.

Table 1 is purely an illustration of stimulation and seizure occurrence. There is no specific interest to compare stimulation types (in what state of seizure it occurred) as it does not provide any meaningful inferences to the study.

Table 1 could be improved by statistics. More could be said and there would be justification to include it.

We thank the reviewer for the suggestion, but as it is yet unclear to what statistical comparison would be feasible to do, we opt to leave it out.

Statistical activation maps - it is not clear how this was done.

Creation of statistical maps are explained in section 2.5.3.

This section is not clear.

We have added a reference (https://doi.org/10.1002/hbm.460020402) for readers to familiarize themselves with the concept of statistical parametric mapping.

Fig 3 "F-contrast maps." Please explain.

Creation of statistical maps are explained in section 2.5.3.

This section is unclear.

We have added a reference (https://doi.org/10.1002/hbm.460020402) for readers to familiarize themself with the concept of statistical parametric mapping.

Reviewer #3 (Recommendations For The Authors):

Aside from the concerns listed as weaknesses above which were not addressed, most of the more minor comments were addressed by the authors in the resubmission. However, the comment below was not addressed because it is impossible to see any firing rate changes elicited by sensory stimuli (if they are present) due to the scale during seizures. The seizure signals should be removed or accounted for by the model so that any possible sensory stimulus-related signals could be seen, and displayed on the same scale as firing rates without seizures. Prior comment (unaddressed) is repeated below:

Figure 6-figure supplement 1, the scales are very different for many of the plots so they are hard to compare. Especially in the ictal periods (D, E, F) it is hard to see if any changes are happening during ictal stimulation similar to interictal stimulation due to very different scales. The activity related to SWD is so large that it overshadows the rest, and perhaps should be subtracted out.

These two comments were addressed and replied in the previous round of reviews. Regarding the different scales of the plots from Figure 6-figure supplement 1, we point out that all the plots in the same scale are already presented in Figure 6 of the main-text. Regarding the activity related to SWD and sensory stimulation, we remark that the effect of the stimulation should be (and was) evaluated with respect to the ongoing activity. All the results concerning the neuronal responsiveness presented in the paper evaluate the statistical significance of the changes in activity produced by the stimulation with respect to the ongoing activity (during ictal and interictal states respectively). For this reason, all the plots containing the time series of neuronal activity in the simulations include the ongoing activity (with SWD dynamics when present) for proper comparison and relevant analysis. 

Additional changes:

In the section 3.2., the sentence: “In addition, responses were observed in the somatosensory cortex during a seizure state.” was removed for clarification purposes as deactivation rather than activation was observed in this brain area during a seizure state.

eLife assessment

In this manuscript, the authors tested the hypothesis that Aβ42 toxicity arises from its proven affinity for γ-secretases. The authors provide useful findings, showing convincingly that human Abeta42 inhibits gamma-secretase activity. The data will be of interest to all scientists working on neurodegenerative diseases.

Reviewer #1 (Public Review):

Summary:

Human Abeta42 inhibits gamma-secretase activity in biochemical assays.

Strengths:

Determination of inhibitory concentration human Abeta42 on gamma-secretase activity in biochemical assays.

Author response:

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

Reviewer #1 (Recommendations For The Authors):

Major concerns:

(1) It is not clear about the biological significance of the inhibitory effects of human Abeta42 on gammasecretase activity. As the authors mentioned in the Discussion, it is plausible that Abeta42 may concentrate up to microM level in endosomes. However, subsets of FAD mutations in APP and presenilin 1 and 2 increase Abeta42/Abeta40 ratio and lead to Abeta42 deposition in brain. APP knock-in mice NLF and NLGF also develop Abeta42 deposition in age-dependent manner, although they produce more human Abeta42 than human Abeta40. 

If the production of Abeta42 is attenuated, which results in less Abeta42 deposition in brain. So, it is unlikely that human Abeta42 interferes gamma-secretase activity in physiological conditions. This reviewer has an impression that inhibition of gamma-secretase by human Abeta42 is an interesting artifact in high Abeta42 concentration. If the authors disagree with this reviewer's comment, this manuscript needs more discussion in this point of view. 

We thank the Reviewer for raising this key conceptual point, we acknowledge that it was insufficiently discussed in the original manuscript. In response to this point, we introduced the following paragraph in the discussion section of the revised manuscript:

“From a mechanistic standpoint, the competitive nature of the Aβ42-mediated inhibition implies

that it is partial, reversible, and regulated by the relative concentrations of the Aβ42 peptide (inhibitor) and the endogenous substrates (Figure 10C and 10D). The model that we put forward is that cellular uptake, as well as endosomal production of Aβ, result in increased intracellular concentration of Aβ42, facilitating γ-secretase inhibition and leading to the buildup of APP-CTFs (and γ-secretase substrates in general). As Aβ42 levels fall, the augmented concentration of substrates shifts the equilibrium towards their processing and subsequent Aβ production. As Aβ42 levels rise again, the equilibrium is shifted back towards inhibition. This cyclic inhibitory mechanism will translate into pulses of (partial) γsecretase inhibition, which will alter γ-secretase mediated-signaling (arising from increased CTF levels at the membrane or decreased release of soluble intracellular domains from substrates). These alterations may affect the dynamics of systems oscillating in the brain, such as NOTCH signaling, implicated in memory formation, and potentially others (related to e.g. cadherins, p75 or neuregulins). It is worth noting that oscillations in γ-secretase activity induced by treatment with a γ-secretase inhibitor semagacestat have been proposed to have contributed to the cognitive alterations observed in semagacestat treated patients in the failed Phase-3 IDENTITY clinical trial (7) and that semagacestat, like Aβ42, acts as a high affinity competitor of substrates (85).

The convergence of Aβ42 and tau at the synapse has been proposed to underlie synaptic dysfunction in AD (86-89), and recent assessment of APP-CTF levels in synaptosome-enriched fractions from healthy control, SAD and FAD brains (temporal cortices) has shown that APP fragments concentrate at higher levels in the synapse in AD-affected than in control individuals (90).  Our analysis adds that endogenous Aβ42 concentrates in synaptosomes derived from end-stage AD brains to reach ~10 nM, a concentration that in CM from human neurons inhibits γ-secretase in PC12 cells (Figure 7). Furthermore, the restricted localization of Aβ in endolysosomal vesicles, within synaptosomes, likely increases the local peptide concentration to the levels that inhibit γ-secretase-mediated processing of substrates in this compartment. In addition, we argue that the deposition of Aβ42 in plaques may be preceded a critical increase in the levels of Aβ present in endosomes and the cyclical inhibition of γsecretase activity that we propose. Under this view, reductions in γ-secretase activity may be a (transient) downstream consequence of increases in Aβ due to failed clearance, as represented by plaque deposition, contributing to AD pathogenesis.“

We have also added figures 10C and 10D, presented here for convenience.

Author response image 1.

(2) It is not clear whether the FRET-based assay in living cells really reflects gamma-secretase activity.

This reviewer thinks that the authors need at least biochemical data, such as levels of Abeta. 

We have established a novel, HiBiT tag based assay reporting on the global γ-secretase activity in cells, using as a proxy the total levels of secreted HiBiT-tagged Aβ peptides. The assay and findings are presented in the revised manuscript as follows:

In the result section, in the “Aβ42 treatment leads to the accumulation of APP C-terminal fragments in neuronal cell lines and human neuron” subsection:

“The increments in the APP-CTF/FL ratio suggested that Aβ42 (partially) inhibits the global γ-

secretase activity. To further investigate this, we measured the direct products of the γ-secretase mediated proteolysis of APP. Since the detection of the endogenous Aβ products via standard ELISA methods was precluded by the presence of exogenous human Aβ42 (treatment), we used an N-terminally tagged version of APPC99 and quantified the amount of total secreted Aβ, which is a proxy for the global γsecretase activity. Briefly, we overexpressed human APPC99 N-terminally tagged with a short 11 amino acid long HiBiT tag in human embryonic kidney (HEK) cells, treated these cultures with human Aβ42 or p3 17-42 peptides at 1 μM or DAPT (GSI) at 10 µM, and determined total HiBiT-Aβ levels in conditioned media (CM). DAPT was considered to result in full γ-secretase inhibition, and hence the values recorded in DAPT treated conditions were used for the background subtraction. We found a ~50% reduction in luminescence signal, directly linked to HiBiT-Aβ levels, in CM of cells treated with human Aβ42 and no effect of p3 peptide treatment, relative to the DMSO control (Figure 3D). The observed reduction in the total Aβ products is consistent with the partial inhibition of γ -secretase by Aβ42.”

In Methods:

“Analysis of γ-secretase substrate proteolysis in cultured cells using secreted HiBiT-Aβ or -Aβ-like peptide levels as a proxy for the global γ-secretase endopeptidase activity

HEK293 stably expressing APP-CTF (C99) or a NOTCH1-based substrate (similar in size as

APP- C99) both N-terminally tagged with the HiBiT tag were plated at the density of 10000 cells per 96-well, and 24h after plating treated with Aβ or p3 peptides diluted in OPTIMEM (Thermo Fisher Scientific) supplemented with 5% FBS (Gibco). Conditioned media was collected and subjected to analysis using Nano-Glo® HiBiT Extracellular Detection System (Promega). Briefly, 50 µl of the medium was mixed with 50 µl of the reaction mixture containing LgBiT Protein (1:100) and Nano-Glo HiBiT Extracellular Substrate (1:50) in Nano-Glo HiBiT Extracellular Buffer, and the reaction was incubated for 10 minutes at room temperature. Luminescence signal corresponding to the amount of the extracellular HiBiT-Aβ or -Aβ-like peptides was measured using victor plate reader with default luminescence measurement settings.”

As the direct substrate of γ -secretase was used in this analysis, the observed reduction (~50%) in the levels of N-terminally-tagged (HiBiT) Aβ peptides in the presence of 1 µM Aβ42, relative to control conditions, demonstrates a selective inhibition of γ-secretase by Aβ42 (not by the p3). These data complement the FRET-based findings presented in Figure 5.

(3) Processing of APP-CTF in living cells is not only the cleavage by gamma-secretase. This reviewer thinks that the authors need at least biochemical data, such as levels of Abeta in Figures 4, 5 and 7.

We tried to measure the levels of Aβ peptides secreted by cells into the culture medium directly by ELISA (using different protocols) or MS (using established methods, as reported in Koch et al, 2023), but exogenous Aβ42 (treatment) present at relatively high levels interfered with the readout and rendered the analysis inconclusive. 

However, we were successful in the determination of total secreted (HiBiT-tagged) Aβ peptides from the HiBiT tagged APP-C99 substrate, as indicated in the previous point. The quantification of the levels of these peptides showed that Aβ42 treatment resulted in ~50% reduction in the γ -secretase mediated processing of the tagged substrate.    

In addition, we would like to highlight that our analysis of the contribution of other APP-CTF degradation pathways, using cycloheximide-based assays in the constant presence of γ-secretase inhibitor, failed to reveal significant differences between Aβ42 treated cells and controls (Figure 6B & C). The lack of a significant impact of Aβ42 on the half-life of APP-CTFs under the conditions of γsecretase inhibition maintained by inhibitor treatment is consistent with the proposed Aβ42-mediated inhibitory mechanism.

(4) Similar to comment #3. Processing of Pancad-CTF and p75 in living cells may be not only the cleavage by gamma-secretase. This reviewer thinks that the authors need at least biochemical data, such as levels of ICDs in Figures 6C and E. 

To address this comment we have now performed additional experiments where we measured Nterminal Aβ-like peptides derived from NOTCH1-based substrate using the HiBiT-based assay. These experiments showed a reduction in the aforementioned peptides in the cells treated with Aβ42 relative to the vehicle control, and hence further confirmed the inhibitory action of Aβ42. These new data have been included as Figure 8D in the revised manuscript and described as follow:

Finally, we measured the direct N-terminal products generated by γ-secretase proteolysis from a HiBiT-tagged NOTCH1-based substrate, an estimate of the global γ-secretase activity. We quantified the Aβ-like peptides secreted by HEK 293 cells stably expressing this HiBiT-tagged substrate upon treatment with 1 µM Aβ1-42,  p3 17-42 peptide or  DAPT (GSI) (Figure 8D). DAPT treatment was considered to result in a complete γ-secretase inhibition, and hence the values recorded in the DAPT condition were used for background subtraction. A ~20% significant reduction in the amount of secreted

N-terminal HiBiT-tagged peptides derived from the NOTCH1-based substrates in cells treated with Aβ1-

42 supports the inhibitory action of Aβ1-42 on γ-secretase mediated proteolysis.

Minor concerns:

(1) Murine Abeta42 may be converted to murine Abeta38 easily, compared to human Abeta42. This may be a reason why murine Abeta42 exhibits no inhibitory effect on gamma-secretase activity. 

In order to address this question, we performed additional experiments where we assessed the processing of murine Aβ42 into Aβ38. Analogous to human Aβ42, the murine Aβ42 peptide was not processed to Aβ38 in the assay conditions. These new data have been integrated in the manuscript and added as a Supplementary figure 1B.

(2) It is curious to know the levels of C99 and C83 in cells in supplementary figure 3.  

The conditions used in these assays were analogous to the conditions used in the figure 3 (i.e. treatment with Aβ peptides at 1 µM concentrations). Such conditions were associated with profound and consistent APP-CTF accumulation in this model system.

Reviewer #2 (Recommendations For The Authors):

In the current study, the authors show that Aβs with low affinity for γ-secretase, but when present at relatively high concentrations, can compete with the longer, higher affinity APPC99 substrate for binding and processing. They also performed kinetic analyses and demonstrate that human Aβ1-42 inhibits γ-secretase-mediated processing of APP C99 and other substrates. Interestingly, neither murine Aβ1-42 nor human p3 (17-42 amino acids in Aβ) peptides exerted inhibition under similar conditions. The authors also show that human Aβ1-42-mediated inhibition of γ-secretase activity results in the accumulation of unprocessed, which leads to p75-dependent activation of caspase 3 in basal forebrain cholinergic neurons (BFCNs) and PC12 cells. 

These analyses demonstrate that, as seen for γ-secretase inhibitors, Aβ1-42 potentiates this marker of apoptosis. However, these are no any in vivo data to support the physiological significance of the current finding. The author should show in APP KO mice whether gamma-secretase enzymatic activity is elevated or not, and putting back Aβ42 peptide will abolish these in vivo effects. 

The findings presented in this manuscript form the basis for further in vitro and in vivo research to investigate the mechanisms of inhibition and its contribution to brain pathophysiology. Here, we used well-controlled model systems to investigate a novel mechanism of Aβ42 toxicity. Multiple mechanisms regulate the local concentration of Aβ42 in vivo, making the dissection of the biochemical mechanisms of the inhibition more complex. Nevertheless, beyond the scope of this report, we consider these very reasonable comments as a motivation for further research activities. 

The experimental concentrations for Aβ42 peptide in the assay are too high, which are far beyond the physiological concentrations or pathological levels. The artificial observations are not supported by any in vivo experimental evidence.

It is correct that in the majority of the experiments we used low μM concentrations of Aβ42. However, we would like to note that we have also performed experiments where conditioned medium collected from human APP.Swe expressing neurons was used as a source of Aβ. In these experiments total Aβ concentration was in low nM range (0.5-1 nM) (Figure 7). Treatment with this conditioned medium  led to the increase APP-CTF levels, supporting  that low nM concentrations of Aβ are sufficient for partial inhibition of  γ-secretase. 

In addition, we highlight that analyses of the brains of the AD affected individuals have shown that APPCTFs accumulate in both sporadic and genetic forms of the disease (Pera et al. 2013, Vaillant-Beuchot et al. 2021); and recently, Ferrer-Raventós et al. 2023 have revealed a correlation between APP-CTFs and Aβ levels at the synapse (Ferrer-Raventós et al. 2023). We therefore assessed the concentration of Aβ42 in synaptosomes derived from frontal cortices of post-mortem AD and age-matched non-demented (ND) control individuals. Our findings and conclusions are included in the revised version as follows: 

In the results section:

“We next investigated the levels of Aβ42 in synaptosomes derived from frontal cortices of post-mortem AD and age-matched non-demented (ND) control individuals (Figure 10B). Towards this, we prepared synaptosomes from frozen brain tissues using Percoll gradient procedure (62, 63). Intact synaptosomes were spun to obtain a pellet which was resuspended in minimum amount of PBS, allowing us to estimate the volume containing the resuspended synaptosome sample. This is likely an overestimate of the actual synaptosome volume. Finally, synaptosomes were lysed in RIPA buffer and Aβ peptide concentrations measured using ELISA (MSD). We observed that the concentration of Aβ42 in the synaptosomes from (end-stage) AD tissues was significantly higher (10.7 nM)  than those isolated from non-demented tissues (0.7 nM), p<0.0005***. These data provide evidence for accumulation at nM concentrations of endogenous Aβ42 in synaptosomes in end-stage AD brains. Given that we measured Aβ42 concentration in synaptosomes, we speculate that even higher concentrations of this peptide may be present in the endolysosome vesicle system, and therein inhibit the endogenous processing of APP-CTF at the synapse. Of note treatment of PC12 cells with conditioned medium containing even lower amounts of Aβ (low nanomolar range (0.5-1 nM)) resulted in the accumulation of APP-CTFs.” 

In the discussion: 

“The convergence of Aβ42 and tau at the synapse has been proposed to underlie synaptic dysfunction in AD (86-89), and recent assessment of APP-CTF levels in synaptosome-enriched fractions from healthy control, SAD and FAD brains (temporal cortices) has shown that APP fragments concentrate at higher levels in the synapse in AD-affected than in control individuals (90).  Our analysis adds that endogenous Aβ42 concentrates in synaptosomes derived from end-stage AD brains to reach ~10 nM, a concentration that in CM from human neurons inhibits γ-secretase in PC12 cells (Figure 7). Furthermore, the restricted localization of Aβ in endolysosomal vesicles, within synaptosomes, likely increases the local peptide concentration to the levels that inhibit γ-secretase-mediated processing of substrates in this compartment. In addition, we argue that the deposition of Aβ42 in plaques may be preceded by a critical increase in the levels of Aβ present in endosomes and the cyclical inhibition of γ-secretase activity that we propose. Under this view, reductions in γ-secretase activity may be a (transient) downstream consequence of increases in Aβ due to failed clearance, as represented by plaque deposition, contributing to AD pathogenesis. ”

eLife assessment

This important study explores infants' attention patterns in real-world settings using advanced protocols and cutting-edge methods. The presented evidence for the role of EEG theta power in infants' attention is solid. The study will be of interest to researchers working on the development and control of attention.

Reviewer #1 (Public Review):

Summary:

The paper investigates the physiological and neural processes that relate to infants' attention allocation in a naturalistic setting. Contrary to experimental paradigms that are usually employed in developmental research, this study investigates attention processes while letting the infants free to play with three toys in the vicinity of their caregiver, which is closer to a common, everyday life context. The paper focuses on infants at 5 and 10 months of age and finds differences in what predicts attention allocation. At 5 months, attention episodes are shorter and their duration is predicted by autonomic arousal. At 10 months, attention episodes are longer, and their duration can be predicted by theta power. Moreover, theta power predicted the proportion of looking at the toys, as well as a decrease in arousal (heart rate). Overall, the authors conclude that attentional systems change across development, becoming more driven by cortical processes.

Strengths:

I enjoyed reading the paper, I am impressed with the level of detail of the analyses, and I am strongly in favour of the overall approach, which tries to move beyond in-lab settings. The collection of multiple sources of data (EEG, heart rate, looking behaviour) at two different ages (5 and 10 months) is a key strength of this paper. The original analyses, which build onto robust EEG preprocessing, are an additional feat that improves the overall value of the paper. The careful consideration of how theta power might change before, during, and in the prediction of attention episodes is especially remarkable.

Weaknesses:

The levels of EEG noise across age groups and periods of attention allocation are not controlled for. I appreciate the analysis of noise reported in supplementary materials. The analysis focuses on a broad level (average noise in 5-month-olds vs 10-month-olds) but variations might be more fine-grained (for example, noise in 5mos might be due to fussiness and crying, while at 10 months it might be due to increased movements). More importantly, noise might even be the same across age groups, but correlated to other aspects of their behaviour (head or eye movements) that are directly related to the measures of interest. Is it possible that noise might co-vary with some of the behaviours of interest, thus leading to either spurious effects or false negatives? One way to address this issue would be for example to check if noise in the signal can predict attention episodes. If this is the case, noise should be added as a covariate in many of the analyses of this paper.

Concerning cross-correlation analyses, the authors state that "Interpreting the exact time intervals over which a cross-correlation is significant is challenging". Then, they say that asymmetry is enough to conclude that attention forward predicted theta power more than vice versa. I think it could be useful to add a bit more of explanation before reaching this conclusion, explaining why such statement is correct, and how it is supported by previous work in statistics.

Finally, the cognitive process under investigation (e.g., attention) and its operationalization (e.g., duration of consecutive looking toward a toy) are not fully distinguished, but conflated instead (e.g., "attention durations"). This does not impact the quality of the work or analyses, but it slightly reduces clarity.

General Remarks<br /> In general, the authors achieved their aim in that they successfully showed the relationship between looking behaviour (as a proxy of attention), autonomic arousal, and electrophysiology. Two aspects are especially interesting. First, the fact that at 5 months, autonomic arousal predicts the duration of subsequent attention episodes, but at 10 months this effect is not present. Conversely, at 10 months, theta power predicts the duration of looking episodes, but this effect is not present in 5-month-old infants. This pattern of results suggests that younger infants have less control over their attention, which mostly depends on their current state of arousal, but older infants have gained cortical control of their attention, which in turn impacts their looking behaviour and arousal.

Reviewer #2 (Public Review):

Summary:

This manuscript explores infants' attention patterns in real-world settings and their relationship with autonomic arousal and EEG oscillations in the theta frequency band. The study included 5- and 10-month-old infants during free play. The results showed that the 5-month-old group exhibited a decline in HR forward-predicted attentional behaviors, while the 10-month-old group exhibited increased theta power following shifts in gaze, indicating the start of a new attention episode. Additionally, this increase in theta power predicted the duration of infants' looking behavior.

Strengths:

The study's strengths lie in its utilization of advanced protocols and cutting-edge techniques to assess infants' neural activity and autonomic arousal associated with their attention patterns, as well as the extensive data coding and processing. Overall, I think this article's findings have important theoretical implications for the development of infant attention.

Weaknesses:

The authors have effectively tackled the majority of my concerns within their revised manuscript, resulting in a substantial improvement. While the revised paper notably addresses many points, one question regarding the potential contamination of saccades on EEG power remains partially unresolved. However, I appreciate the authors' explanation that resolving this issue was challenging due to the absence of eye-tracking data in the current study. Additionally, I acknowledge their inclusion of this concern in the limitations section.

Author response:

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

eLife assessment

This important study explores infants' attention patterns in real-world settings using advanced protocols and cutting-edge methods. The presented evidence for the role of EEG theta power in infants' attention is currently incomplete. The study will be of interest to researchers working on the development and control of attention.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The paper investigates the physiological and neural processes that relate to infants' attention allocation in a naturalistic setting. Contrary to experimental paradigms that are usually employed in developmental research, this study investigates attention processes while letting the infants be free to play with three toys in the vicinity of their caregiver, which is closer to a common, everyday life context. The paper focuses on infants at 5 and 10 months of age and finds differences in what predicts attention allocation. At 5 months, attention episodes are shorter and their duration is predicted by autonomic arousal. At 10 months, attention episodes are longer, and their duration can be predicted by theta power. Moreover, theta power predicted the proportion of looking at the toys, as well as a decrease in arousal (heart rate). Overall, the authors conclude that attentional systems change across development, becoming more driven by cortical processes.

Strengths:

I enjoyed reading the paper, I am impressed with the level of detail of the analyses, and I am strongly in favour of the overall approach, which tries to move beyond in-lab settings. The collection of multiple sources of data (EEG, heart rate, looking behaviour) at two different ages (5 and 10 months) is a key strength of this paper. The original analyses, which build onto robust EEG preprocessing, are an additional feat that improves the overall value of the paper. The careful consideration of how theta power might change before, during, and in the prediction of attention episodes is especially remarkable. However, I have a few major concerns that I would like the authors to address, especially on the methodological side.

Points of improvement

(1) Noise

The first concern is the level of noise across age groups, periods of attention allocation, and metrics. Starting with EEG, I appreciate the analysis of noise reported in supplementary materials. The analysis focuses on a broad level (average noise in 5-month-olds vs 10-month-olds) but variations might be more fine-grained (for example, noise in 5mos might be due to fussiness and crying, while at 10 months it might be due to increased movements). More importantly, noise might even be the same across age groups, but correlated to other aspects of their behaviour (head or eye movements) that are directly related to the measures of interest. Is it possible that noise might co-vary with some of the behaviours of interest, thus leading to either spurious effects or false negatives? One way to address this issue would be for example to check if noise in the signal can predict attention episodes. If this is the case, noise should be added as a covariate in many of the analyses of this paper. 

We thank the reviewer for this comment. We certainly have evidence that even the most state-of-the-art cleaning procedures (such as machine-learning trained ICA decompositions, as we applied here) are unable to remove eye movement artifact entirely from EEG data (Haresign et al., 2021; Phillips et al., 2023). (This applies to our data but also to others’ where confounding effects of eye movements are generally not considered.) Importantly, however, our analyses have been designed very carefully with this explicit challenge in mind. All of our analyses compare changes in the relationship between brain activity and attention as a function of age, and there is no evidence to suggest that different sources of noise (e.g. crying vs. movement) would associate differently with attention durations nor change their interactions with attention over developmental time. And figures 5 and 7, for example, both look at the relationship of EEG data at one moment in time to a child’s attention patterns hundreds or thousands of milliseconds before and after that moment, for which there is no possibility that head or eye movement artifact can have systematically influenced the results.

Moving onto the video coding, I see that inter-rater reliability was not very high. Is this due to the fine-grained nature of the coding (20ms)? Is it driven by differences in expertise among the two coders? Or because coding this fine-grained behaviour from video data is simply too difficult? The main dependent variable (looking duration) is extracted from the video coding, and I think the authors should be confident they are maximising measurement accuracy.

We appreciate the concern. To calculate IRR we used this function (Cardillo G. (2007) Cohen's kappa: compute the Cohen's kappa ratio on a square matrix. http://www.mathworks.com/matlabcentral/fileexchange/15365). Our “Observed agreement” was 0.7 (std= 0.15). However, we decided to report the Cohen's kappa coefficient, which is generally thought to be a more robust measure as it takes into account the agreement occurring by chance. We conducted the training meticulously (refer to response to Q6, R3), and we have confidence that our coders performed to the best of their abilities.

(2) Cross-correlation analyses

I would like to raise two issues here. The first is the potential problem of using auto-correlated variables as input for cross-correlations. I am not sure whether theta power was significantly autocorrelated. If it is, could it explain the cross-correlation result? The fact that the cross-correlation plots in Figure 6 peak at zero, and are significant (but lower) around zero, makes me think that it could be a consequence of periods around zero being autocorrelated. Relatedly: how does the fact that the significant lag includes zero, and a bit before, affect the interpretation of this effect? 

Just to clarify this analysis, we did include a plot showing autocorrelation of theta activity in the original submission (Figs 7A and 7B in the revised paper). These indicate that theta shows little to no autocorrelation. And we can see no way in which this might have influenced our results. From their comments, the reviewer seems rather to be thinking of phasic changes in the autocorrelation, and whether the possibility that greater stability in theta during the time period around looks might have caused the cross-correlation result shown in 7E. Again though we can see no way in which this might be true, as the cross-correlation indicates that greater theta power is associated with a greater likelihood of looking, and this would not have been affected by changes in the autocorrelation.

A second issue with the cross-correlation analyses is the coding of the looking behaviour. If I understand correctly, if an infant looked for a full second at the same object, they would get a maximum score (e.g., 1) while if they looked at 500ms at the object and 500ms away from the object, they would receive a score of e.g., 0.5. However, if they looked at one object for 500ms and another object for 500ms, they would receive a maximum score (e.g., 1). The reason seems unclear to me because these are different attention episodes, but they would be treated as one. In addition, the authors also show that within an attentional episode theta power changes (for 10mos). What is the reason behind this scoring system? Wouldn't it be better to adjust by the number of attention switches, e.g., with the formula: looking-time/(1+N_switches), so that if infants looked for a full second, but made 1 switch from one object to the other, the score would be .5, thus reflecting that attention was terminated within that episode? 

We appreciate this suggestion. This is something we did not consider, and we thank the reviewer for raising it. In response to their comment, we have now rerun the analyses using the new measure (looking-time/(1+N_switches), and we are reassured to find that the results remain highly consistent. Please see Author response image 1 below where you can see the original results in orange and the new measure in blue at 5 and 10 months.

Author response image 1.

(3) Clearer definitions of variables, constructs, and visualisations

The second issue is the overall clarity and systematicity of the paper. The concept of attention appears with many different names. Only in the abstract, it is described as attention control, attentional behaviours, attentiveness, attention durations, attention shifts and attention episode. More names are used elsewhere in the paper. Although some of them are indeed meant to describe different aspects, others are overlapping. As a consequence, the main results also become more difficult to grasp. For example, it is stated that autonomic arousal predicts attention, but it's harder to understand what specific aspect (duration of looking, disengagement, etc.) it is predictive of. Relatedly, the cognitive process under investigation (e.g., attention) and its operationalization (e.g., duration of consecutive looking toward a toy) are used interchangeably. I would want to see more demarcation between different concepts and between concepts and measurements.

We appreciate the comment and we have clarified the concepts and their operationalisation throughout the revised manuscript.

General Remarks

In general, the authors achieved their aim in that they successfully showed the relationship between looking behaviour (as a proxy of attention), autonomic arousal, and electrophysiology. Two aspects are especially interesting. First, the fact that at 5 months, autonomic arousal predicts the duration of subsequent attention episodes, but at 10 months this effect is not present. Conversely, at 10 months, theta power predicts the duration of looking episodes, but this effect is not present in 5-month-old infants. This pattern of results suggests that younger infants have less control over their attention, which mostly depends on their current state of arousal, but older infants have gained cortical control of their attention, which in turn impacts their looking behaviour and arousal.

We thank the reviewer for the close attention that they have paid to our manuscript, and for their insightful comments.

Reviewer #2 (Public Review):

Summary:

This manuscript explores infants' attention patterns in real-world settings and their relationship with autonomic arousal and EEG oscillations in the theta frequency band. The study included 5- and 10-month-old infants during free play. The results showed that the 5-month-old group exhibited a decline in HR forward-predicted attentional behaviors, while the 10-month-old group exhibited increased theta power following shifts in gaze, indicating the start of a new attention episode. Additionally, this increase in theta power predicted the duration of infants' looking behavior.

Strengths:

The study's strengths lie in its utilization of advanced protocols and cutting-edge techniques to assess infants' neural activity and autonomic arousal associated with their attention patterns, as well as the extensive data coding and processing. Overall, the findings have important theoretical implications for the development of infant attention.

Weaknesses:

Certain methodological procedures require further clarification, e.g., details on EEG data processing. Additionally, it would be beneficial to eliminate possible confounding factors and consider alternative interpretations, e,g., whether the differences observed between the two age groups were partly due to varying levels of general arousal and engagement during the free play.

We thank the reviewer for their suggestions and have addressed them in our point-by-point responses below.

Reviewer #3 (Public Review):

Summary:

Much of the literature on attention has focused on static, non-contingent stimuli that can be easily controlled and replicated--a mismatch with the actual day-to-day deployment of attention. The same limitation is evident in the developmental literature, which is further hampered by infants' limited behavioral repertoires and the general difficulty in collecting robust and reliable data in the first year of life. The current study engages young infants as they play with age-appropriate toys, capturing visual attention, cardiac measures of arousal, and EEG-based metrics of cognitive processing. The authors find that the temporal relations between measures are different at age 5 months vs. age 10 months. In particular, at 5 months of age, cardiac arousal appears to precede attention, while at 10 months of age attention processes lead to shifts in neural markers of engagement, as captured in theta activity.

Strengths:

The study brings to the forefront sophisticated analytical and methodological techniques to bring greater validity to the work typically done in the research lab. By using measures in the moment, they can more closely link biological measures to actual behaviors and cognitive stages. Often, we are forced to capture these measures in separate contexts and then infer in-the-moment relations. The data and techniques provide insights for future research work.

Weaknesses:

The sample is relatively modest, although this is somewhat balanced by the sheer number of data points generated by the moment-to-moment analyses. In addition, the study is cross-sectional, so the data cannot capture true change over time. Larger samples, followed over time, will provide a stronger test for the robustness and reliability of the preliminary data noted here. Finally, while the method certainly provides for a more active and interactive infant in testing, we are a few steps removed from the complexity of daily life and social interactions.

We thank the reviewer for their suggestions and have addressed them in our point-by-point responses below.

Reviewer #1 (Recommendations For The Authors):

Here are some specific ways in which clarity can be improved:

A. Regarding the distinction between constructs, or measures and constructs:

i. In the results section, I would prefer to mention looking at duration and heart rate as metrics that have been measured, while in the introduction and discussion, a clear 1-to-1 link between construct/cognitive process and behavioural or (neuro)psychophysical measure can be made (e.g., sustained attention is measured via looking durations; autonomic arousal is measured via heart-rate). 

The way attention and arousal were operationalised are now clarified throughout the text, especially in the results.

ii. Relatedly, the "attention" variable is not really measuring attention directly. It is rather measuring looking time (proportion of looking time to the toys?), which is the operationalisation, which is hypothesised to be related to attention (the construct/cognitive process). I would make the distinction between the two stronger.

This distinction between looking and paying attention is clearer now in the reviewed manuscript as per R1 and R3’s suggestions. We have also added a paragraph in the Introduction to clarify it and pointed out its limitations (see pg.5).

B. Each analysis should be set out to address a specific hypothesis. I would rather see hypotheses in the introduction (without direct reference to the details of the models that were used), and how a specific relation between variables should follow from such hypotheses. This would also solve the issue that some analyses did not seem directly necessary to the main goal of the paper. For example:

i. Are ACF and survival probability analyses aimed at proving different points, or are they different analyses to prove the same point? Consider either making clearer how they differ or moving one to supplementary materials.

We clarified this in pg. 4 of the revised manuscript.

ii. The autocorrelation results are not mentioned in the introduction. Are they aiming to show that the variables can be used for cross-correlation? Please clarify their role or remove them.

We clarified this in pg. 4 of the revised manuscript.

C. Clarity of cross-correlation figures. To ensure clarity when presenting a cross-correlation plot, it's important to provide information on the lead-lag relationships and which variable is considered X and which is Y. This could be done by labelling the axes more clearly (e.g., the left-hand side of the - axis specifies x leads y, right hand specifies y leads x) or adding a legend (e.g., dashed line indicates x leading y, solid line indicates y leading x). Finally, the limits of the x-axis are consistent across plots, but the limits of the y-axis differ, which makes it harder to visually compare the different plots. More broadly, the plots could have clearer labels, and their resolution could also be improved. 

This information on what variable precedes/ follows was in the caption of the figures. However, we have edited the figures as per the reviewer’s suggestion and added this information in the figures themselves. We have also uploaded all the figures in higher resolution.

D. Figure 7 was extremely helpful for understanding the paper, and I would rather have it as Figure 1 in the introduction. 

We have moved figure 7 to figure 1 as per this request.

E. Statistics should always be reported, and effects should always be described. For example, results of autocorrelation are not reported, and from the plot, it is also not clear if the effects are significant (the caption states that red dots indicate significance, but there are no red dots. Does this mean there is no autocorrelation?).

We apologise – this was hard to read in the original. We have clarified that there is no autocorrelation present in Fig 7A and 7D.

And if so, given that theta is a wave, how is it possible that there is no autocorrelation (connected to point 1)? 

We thank the reviewer for raising this point. In fact, theta power is looking at oscillatory activity in the EEG within the 3-6Hz window (i.e. 3 to 6 oscillations per second). Whereas we were analysing the autocorrelation in the EEG data by looking at changes in theta power between consecutive 1 second long windows. To say that there is no autocorrelation in the data means that, if there is more 3-6Hz activity within one particular 1-second window, there tends not to be significantly more 3-6Hz activity within the 1-second windows immediately before and after.

F. Alpha power is introduced later on, and in the discussion, it is mentioned that the effects that were found go against the authors' expectations. However, alpha power and the authors' expectations about it are not mentioned in the introduction. 

We thank the reviewer for this comment. We have added a paragraph on alpha in the introduction (pg.4).

Minor points:

1. At the end of 1st page of introduction, the authors state that: 

“How children allocate their attention in experimenter-controlled, screen-based lab tasks differs, however, from actual real-world attention in several ways (32-34). For example, the real-world is interactive and manipulable, and so how we interact with the world determines what information we, in turn, receive from it: experiences generate behaviours (35).”

I think there's more to this though - Lab-based studies can be made interactive too (e.g., Meyer et al., 2023, Stahl & Feigenson, 2015). What remains unexplored is how infants actively and freely initiate and self-structure their attention, rather than how they respond to experimental manipulations.

Meyer, M., van Schaik, J. E., Poli, F., & Hunnius, S. (2023). How infant‐directed actions enhance infants' attention, learning, and exploration: Evidence from EEG and computational modeling. Developmental Science, 26(1), e13259.

Stahl, A. E., & Feigenson, L. (2015). Observing the unexpected enhances infants' learning and exploration. Science, 348(6230), 91-94.

We thank the reviewer for this suggestion and added their point in pg. 4.

(2) Regarding analysis 4:

a. In analysis 1 you showed that the duration of attentional episodes changes with age. Is it fair to keep the same start, middle, and termination ranges across age groups? Is 3-4 seconds "middle" for 5-month-olds? 

We appreciate the comment. There are many ways we could have run these analyses and, in fact, in other papers we have done it differently, for example by splitting each look in 3, irrespective of its duration (Phillips et al., 2023).

However, one aspect we took into account was the observation that 5-month-old infants exhibited more shorter looks compared to older infants. We recognized that dividing each into 3 parts, regardless of its duration, might have impacted the results. Presumably, the activity during the middle and termination phases of a 1.5-second look differs from that of a look lasting over 7 seconds.

Two additional factors that provided us with confidence in our approach were: 1) while the definition of "middle" was somewhat arbitrary, it allowed us to maintain consistency in our analyses across different age points. And, 2) we obtained a comparable amount of observations across the two time points (e.g. “middle” at 5 months we had 172 events at 5 months, and 194 events at 10 months).

b. It is recommended not to interpret lower-level interactions if more complex interactions are not significant. How are the interaction effects in a simpler model in which the 3-way interaction is removed? 

We appreciate the comment. We tried to follow the same steps as in (Xie et al., 2018). However, we have re-analysed the data removing the 3-way interaction and the significance of the results stayed the same. Please see Author response image 2 below (first: new analyses without the 3-way interactions, second: original analyses that included the 3-way interaction).

Author response image 2.

(3) Figure S1: there seems to be an outlier in the bottom-right panel. Do results hold excluding it? 

We re-run these analyses as per this suggestion and the results stayed the same (refer to SM pg. 2).

(4) Figure S2 should refer to 10 months instead of 12.

We thank the reviewer for noticing this typo, we have changed it in the reviewed manuscript (see SM pg. 3). 

(5) In the 2nd paragraph of the discussion, I found this sentence unclear: "From Analysis 1 we found that infants at both ages showed a preferred modal reorientation rate". 

We clarified this in the reviewed manuscript in pg10

(6) Discussion: many (infant) studies have used theta in anticipation of receiving information (Begus et al., 2016) surprising events (Meyer et al., 2023), and especially exploration (Begus et al., 2015). Can you make a broader point on how these findings inform our interpretation of theta in the infant population (go more from description to underlying mechanisms)? 

We have extended on this point on interpreting frequency bands in pg13 of the reviewed manuscript and thank the reviewer for bringing it up.

Begus, K., Gliga, T., & Southgate, V. (2016). Infants' preferences for native speakers are associated with an expectation of information. Proceedings of the National Academy of Sciences, 113(44), 12397-12402.

Meyer, M., van Schaik, J. E., Poli, F., & Hunnius, S. (2023). How infant‐directed actions enhance infants' attention, learning, and exploration: Evidence from EEG and computational modeling. Developmental Science, 26(1), e13259.

Begus, K., Southgate, V., & Gliga, T. (2015). Neural mechanisms of infant learning: differences in frontal theta activity during object exploration modulate subsequent object recognition. Biology letters, 11(5), 20150041.

(7) 2nd page of discussion, last paragraph: "preferred modal reorientation timer" is not a neural/cognitive mechanism, just a resulting behaviour. 

We agree with this comment and thank the reviewer for bringing it out to our attention. We clarified this in in pg12 and pg13 of the reviewed manuscript.

Reviewer #2 (Recommendations For The Authors):

I have a few comments and questions that I think the authors should consider addressing in a revised version. Please see below:

(1) During preprocessing (steps 5 and 6), it seems like the "noisy channels" were rejected using the pop_rejchan.m function and then interpolated. This procedure is common in infant EEG analysis, but a concern arises: was there no upper limit for channel interpolation? Did the authors still perform bad channel interpolation even when more than 30% or 40% of the channels were identified as "bad" at the beginning with the continuous data? 

We did state in the original manuscript that “participants with fewer than 30% channels interpolated at 5 months and 25% at 10 months made it to the final step (ICA) and final analyses”. In the revised version we have re-written this section in order to make this more clear (pg. 17).

(2) I am also perplexed about the sequencing of the ICA pruning step. If the intention of ICA pruning is to eliminate artificial components, would it be more logical to perform this procedure before the conventional artifacts' rejection (i.e., step 7), rather than after? In addition, what was the methodology employed by the authors to identify the artificial ICA components? Was it done through manual visual inspection or utilizing specific toolboxes? 

We agree that the ICA is often run before, however, the decision to reject continuous data prior to ICA was to remove the very worst sections of data (where almost all channels were affected), which can arise during times when infants fuss or pull the caps. Thus, this step was applied at this point in the pipeline so that these sections of really bad data were not inputted into the ICA. This is fairly widespread practice in cleaning infant data.

Concerning the reviewer’s second question, of how ICA components were removed – the answer to this is described in considerable detail in the paper that we refer to in that setion of the manuscript. This was done by training a classifier specially designed to clean naturalistic infant EEG data (Haresign et al., 2021) and has since been employed in similar studies (e.g. Georgieva et al., 2020; Phillips et al., 2023).

(3) Please clarify how the relative power was calculated for the theta (3-6Hz) and alpha (6-9Hz) bands. Were they calculated by dividing the ratio of theta or alpha power to the power between 3 and 9Hz, or the total power between 1 (or 3) and 20 Hz? In other words, what does the term "all frequency bands" refer to in section 4.3.7? 

We thank the reviewer for this comment, we have now clarified this in pg. 22.

(4) One of the key discoveries presented in this paper is the observation that attention shifts are accompanied by a subsequent enhancement in theta band power shortly after the shifts occur. Is it possible that this effect or alteration might be linked to infants' saccades, which are used as indicators of attention shifts? Would it be feasible to analyze the disparities in amplitude between the left and right frontal electrodes (e.g., Fp1 and Fp2, which could be viewed as virtual horizontal EOG channels) in relation to theta band power, in order to eliminate the possibility that the augmentation of theta power was attributable to the intensity of the saccades? 

We appreciate the concern. Average saccade duration in infants is about 40ms (Garbutt et al., 2007). Our finding that the positive cross-correlation between theta and look duration is present not only when we examine zero-lag data but also when we examine how theta forwards-predicts attention 1-2 seconds afterwards seems therefore unlikely to be directly attributable to saccade-related artifact. Concerning the reviewer’s suggestion – this is something that we have tried in the past. Unfortunately, however, our experience is that identifying saccades based on the disparity between Fp1 and Fp2 is much too unreliable to be of any use in analysing data. Even if specially positioned HEOG electrodes are used, we still find the saccade detection to be insufficiently reliable. In ongoing work we are tracking eye movements separately, in order to be able to address this point more satisfactorily.

(5) The following question is related to my previous comment. Why is the duration of the relationship between theta power and moment-to-moment changes in attention so short? If theta is indeed associated with attention and information processing, shouldn't the relationship between the two variables strengthen as the attention episode progresses? Given that the authors themselves suggest that "One possible interpretation of this is that neural activity associates with the maintenance more than the initiation of attentional behaviors," it raises the question of (is in contradiction to) why the duration of the relationship is not longer but declines drastically (Figure 6). 

We thank the reviewer for raising this excellent point. Certainly we argue that this, together with the low autocorrelation values for theta documented in Fig 7A and 7D challenge many conventional ways of interpreting theta. We are continuing to investigate this question in ongoing work.

(6) Have the authors conducted a comparison of alpha relative power and HR deceleration durations between 5 and 10-month-old infants? This analysis could provide insights into whether the differences observed between the two age groups were partly due to varying levels of general arousal and engagement during free play.

We thank the reviewer for this suggestion. Indeed, this is an aspect we investigated but ultimately, given that our primary emphasis was on the theta frequency, and considering the length of the manuscript, we decided not to incorporate. However, we attached Author response image 3 below showing there was no significant interaction between HR and alpha band.

Author response image 3.

Reviewer #3 (Recommendations For The Authors):

(1) In reading the manuscript, the language used seems to imply longitudinal data or at the very least the ability to detect change or maturation. Given the cross-sectional nature of the data, the language should be tempered throughout. The data are illustrative but not definitive. 

We thank the reviewer for this comment. We have now clarified that “Data was analysed in a cross-sectional manner” in pg15.

(2) The sample size is quite modest, particularly in the specific age groups. This is likely tempered by the sheer number of data points available. This latter argument is implied in the text, but not as explicitly noted. (However, I may have missed this as the text is quite dense). I think more notice is needed on the reliability and stability of the findings given the sample. 

We have clarified this in pg16.

(3) On a related note, how was the sample size determined? Was there a power analysis to help guide decision-making for both recruitment and choosing which analyses to proceed with? Again, the analytic approach is quite sophisticated and the questions are of central interest to researchers, but I was left feeling maybe these two aspects of the study were out-sprinting the available data. The general impression is that the sample is small, but it is not until looking at table s7, that it is in full relief. I think this should be more prominent in the main body of the study.

We have clarified this in pg16.

(4) The devotes a few sentences to the relation between looking and attention. However, this distinction is central to the design of the study, and any philosophical differences regarding what take-away points can be generated. In my reading, I think this point needs to be more heavily interrogated. 

This distinction between looking and paying attention is clearer now in the reviewed manuscript as per R1 and R3’s suggestions. We have also added a paragraph in the Introduction to clarify it and pointed out its limitations (see pg.5).

(5) I would temper the real-world attention language. This study is certainly a great step forward, relative to static faces on a computer screen. However, there are still a great number of artificial constraints that have been added. That is not to say that the constraints are bad--they are necessary to carry out the work. However, it should be acknowledged that it constrains the external validity. 

We have added a paragraph to acknowledged limitations of the setup in pg. 14.

(6) The kappa on the coding is not strong. The authors chose to proceed nonetheless. Given that, I think more information is needed on how coders were trained, how they were standardized, and what parameters were used to decide they were ready to code independently. Again, with the sample size and the kappa presented, I think more discussion is needed regarding the robustness of the findings. 

We appreciate the concern. As per our answer to R1, we chose to report the most stringent calculator of inter-rater reliability, but other calculation methods (i.e., percent agreement) return higher scores (see response to R1).

As per the training, we wrote an extensively detailed coding scheme describing exactly how to code each look that was handed to our coders. Throughout the initial months of training, we meet with the coders on a weekly basis to discuss questions and individual frames that looked ambiguous. After each session, we would revise the coding scheme to incorporate additional details, aiming to make the coding process progressively less subjective. During this period, every coder analysed the same interactions, and inter-rater reliability (IRR) was assessed weekly, comparing their evaluations with mine (Marta). With time, the coders had fewer questions and IRR increased. At that point, we deemed them sufficiently trained, and began assigning them different interactions from each other. Periodically, though, we all assessed the same interaction and meet to review and discuss our coding outputs.

eLife assessment

This valuable manuscript reveals sex differences in bi-conditioning Pavlovian learning and conditional behavior. Males learn hierarchical context-cue-outcome associations more quickly, but females show more stable and robust task performance. These sex differences are related to cellular activation in the orbitofrontal cortex. Although the evidence for the claims is convincing, the claim of sex differences in context-dependent discrimination behaviour is overstated in places. Nevertheless, the results will be of interest to many behavioural neuroscientists, particularly those who investigate sex-specific behaviours.

Reviewer #1 (Public Review):

Summary:

Peterson et al., present a series of experiments in which the Pavlovian performance (i.e. time spent at a food cup/port) of male and female rats is assessed in various tasks in which context/cue/outcome relationships are altered. The authors find no sex differences in context-irrelevant tasks, and no such differences in tasks in which the context signals that different cues will earn different outcomes. They do find sex differences, however, when a single outcome is given and context cues must be used to ascertain which cue will be rewarded with that outcome (Ctx-dep O1 task). Specifically, they find that males acquired the task faster, but that once acquired, performance of the task was more resilient in female rats against exposures to a stressor. Finally, they show that these sex differences are reflected in differential rates of c-fos expression in all three subregions of rat OFC, medial, lateral and ventral, in the sense that it is higher in females than males, and only in the animals subject to the Ctx-dep O1 task in which sex differences were observed.

Strengths:

• Well written<br /> • Experiments elegantly designed<br /> • Robust statistics<br /> • Behaviour is the main feature of this manuscript, rather than any flashy techniques or fashionable lab methodologies, and luckily the behaviour is done really well.<br /> • For the most part I think the conclusions were well supported, although I do have some slightly different interpretations to the authors in places.

Weaknesses:

The authors have done an excellent job of addressing all previous weaknesses. I have no further comments.

Reviewer #2 (Public Review):

Summary:

A bidirectional occasion-setting design is used to examine sex differences in the contextual modulation of reward-related behaviour. It is shown that females are slower to acquire contextual control over cue-evoked reward seeking. However, once established, the contextual control over behaviour was more robust in female rats (i.e., less within-session variability and greater resistance to stress) and this was also associated with increased OFC activation.

Strengths:

The authors use sophisticated behavioural paradigms to study the hierarchical contextual modulation of behaviour. The behavioural controls are particularly impressive and do, to some extent, support the specificity of the conclusions. The analyses of the behavioural data are also elegant, thoughtful, and rigorous.

Comments on revised version:

In this revised version the authors have addressed the major weaknesses that I identified in my previous review.

Reviewer #3 (Public Review):

Summary:

This manuscript reports an experiment that compared groups of rats acquisition and performance of a Pavlovian bi-conditional discrimination, in which the presence of one cue, A, signals that the presentation of one CS, X, will be followed by a reinforcer and a second CS, Y, will be nonreinforced. Periods of cue A alternated with periods of cue B, which signaled the opposite relationship, cue X is nonreinforced and cue Y is reinforced. This is a conditional discrimination problem in which the rats learned to approach the food cup in the presence of each CS conditional on the presence of the third background cue. The comparison groups consisted of the same conditional discrimination with the exception that each CS was paired with a different reinforcer. This makes the problem easier to solve as the background is now priming a differential outcome. A third group received simple discrimination training of X reinforced and Y nonreinforced in cues A and B, and the final group were trained with X and Y reinforced on half the trials (no discrimination). The results were clear that the latter two discrimination learning procedures resulted in rapid learning in comparison to the first. Rats required about 3 times as many 4-session blocks to acquire the bi-conditional discrimination than the other two discrimination groups. Within the biconditional discrimination group, female and male rats spent the same amount of time in the food cup during the rewarded CS, but females spent more time in the food cup during CS- than males. The authors interpret this as a deficit in discrimination performance in females on this task and use a measure that exaggerates the difference in CS+ and CS_ responding (a discrimination ratio) to support their point. When tested after acute restraint stress, the male rats spent less time in the food cup during the reinforced CS in comparison to the female rats, but did not lose discrimination performance entirely. The was also some evidence of more fos positive cells in the orbitofrontal cortex in females. Overall, I think the authors were successful in documenting performance on the biconditional discrimination task, showing that it is more difficult to perform than other discriminations is valuable and consistent with the proposal that accurate performance requires encoding of conditional information (which the authors refer to as "context"). There is evidence that female rats spend more time in the food cup during CS-, but this I hesitate to agree that this is an important sex difference. There is no cost to spending more time in the food cup during CS- and they spend much less time there than during CS+. Males and females also did not differ in their CS+ responding, suggesting similar levels of learning, A number of factors could contribute to more food cup time in CS-, such as smaller body size and more locomotor activity. The number of food cup entries during CS+ and CS- was not reported here. Nevertheless, I think the manuscript will make a useful contribution to the field and hopefully lead readers to follow up on these types of tasks. One area for development would be to test the associative properties of the cues controlling the conditional discrimination, can they be shown to have the properties of Pavlovian occasion setting stimuli? Such work would strengthen the justification/rationale for using the term "context" and "occasion setter" to refer to these stimuli in this task in the way the authors do in this paper.

Strengths:

Nicely designed and conducted experiment.<br /> Documents performance difference by sex.

Weaknesses:

Overstatement of sex differences.<br /> Inconsistent, confusing, and possibly misleading use of terms to describe/imply the underlying processes contributing to performance.

Author response:

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

We thank the reviewers for their constructive comments on our manuscript and their appreciation of the results. We provide point-by-point responses bellow. For your convenience we highlight here the main changes to the manuscript.

·        More descriptive terminology for the contextual cues (Ctx.A / Ctx.noA is now referred to as LIGHT / DARK).

·        Schematic of experiment timeline highlighting the exclusion of non-discriminators following the initial acquisition period. This explains the absence of baseline sex differences post acquisition and clears up some misconceptions about lack of replicability.

·        New data (time in port preCS) showing that a prior reward does not cause continued presence in port.

·        Several text edits to address all the points raised by the reviewers.

We hope that the editors and reviewers will be satisfied with this revised version and find the strength of the evidence more convincing.

Reviewer #1 (Recommendations For The Authors):

In relation to weaknesses points 1-4 in the public review:

(1) With regards to the claim (page 4 of pdf), I think I can see what the authors are getting at when they claim "Only Ctx-dep.01 engages context-gated reward predictions", because the same reward is available in each context, and the animal must use contextual information to determine which cue will be rewarded. In other words, it has a discriminative purpose. In Ctx-dep.O1/O2, however, although the context doesn't serve a discriminative purpose in the sense that one cue will always earn a unique outcome, regardless of context, the fact that these cues are differentially rewarded in the different context means that animals may well form context-gated cue-outcome associations (e.g. CtxA-(CS1-O1), CtxnoA-(CS2-O2)). Moreover, the context is informative in this group in telling the animal which cue will be rewarded, even prior to outcome delivery, such that I don't think contextual information will fade to the background of the association and attention be lost to it in the way, say Mackintosh (1975) might predict. Therefore, I don't think this statement is correct.

I suggest that the authors refine the statement to be more accurate.

We agree with the reviewer —the context is absolutely relevant for rats trained in the Ctx-dep. O1/O2 task. We have edited the text in several places to make this clear. The question is how (by what mechanism) does the context participate in the control of behavior in this group. The reviewer correctly points out that, just like rats trained in the Ctx-dep. O1 task, rats trained in the Ctx-dep. O1/O2 might have formed context-gated cue-outcome associations. We now clearly acknowledge that in the text.

However, because in this group the two outcomes are always encountered in different contexts, we argue that these rats could also have formed a direct association between the two contexts and the two outcomes. In other words, each context might directly evoke the expectation of a distinct reward outcome (prepare to drink, or prepare to eat). On a given trial, if the cue and context both tend to activate the same outcome representation, the converging cue+context excitation can add up. This would produce a context-sensitive response, but not via hierarchical modulation process (unlike Ctx-dep O1). Arguably, this last associative mechanism is much simpler and might explain why almost all rats in Ctx-dep. O1/O2 group learned the discrimination and at a much faster rate.

Therefore, while rats trained in Ctx-dep O1/O2 might engage a combination of associative processes to achieve context-sensitive behavior (including hierarchical associations), only rats in the Ctx-dep O1 critically and unambiguously rely on hierarchical associations to achieve context-sensitive behavior.

(2) I think the results shown in Figure 1 are very interesting, and well supported by the statistics. It's so nice to see a significant interaction, as so many papers try to report these types of effects without it. However, I do wonder how specific the results are to contextual modulation. That is, should a discriminative discrete cue be used instead of each context (e.g. CS1 indicates CS2 earns O1, CS3 indicates CS4 earns O1), would female rats still be as slow to learn the discrimination?

I am just curious as to whether the authors have thoughts on this.

We have not tested this and are not aware of a paper that examined this question specifically.

However, we would like to point out that in the suggested design (CS1→[CS2→O1]; CS3→[CS4→O1]) the discriminative cues (CS1 and CS3) would almost certainly also acquire substantial reward-predictive value, either because of their direct association with the reward, or via second-order conditioning. This would complicate the interpretation of the results in terms of hierarchical associations. Incorporating non-rewarded presentation of CS1 and CS3 alone (i.e. extinguishing those cues, as is sometimes done in occasion setting experiments) would be one way to reduce the reward expectation evoked by those cues, but this approach has some limitations. Indeed, as mentioned by Rescorla (2006) “During extinction, the net associative strength of a stimulus declines to the level of [a response] threshold, but further decrement stops at that point”. So while extinguished CS1 and CS3 might no longer evoke overt behavioral responses, these cues could retain nonnegligible subthreshold excitatory connection with the US.  Individually, these cues might fail to evoke responding but could nonetheless increase responding during the CS1→CS2 trials (or CS3→CS4 trials), via simple summation. (Rescorla, 2006: “the compound of two [extinguished] stimuli has a strength that exceeds the threshold and so evokes responding”).

This type of consideration is precisely why we opted for the behavioral task used in the study. In Ctx-dep. O1, the discriminative stimuli exert opposite effects on the two target cues, which rules out summation effects as a mechanism for context-sensitive behavior.

(3) Pages 8-9 of pdf, where the biological basis or the delayed acquisition of contextual control in females is considered, I find this to be written from a place of assuming that what is observed in the males is the default behaviour. That is, although the estrous cycle and its effects on synaptic plasticity/physiology may well account for the results, is there not a similar argument to be made for androgens in males? Perhaps the androgens also somehow alter synaptic plasticity/physiology, leading to their faster speed, reduced performance stability, and increased susceptibility to stress.

I would like the argument that female behaviour might be the default, and male behaviour the deviation to be considered in the discussion in addition to those already stated.

We regret if we gave the impression that male behavior was the default. The paper is intended to report sex differences but we don’t view either sex as the default. To correct this impression, we have added a few sentences in the discussion to highlight male-hormonal factors as well as non-gonadal genetic factors that might have contributed to the observed sex differences.

(4) In addition, the OFC - which is the brain region found to have differential expression of c-fos in males and females in Figure 5 - is not explicitly discussed with regard to the biological mechanisms of differences, which seems odd.

I suggest OFC be discussed with regard to biological mechanisms of differences.

We added a few sentences in the discussion to i) highlight the parallel between our study and human fMRI studies showing superior OFC activation in females during the regulation of emotional responses, ii) Suggest a potential relationship between the reported sex differences (speed of acquisition, robustness of performance, and OFC activation in context-gated reward prediction), iii) acknowledge our ignorance of the root causes of these sex differences.

We wish we could offer a better answer. We have attempted to offer possible proximal explanations for the observed sex differences, but ultimately our work did not address the root causes of these behavioral and neural sex differences. Therefore we feel that further attempts to explain these differences would be too speculative.

(5) I did wonder if the authors were aware that in the Rescorla-Wagner model, contextual stimuli are thought to summate with discrete cues to enter into the association with the outcome (i.e., the error term is between lambda and sigmaV, with sigmaV the 'summation' of all stimuli present on a trial, including contextual stimuli). Typically, this is not considered much, because the cue itself is so salient and more consistently paired with reward (whereas the ever-present context is often paired with no reward), but nevertheless, it is a part of the association. I'm not sure it's wrong to say that the background circumstances under which events occur are thought to play little role (as in the second sentence of the introduction), but I was wondering if the authors were aware of this fact when they wrote that.

This sentence in the introduction was meant to introduce the distinction between eliciting stimuli and modulating contexts. Admittedly, this paints a naive picture, which we now acknowledge (we hope that the rest of the paper provides more nuance). As pointed out by this reviewer, the context is also a stimulus, and, just like any other stimulus, it is eligible for direct association with an outcome. The possibility for direct context→outcome association is precisely the rational for the Ctx-dep O1/O2 group.

(6) Context-noA - Seems a little confusing for a name, why not just call it context B? NoA appears to imply that nothing happens in A or no outcome is available, whereas this is not always the case.

We debated which terminology to use. We felt that “Context A vs. Context B” should perhaps be reserved to situations where the global context changes (e.g. two different conditioning boxes with different odors, floor texture etc., with proper counterbalancing procedures). We felt that “Context A vs noA” might be more appropriate here, as we are manipulating the local context by introducing (or removing) one single stimulus (the houselight). In this revised version we followed this reviewer’s advice and adopted a more descriptive, and hopefully less confusing, terminology: "Light vs Dark”.

(7) Why is it that in the text the Ctx-dep O1/O2 is explained before simple and no discrimination, but in the Figure Ctx-dep O1/O2 is shown last? These should be consistent.

Thanks for pointing that out. We have switched the order of task description to be consistent with the figures.

(8) Page 6 (of pdf) - could the authors elaborate a little on why or how (or both) the delivery of reward can interfere with the expression of context-dependent discrimination? Do they just mean the performance of discrimination (e.g., animals will sit at the food port longer if there is food there because they are sitting there and eating it, which does not necessarily reflect the expectation of food based on cue presentations?), in which case it is not the discrimination itself that is being interfered with, just the measure of it. Perhaps the authors could elaborate by just inserting a sentence.

We have added a few sentences to discuss this effect.

The first clarification that we can make is that the reduced discrimination performance following reward is not simply due to animals’ continued presence in the reward port. We have added the time pre-cue to Fig. 3 B-F. This measure is not affected by previous reward history, showing that rats are leaving the port between trials.

So what is driving this effect? At this stage, we are agnostic about the mechanism(s) for this effect. Kuchibhotla et al. (2019) —who first reported a similar effect— proposed a model in which recent rewards modify the threshold for behavioral responses (i.e. performance). In this model, a cue might evoke a weak reward prediction but evoke a strong behavioral response if presented after a reward. Additionally, we believe that learning factors might also contribute to the effect reported here. Indeed, the behavioral response on a given trial likely reflects the balance of hierarchical (context-dependent) associations vs. direct associations (Bradfield and Balleine, 2013). Naturally, this balance is dynamic and influenced by trial history. For instance, a Light:X+ trial might increase the value of cue X and promote responding during the following Dark:X- trial. The same logic could be applied to the influence of the context (e.g., Light:X+ trial might promote responding to a subsequent Light:Y- trial). We are currently working on a computational model that captures the dynamic interplay between hierarchical associations and direct associations. We hope that this model will provide some insight into the learning/performance mechanism for the effects reported here. However this computational work is still in the early stages and beyond the scope of the present study.

(9) The lack of effect in the Ctx-dep O1/O2 groups in Figure 4 could be due to a lack of power - the group sizes are a lot smaller for this group than for Ctx-dep O1 where an interaction was detected. I think this should be at least addressed in the discussion (i.e., that this lack of effect is possibly due to less power here, as the effects are in the same direction).

Good point. We now acknowledge this limitation in the text.

Reviewer #2 (Recommendations For The Authors):

(1) Please comment on the failure to replicate the sex differences across experiments. Perhaps this is due to some change in the training procedure that is briefly mentioned in the methods (a reduction in the number of rewarded trials) but it is unclear.

The reviewer correctly observed that Fig. 3-5 do not show sex differences in baseline condition. This is not because of a replication failure, but because non-discriminating subjects were excluded from the experiment at the end of the acquisition period (after 72 training sessions). We now clarify this in the Method and Results section. We also added a schematic of the experiment timeline that highlights the exclusion of non-discriminators at the end of the acquisition period (Fig 1).

On the topic of replicability, the data for Ctx-dep O1 was collected over 3 cohorts (over the course of 2 years) and the sex difference pattern was consistent.  For instance, the proportion of discriminators vs. non-discriminators for males and females trained in Ctx-dep O1, showed similar patterns across cohorts (see below).

Author response table 1.

(2) The design of this experiment makes it possible to analyse whether there is a differential outcome effect (DOE). The DOE would indeed predict better discrimination in group cxt-dep O1/O2 versus cxt-dep O1, which seems to be exactly what the authors observe although between-group statistics are not reported. Inspection of Figure 1 suggests that there may be a DOE in females but not in males. I wonder if the authors might consider reanalysing the data to check this.

Indeed, there is clearly a differential outcome effect. We now point out this DOE in relation to the latency to achieve discrimination criterion (Fig. 2 C-D). Rats in the Ctx-dep. O1/O2 group acquired discrimination (reached criterion) much faster than rats in in the Ctx-dep. O1 group.

Following the reviewer’s suggestion, we provide here the results of targeted ANOVAs (focusing exclusively on Ctx-dep. O1 and Ctx-dep. O1/O2) to investigate a potential sex-dependent effect of DOE (i.e. Sex x Task interactions), see figure below. A three-way ANOVA (Sex x Task x Session) conducted on the discrimination index reveal a main effect of Task (F1, 86 \= 173.560, P < 0.001), Session (F2.678, 230.329 \= 140.479, P<0.001) and a marginal effect of Sex (F1,86 = 3.929, P = 0.051), but critically no Task x Sex or Task x Sex x Session interaction (P ≥ 0.504). A two-way ANOVA (Sex x Task) conducted on the sessions to criterion revealed a main effect of both factors (Sex F1, 63 = 9.52, P = 0.003; Task F1, 62 = 184.143, P < 0.001) but critically, no Sex x Task interaction (P = 0.233).  These results indicate that the use of two different outcomes clearly facilitated the acquisition of context-dependent discrimination (DOE effect), but this effect benefited both sexes equally. We thank the reviewer for recommending this analysis.

Author response image 1.

Differential outcome effect (DOE) affects males and females equally. A. Discrimination ratio over the acquisition period. B. trials to criterion. Compared to animals trained with a single outcome (Ctx-dep. O1), the introducing dissociable outcomes for the two type of rewarded trials (Ctx-dep. O1/O2) profoundly facilitated the acquisition of discriminated behavior. This effect benefited both sexes equally.

(3) Some minor points for clarification that the authors may also wish to address:

- Figure 3: is data presented from sessions 71-80 only or for all sessions? I didn't fully follow the explanation offered in the results section.

That’s right. The data presented in Fig. 3 considers only sessions 71-80, in discriminator rats —when performance is globally stable. We have edited the text to make this clearer. These 10 sessions represent a total of 800 trials (=10 session * 80 trials). The first trial of a session what not included in the analysis since it was not preceded by any trial. For the remaining 790 trials (10 session x 79 trials), we examined how the outcome of the past trial (reward or nonrewarded) influenced responding on the next trial.  This large sample size (790 trials / rat) was required to ensure that enough data was collected for each possible trial history scenario.

- The authors argue that females are protected from the disrupting effect of stress. It might be useful if the authors offer further explanation as to what they mean by "protected".

By “protected”, we simply mean “less sensitive”. We have reworded this sentence in that way. We do not claim to have an understanding of the precise mechanism for this sex dependent effect (although our data point to a possible role of the OFC).

- The authors state that "delivery of reward, while critical for learning, can also interfere with the expression of context-dependent discrimination". This statement should be explained in further detail. For instance, why should reward delivery specifically impair context-dependent discrimination but not other forms of discrimination?

We have reworded this sentence to be more inclusive. Indeed, delivery of reward also interferes with other forms of discrimination, particularly when discrimination performance is not yet optimal. We have also added a paragraph to discuss the possible mechanisms by which reward might interfere with discrimination performance in our task.   

Reviewer #3 (Recommendations For The Authors):

I do not suggest additional experiments, but I do hope you continue the behavioral work to characterize what is being learned in the task. I think the approach is promising. I would suggest reporting the % time in port and port entries for the entire CS. There is no justification for only analyzing the response in the last 5s.

We thank the reviewer for the encouragement.

We opted to focus on the time in port for two main reasons:

(1) This measure is relatively consistent across the two different reward outcomes (unlike the rate of port entries). Indeed, consistent with prior studies (Delamater et al., 2017), we observed that the type of reward (solid or liquid) influences the topography of the anticipatory magazine-directed behavior. Specifically, cues paired with pellets elicited significantly more port entries than cues paired with chocolate milk. The opposite pattern was observed for time in port --cues paired with chocolate milk elicited more sustained time in port compared to cues paired with pellets (see figure below). While these measures (port entries and time in port) show opposite bias for the two possible outcomes, the size of this bias is much smaller for the time in port (Cohen’s d effect size: port entries: 1.41; time in port: 0.62). As a result, the discrimination ratio calculated from Time in port is consistent across the two outcomes (P = 0.078; effect size: 0.07), which is not the case for the discrimination ratio calculated from port entries (P = 0.007; effect size 0.32 see figure below).

(2) Unlike the rate of port entries, the time in port shows monotonic increase during training in these tasks. Indeed, we observed here and in past work (Keiflin et al., 2019), that the rate of port entries initially increases with training, but then slightly decreases; particularly for cues paired with liquid reward. In contrast, the time in port continues to increase, or remains high, with extended training. This is easy to understand if we consider the extreme case of a hypothetical rat that might enter the port once upon cue presentation and maintain continued presence in port for the whole cue duration. This rat would have a relatively low rate of port entry (a single port entry per trial) but a high time in port.

This is not to say that the rate of port entries is not a valid measure overall (we have used, and continue to use, this metric in other preparations). However, for the reasons explained above, we believe that the time in port is a better metric for reward anticipation in this specific study.

Moreover, we chose to focus our analysis on the last 5s of the cue because that’s when anticipatory food cup behavior is more reliably observed (in our preparation >2/3 of the total time in port in occurs during the last 5s of the cue) and less contaminated by orienting behaviors (Holland, 1977, 1980, 2000). For these reasons, analysis of the last portion of the cue is relatively common in Pavlovian anticipatory approach preparations (El-Amamy and Holland, 2007; Olshavsky et al., 2013; Esber et al., 2015; Holland, 2016a, 2016b; Schiffino and Holland, 2016; Gardner et al., 2017; Sharpe et al., 2021; Maes et al., 2020; Sharpe et al., 2020; Siemian et al., 2021; Kang et al., 2021). Reporting time in port during the same cue epoch facilitates comparisons between these studies.

We have edited the text in the Method section to provide a brief justification for focusing our analyses on this cue epoch.

Author response image 2.

Outcome identity influences the topography of the conditioned response. A-C: Conditioned responding expressed as the number of port entries per trial (A) or time in port per trials (C) for rats trained in the simple discrimination task with a chocolate milk reward (n= 19) or a sucrose pellet (n = 16). Data show the average of the last three 3 sessions. Compared to chocolate milk, pellets tend to produce more port entries. Conversely, chocolate milk tend to produce more time in port. However the magnitude of this bias is smaller for the Time in port. C-D: discrimination ratio calculate from the number of port entries (C) or the time in port (D); the latter is not affected by the outcome identity. *P<0.05; **P<0.01; ***P<0.001 T tests.

The inconsistent use of terms is distracting throughout the paper. Is it discriminated or context-gated? Please provide a definition of your terms and then use them consistently. Is it a discriminative stimulus, a context, or an occasion setter? These all imply slightly different things and it would help the reader if you just used one term throughout the paper.

Thanks for pointing that out. We have added a definition for “context-gated” and edited the text to keep the terminology consistent when appropriate. The words “discrimination”/”discriminated” still appear in the manuscript but without implying a mechanism (all tasks are variations of Pavlovian discrimination; the rats discriminating between rewarded and non-rewarded trials).

As mentioned by this reviewer, the terms “context” and “occasion setter” are not synonymous. Therefore these terms still appear in the manuscript to refer to different concepts (e.g. in our task the visual stimulus is a context for all rats; this context acts as an occasion setter only for some rats).

Minor:

Intro, 2nd PP: "autism". This is abbreviated in the abstract but spelled out here. I suggest not abbreviating in the abstract and introducing abbreviations here, as you do with PTSD.

Fixed as suggested

Have deficits in contextual modulation been distinguished from potential deficits in binary associative learning in autism, PTSD, and substance use disorders? This is implied, but there are no citations provided.

We provide a list of references showing deficits in contextual modulation in these disorders.

This does not mean that these disorders are reducible to deficits in contextual modulation and it does not exclude other forms of deficits in those disorders --including alterations in certain aspects of binary associative learning.

"In positive occasion-setting, animals learn that a target cue (X) results in a reward outcome (+) only when that cue is accompanied by a contextual feature (A); the same cue presented in absence of this contextual feature remains without consequence (A:X+ / X-)." - there are words missing in this sentence.

We apologize but we fail identify the missing word(s). Perhaps the reviewer could be more specific and we will be happy to edit the sentence as needed.

What is a contextual feature, is this redundant or can you provide a specific definition?

We use the terminology “feature” and “target” as these are the standard terms in the description of occasion setting preparations (one stimulus, “the feature”, sets the occasion for responding –or not responding- to the “target” cue). By contextual feature, we meant that in this specific example the context was the feature. We have clarified this in the text. We believe that these terms are not redundant. Indeed, the context is not always a feature, and a feature is not necessarily a context (phasic cues can serve as “features”).

Can you provide some background on studies of sex differences in simple associative learning? You imply these have been much more thoroughly studied than conditional discriminations.

We added a few references as suggested.

What is the rationale for studying stress?

Stressful life events exacerbate several mental illnesses, potentially by impacting cognitive functions.

Although the (sex-dependent) effects of stress on some cognitive function are well established (e.g. working memory, selective attention, spatial navigation), the effect of stress on contextual modulation (a core dysfunction in certain mental illnesses) --and the possible sex-differences in this effect-- had not been formally tested. We added a few sentences in the results section (at the beginning of the stress section) to remind the reminder of why we tested the effect of stress in this task.

Method/Results:

Cues are not counterbalanced; the feature is visual and targets are auditory - this should be noted as a limitation in the discussion section.

We now acknowledge this limitation in the discussion. Moreover we believe that the new terminology for the context —Light vs Dark— (instead of A vs. noA in the original version) makes it abundantly clear that the “context” is this study was always visual.

Summation is invoked to describe the discrimination with different outcomes, how is summation happening? This is not described. Perhaps incorporate the literature on conditional discriminations with differential outcomes (the "differential outcomes effect").

We have edited the Result + Discussion section to clarify how summation might contribute to discrimination with different outcomes. We have also added references for the DOE in this task.

The stress effect is confounded with test order; comparing stress vs. baseline.

Sorry we don’t understand this point. The “baseline” refers to the animal’s performance on the last training session before the acute stress manipulation (we have edited the text to make this clear). Animals are first trained in the task and then we examine how stress alters their performance in this learned task. We don’t see how this could induce a test order confound.

Throughout the results section, it would be helpful to have the number of animals reported for each analysis.

The number of animals for each part of the experiment is now reported in the text, as well as in the figures.

Discussion:

"For Ctx-dep. O1, context is an occasion-setter, i.e. a stimulus that hierarchically modulates the associative strength between a target cue and its outcome." This is inaccurate. Occasion setters do not change or modulate the associative strength of a target cue. They modulate whether excitation or inhibition is expressed.

We reworded the sentence as suggested: “For Ctx-dep. O1, context is an occasion-setter, i.e. a stimulus that modulates the response to a target cue”.

"Together, these results indicate that the sex differences observed here are not attributable to simple associative, motivational, working-memory, or attentional processes, but are specific to the neurocomputational operations required for the hierarchical, contextual control of behavior." It should be noted here that the difference is one of degree, a quantitative difference, but not a difference in the qualitative features of the process.

"Regardless of the precise mechanism, our results indicate that, compared to male rats, females ultimately achieved more stable contextual control over cued reward-seeking; their behavior remained context-regulated under stress or after recent rewards." Again this is a matter of degree.

We absolutely agree. All the sex-difference reported here are a matter of degree. In the framework of McCarthy et al. (2012) the reported effects are type 2 or type 3 sex differences, not type 1 sexual dimorphism. We made a few edits in the Discussion to clarify this point.

Procedure:

Please clarify the percentage of trials that were reinforced in the No Discrimination group.

From session 1-32 (acquisition period), 50% of the trials were reinforced. Following this acquisition period, only 25% of the trials were reinforced to match all the other groups. We have edited the method section to clarify this point.

Please provide the dimensions of the restraint tubes and the model number if available.

This information is now included.

References

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Delamater AR, Garr E, Lawrence S, Whitlow JW (2017) Elemental, configural, and occasion setting mechanisms in biconditional and patterning discriminations. Behav Processes 137:40–52.

El-Amamy H, Holland PC (2007) Dissociable effects of disconnecting amygdala central nucleus from the ventral tegmental area or substantia nigra on learned orienting and incentive motivation. Eur J Neurosci 25:1557–1567.

Esber GR, Torres-Tristani K, Holland PC (2015) Amygdalo-striatal interaction in the enhancement of stimulus salience in associative learning. Behav Neurosci 129:87–95.

Gardner MPH, Conroy JS, Shaham MH, Styer CV, Schoenbaum G (2017) Lateral Orbitofrontal Inactivation Dissociates Devaluation-Sensitive Behavior and Economic Choice. Neuron 96:1192–1203.e4.

Holland PC (1977) Conditioned stimulus as a determinant of the form of the Pavlovian conditioned response. J Exp Psychol Anim Behav Process 3:77–104.

Holland PC (1980) CS-US interval as a determinant of the form of Pavlovian appetitive conditioned responses. J Exp Psychol Anim Behav Process 6:155–174.

Holland PC (2000) Trial and intertrial durations in appetitive conditioning in rats. Anim Learn Behav 28:121–135.

Holland PC (2016a) Enhancing second-order conditioning with lesions of the basolateral amygdala. Behav Neurosci 130:176–181.

Holland PC (2016b) Effects of amygdala lesions on overexpectation phenomena in food cup approach and autoshaping procedures. Behav Neurosci 130:357–375.

Kang M, Reverte I, Volz S, Kaufman K, Fevola S, Matarazzo A, Alhazmi FH, Marquez I, Iordanova MD, Esber GR (2021) Agency rescues competition for credit assignment among predictive cues from adverse learning conditions. Sci Rep 11:16187.

Keiflin R, Pribut HJ, Shah NB, Janak PH (2019) Ventral tegmental dopamine neurons participate in reward identity predictions. Curr Biol 29:93–103.e3.

Kuchibhotla KV, Hindmarsh Sten T, Papadoyannis ES, Elnozahy S, Fogelson KA, Kumar R, Boubenec Y, Holland PC, Ostojic S, Froemke RC (2019) Dissociating task acquisition from expression during learning reveals latent knowledge. Nat Commun 10:2151.

Maes EJP, Sharpe MJ, Usypchuk AA, Lozzi M, Chang CY, Gardner MPH, Schoenbaum G, Iordanova MD (2020) Causal evidence supporting the proposal that dopamine transients function as temporal difference prediction errors. Nat Neurosci 23:176–178.

McCarthy MM, Arnold AP, Ball GF, Blaustein JD, De Vries GJ (2012) Sex differences in the brain: the not so inconvenient truth. J Neurosci 32:2241–2247.

Olshavsky ME, Song BJ, Powell DJ, Jones CE, Monfils M-H, Lee HJ (2013) Updating appetitive memory during reconsolidation window: critical role of cue-directed behavior and amygdala central nucleus. Front Behav Neurosci 7:186.

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Schiffino FL, Holland PC (2016) Secondary visual cortex is critical to the expression of surprise-induced enhancements in cue associability in rats. Eur J Neurosci 44:1870–1877.

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eLife assessment

This important study shows that a high autism quotient in neurotypical adults is associated with suboptimal motor planning and visual updating after eye movements, suggesting a disrupted efference copy mechanism. The implication is that abnormal visuomotor updating may contribute to sensory overload - a key symptom in autism spectrum disorder. The evidence presented is convincing, with few limitations, and should be of broad interest to neuroscientists at large.

Reviewer #1 (Public Review):

Summary:

This study examines a hypothesized link between autism symptomatology and efference copy mechanisms. This is an important question for a number of reasons. Efference copy is both a critical brain mechanism that is key to rapid sensorimotor behaviors, and one that has important implications for autism given recent empirical and theoretical work implicating atypical prediction mechanisms and atypical reliance on priors in ASD.<br /> The authors test this relationship in two different experiments, both of which show larger errors/biases in spatial updating for those with heightened autistic traits (as measured by AQ in neurotypical (NT) individuals).

Strengths:

The empirical results are convincing - effects are strong, sample sizes are sufficient, and the authors also rule out alternative explanations (ruling out differences in motor behavior or perceptual processing per se).

Weaknesses:

My main residual concern is that the paper should be more transparent about both (1) that this study does not include individuals with autism, and (2) acknowledging the limitations of the AQ.<br /> On the first point, and I don't think this is intentional, there are several instances where the line between heightened autistic traits in the NT population and ASD is blurred or absent. For example, in the second sentence of the abstract, the authors state "Here, we examine the idea that sensory overload in ASD may be linked to issues with efference copy mechanisms". I would say this is not correct because the authors did not test individuals with ASD. I don't see a problem with using ASD to motivate and discuss this work, but it should be clear in key places that this was done using AQ in NT individuals.<br /> For the second issue, the AQ measure itself has some problems. For example, reference 38 in the paper (a key AQ paper) also shows that the AQ is skewed more male than modern estimates of ASD, suggesting that the AQ may not fully capture the full spectrum of ASD symptomatology.<br /> Of course, this does not mean that the AQ is not a useful measure (the present data clearly show that it captures something important about spatial updating during eye movements), but it should not be confused with ASD, and its limitations need to be acknowledged. My recommendation would be to do this in the title as well - e.g. note impaired visuomotor updating in individuals with "heightened autistic traits".

Suggestions for improvement:<br /> - Figure 5 is really interesting. I think it should be highlighted a bit more, perhaps even with a model that uses the results of both tasks to predict AQ scores.<br /> - Some discussion of the memory demands of the tasks will be helpful. The authors argue that memory is not a factor, but some support for this is needed.<br /> - With 3 sessions for each experiment, the authors also have data to look at learning. Did people with high AQ get better over time, or did the observed errors/biases persist throughout the experiment?

Reviewer #2 (Public Review):

Summary:

The idea that various clinical conditions may be associated, at least partially, with a disrupted corollary discharge mechanism has been present for long. In this paper, the authors draw a link between sensory overload, a characteristic of autism spectrum disorder, and a disturbance in the corollary discharge mechanism. The authors substantiate their hypothesis with strong evidence from both the motor and perceptual domains. As a result, they broaden the clinical relevance of the corollary discharge mechanism to encompass autism spectrum disorder.

Public comments:

The authors write:

"Imagine a scenario in which you're watching a video of a fast-moving car on a bumpy road. As the car hits a pothole, your eyes naturally make quick, involuntary saccades to keep the car in your visual field. Without a functional efference copy system, your brain would have difficulty accurately determining the current position of your eye in space, which in turn affects its ability to anticipate where the car should appear after each eye movement."

I appreciate the use of examples to clarify the concept of efference copy. However, I believe this example is more related to a gain-field mechanism, informing the system about the position of the eye with respect to the head, rather than an example of efference copy per-se.

Without an efference copy mechanism, the brain would have trouble to accurately determine where the eyes will be in space after an eye movement, and it will have trouble predicting the sensory consequences of the eye movement. But it can be argued that the gain-field mechanism would be sufficient to inform the brain about the current position of the eyes with respect the head.

The authors write:

"In the double-step paradigm, two consecutive saccades are made to briefly displayed targets 21,22. The first saccade occurs without visual references, relying on internal updating to determine the eye's position."

Maybe I am missed something, but in the double-step paradigm the first saccade can occur without the help of visual references if no visual feedback is present, that is, when saccades are performed in total darkness. Was this the case for this experiment? I could not find details about room conditions in the methods. Please provide further details.<br /> In case saccades were not performed in total darkness, then the first saccade can be based on the remembered location of the first target presented, which can be derived from the retinotopic trace of the first stimuli, as well as contribution from the surroundings, that is: the remembered relative location of the first target with respect to the screen border along the horizontal meridian (i.e. allocentric cues)<br /> A similar logic could be applied to the second saccade. If the second saccade were based only on the retinotopic trace, without updating, then it would go up and 45 deg to the right, based on the example shown in Figure 1. With appropriate updating, the second saccade would go straight up. However, if saccades were not performed in total darkness, then the location of the second target could also be derived from its relationship with the surroundings (for example, the remembered distance from screen borders, i.e. allocentric cues).<br /> If saccades were not performed in total darkness, the results shown in Figures 2 and 3 could then be related to: i) differences in motor updating between AQ score groups; ii) differences in the use of allocentric cues between AQ score groups; iii) a combination of i) and ii). I believe this is a point worth mentioning in the discussion."

The authors write:

"According to theories of saccadic suppression, an efference copy is necessary to predict the occurrence of a saccade."

I would also refer to alternative accounts, where saccadic suppression appears to arise as early as the retina, due to the interaction between the visual shift introduced by the eye movement, and the retinal signal associated with the probe used to measure saccadic suppression. This could potentially account for the scaling of saccadic suppression magnitude with saccade amplitude.

Idrees, S., Baumann, M.P., Franke, F., Münch, T.A. and Hafed, Z.M., 2020. Perceptual saccadic suppression starts in the retina. Nature communications, 11(1), p.1977.

Reviewer #3 (Public Review):

Summary:

This work examined efference copy related to eye movements in healthy adults who have high autistic traits. Efference copies allow the brain to make predictions about sensory outcomes of self-generated actions, and thus serve important roles in motor planning and maintaining visual stability. Consequently, disrupted efference copies have been posited as a potential mechanism underlying motor and sensory symptoms in psychopathology such as Autism Spectrum Disorder (ASD), but so far very few studies have directly investigated this theory. Therefore, this study makes an important contribution as an attempt to fill in this knowledge gap. The authors conducted two eye-tracking experiments examining the accuracy of motor planning and visual perception following a saccade, and found that participants with high autistic traits exhibited worse task performance (i.e., less accurate second saccade and biased perception of object displacement), consistent with their hypothesis of less impact of efference copies on motor and visual updating. Moreover, the motor and visual biases are positively correlated, indicative of a common underlying mechanism. These findings are promising and can have important implications for clinical intervention, if they can be replicated in a clinical sample.

Strengths:

The authors utilized well-established and rigorously designed experiments and sound analytic methods. This enables easy translations between similar work in non-human primates and humans and readily points to potential candidates for underlying neural circuits that could be further examined in follow-up studies (e.g., superior colliculus, frontal eye fields, mediodorsal thalamus). The finding of no association between initial saccade accuracy and level of autistic trait in both experiments also serves as an important control analysis and increases one's confidence in the conclusion that the observed differences in task performance were indeed due to disrupted efference copies, not confounding factors such as basic visual/motor deficits or issues with working memory. The strong correlation between the observed motor and visual biases further strengthens the claim that the findings from both experiments may be explained by the same underlying mechanism - disrupted efference copies. Lastly, the authors also presented a thoughtful and detailed mechanistic theory of how efference copy impairment may lead to ASD symptomatology, which can serve as a nice framework for more research into the role of efference copies in ASD.

Weaknesses:

Although the paper has a lot of strengths, the main weakness of the paper is that a direct link with sensory/motor symptoms cannot be established. As the authors have discussed, the most likely symptoms resulting from disrupted efference copies would be sensory overload and motor inflexibility. The measure used to quantify the level of autistic traits, Autistic Quotient (AQ), does not capture any sensory or motor characteristics of the Autism spectrum. Therefore, it is unknown whether those scored high on AQ in this study experienced high, or even any, sensory or motor difficulties. In other words, more evidence is needed to demonstrate a direct link between disrupted efference copies and sensory/motor symptoms in ASD.

Author response:

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

eLife assessment

This important study tests the hypothesis that a high autism quotient in neurotypical adults is strongly associated with suboptimal motor planning and visual updating after eye movements, which in turn, is related to a disrupted efference copy mechanism. The implication is that such abnormal behavior would be exaggerated in those with ASD and may contribute to sensory overload - a key symptom in this condition. The evidence presented is convincing, with significant effects in both visual and motor domains, adequate sample sizes, and consideration of alternatives. However, the study would be strengthened with minor but necessary corrections to methods and statistics, as well as a moderation of claims regarding direct application to ASD in the absence of testing such patients.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This study examines a hypothesized link between autism symptomatology and efference copy mechanisms. This is an important question for several reasons. Efference copy is both a critical brain mechanism that is key to rapid sensorimotor behaviors, and one that has important implications for autism given recent empirical and theoretical work implicating atypical prediction mechanisms and atypical reliance on priors in ASD.

The authors test this relationship in two different experiments, both of which show larger errors/biases in spatial updating for those with heightened autistic traits (as measured by AQ in neurotypical (NT) individuals).

Strengths:

The empirical results are convincing - effects are strong, sample sizes are sufficient, and the authors also rule out alternative explanations (ruling out differences in motor behavior or perceptual processing per se).

Weaknesses:

My main concern is that the paper should be more transparent about both (1) that this study does not include individuals with autism, and (2) acknowledging the limitations of the AQ.

On the first point, and I don't think this is intentional, there are several instances where the line between heightened autistic traits in the NT population and ASD is blurred or absent. For example, in the second sentence of the abstract, the authors state "Here, we examine the idea that sensory overload in ASD may be linked to issues with efference copy mechanisms". I would say this is not correct because the authors did not test individuals with ASD. I don't see a problem with using ASD to motivate and discuss this work, but it should be clear in key places that this was done using AQ in NT individuals.

For the second issue, the AQ measure itself has some problems. For example, reference 38 in the paper (a key paper on AQ) also shows that those with high AQ skew more male than modern estimates of ASD, suggesting that the AQ may not fully capture the full spectrum of ASD symptomatology. Of course, this does not mean that the AQ is not a useful measure (the present data clearly show that it captures something important about spatial updating during eye movements), but it should not be confused with ASD, and its limitations need to be acknowledged. My recommendation would be to do this in the title as well - e.g. note impaired visuomotor updating in individuals with "heightened autistic traits".

We thank the reviewer for the kind words. We now specify more carefully that our sample of participants consists of neurotypical adults scored for autistic traits and none of them was diagnosed with autism before participating in our experiment. Regarding the Autistic Quotient Questionnaire (AQ) on page 5 of the Introduction we now write:

“The autistic traits of the whole population form a continuum, with ASD diagnosis usually situated on the high end 31-33. Moreover, autistic traits share a genetic and biological etiology with ASD 34. Thus, quantifying autistic-trait-related differences in healthy people can provide unique perspectives as well as a useful surrogate for understanding the symptoms of ASD 31,35.”

In the Discussion (page 9) we now write:

”It is essential to note that our participant pool lacked pre-existing diagnoses before engaging in the experiments and we must address limitations associated with the AQ questionnaire. The AQ questionnaire demonstrates adequate test-retest reliability 36, normal distribution of sum scores in the general population 50, and cross-cultural equivalence has been established in Dutch and Japanese samples 51-53. The AQ effectively categorizes individuals into low, average, and high degrees of autistic traits, demonstrating sensitivity for both group and individual assessments 54.

However, evolving research underscores many aspects that are not fully captured by the self-administered questionnaire: for example, gender differences in ASD trait manifestation 55. Autistic females may exhibit more socially typical interests, often overlooked by professionals 56. Camouflaging behaviors, employed by autistic women to blend in, pose challenges for accurate diagnosis 57. Late diagnoses are attributed to a lack of awareness, gendered traits, and outdated assessment tools 58. Moving forward, complementing AQ evaluations in the general population with other questionnaires, such as those assessing camouflaging abilities 59, or motor skills in everyday situation (MOSES-test 60) becomes crucial for a comprehensive understanding of autistic traits.”

Suggestions for improvement:

- Figure 5 is really interesting. I think it should be highlighted a bit more, perhaps even with a model that uses the results of both tasks to predict AQ scores.

We thank the reviewer for the suggestion. However, the sample size is relatively small for building a robust and generalizable model to predict AQ scores. Statistical models built on small datasets can be prone to overfitting, meaning that they might not accurately predict the AQ for new individuals.

- Some discussion of the memory demands of the tasks will be helpful. The authors argue that memory is not a factor, but some support for this is needed. 

The reviewer raises an important point regarding the potential for memory demands to influence our results. We have now also investigated the accuracy of the second saccade separately for the x and y dimension. As also shown in figure 3 panel A, a motor bias was observed only in one dimension (x), weaking the argument of memory which would imply a bias in both directions (participants remembering the position of the target relative to both screen borders for example). We performed a t-test between our subsample of participants and indeed we found a difference in saccade accuracy for the x dimension (p = 0.03) but not in the y dimension (p = 0.88).

We now add these analyses in Discussion on page 8.

- With 3 sessions for each experiment, the authors also have data to look at learning. Did people with high AQ get better over time, or did the observed errors/biases persist throughout the experiment? 

We thank the reviewer for pointing this out. On page 7 (Results) we now write:

” Understanding how these biases might change over time could provide further insights into this mechanism. Specifically, we investigated whether participants exhibited any learning effects throughout the experiments. For data of Experiment 1 – motor updating – we divided our data into 10 separate bins of 30 trials each. We conducted a repeated measure ANOVA with the within-subject factor “number of sessions” (two main sessions of 5 bins each, ~150 trials) and the between-subject factor “group” (lower vs upper quartile of the AQ distribution). We found no main effect of “number of sessions” (F(1,7) = 0.25, p = 0.66), a main effect of “group” (F(1,7) = 2.52, p = 0.015), and no interaction between the two subsample of participants and the sessions tested (F(1,7) = 0.51, p = 0.49). Data of Experiment 2 – visual updating– were separated into 3 sessions. For each session we extracted the PSE and we conducted a repeated measure ANOVA with within subject factor “sessions” and between subject factor “groups” (lower vs upper quartile of the AQ distribution). Also here we found no main effect of sessions (F(1,13) = 0.86, p = 0.39), a main effect of group (F(1,14) = 11.85, p = 0.004), and no interaction between the two subsample of participants and the sessions tested (F(1,13) = 0.20, p = 0.73). In conclusion, the current study found no evidence of learning effects across the experimental sessions. However, a significant main effect of group was observed in both Experiment 1 (motor updating) and Experiment 2 (visual updating). Participants in the group with higher autistic traits performed systematically differently on the task, regardless of the number of sessions completed compared to those in the group with lower autistic traits.”

Reviewer #2 (Public Review):

Summary:

The idea that various clinical conditions may be associated, at least partially, with a disrupted corollary discharge mechanism has been present for a long time.

In this paper, the authors draw a link between sensory overload, a characteristic of autism spectrum disorder, and a disturbance in the corollary discharge mechanism. The authors substantiate their hypothesis with strong evidence from both the motor and perceptual domains. As a result, they broaden the clinical relevance of the corollary discharge mechanism to encompass autism spectrum disorder.

The authors write:

"Imagine a scenario in which you're watching a video of a fast-moving car on a bumpy road. As the car hits a pothole, your eyes naturally make quick, involuntary saccades to keep the car in your visual field. Without a functional efference copy system, your brain would have difficulty accurately determining the current position of your eye in space, which in turn affects its ability to anticipate where the car should appear after each eye movement."

I appreciate the use of examples to clarify the concept of efference copy. However, I believe this example is more related to a gain-field mechanism, informing the system about the position of the eye with respect to the head, rather than an example of efference copy per se.

Without an efference copy mechanism, the brain would have trouble accurately determining where the eyes will be in space after an eye movement, and it will have trouble predicting the sensory consequences of the eye movement. However it can be argued that the gain-field mechanism would be sufficient to inform the brain about the current position of the eyes with respect to the head. 

We now used a different example. And on page 3 of Introduction, we now write:

“During a tennis game, rapid oculomotor saccades are employed to track the high-velocity ball across the visual display. In the absence of a functional efference copy mechanism, the brain would encounter difficulty in anticipating the precise retinal location of the ball following each saccade. This could result in a transient period of visual disruption as the visual system adjusts to the new eye position. The efference copy, by predicting the forthcoming sensory consequences of the saccade, would bridge this gap and facilitate the maintenance of a continuous and accurate representation of the ball's trajectory.”

The authors write:

"In the double-step paradigm, two consecutive saccades are made to briefly displayed targets 21, 22. The first saccade occurs without visual references, relying on internal updating to determine the eye's position."

Maybe I have missed something, but in the double-step paradigm the first saccade can occur without the help of visual references if no visual feedback is present, that is, when saccades are performed in total darkness. Was this the case for this experiment? I could not find details about room conditions in the methods. Please provide further details.

In case saccades were not performed in total darkness, then the first saccade can be based on the remembered location of the first target presented, which can be derived from the retinotopic trace of the first stimuli, as well as the contribution from the surroundings, that is: the remembered relative location of the first target with respect to the screen border along the horizontal meridian (i.e. allocentric cues).

A similar logic could be applied to the second saccade. If the second saccade were based only on the retinotopic trace, without updating, then it would go up and 45 deg to the right, based on the example shown in Figure 1. With appropriate updating, the second saccade would go straight up. However, if saccades were not performed in total darkness, then the location of the second target could also be derived from its relationship with the surroundings (for example, the remembered distance from screen borders, i.e. allocentric cues).

If saccades were not performed in total darkness, the results shown in Figures 2 and 3 could then be related to i) differences in motor updating between AQ score groups; ii) differences in the use of allocentric cues between AQ score groups; iii) a combination of i) and ii). I believe this is a point worth mentioning in the discussion." 

Thank you for raising the important issue of visual references in the double-step saccade task. Participants performed saccades in a dimly lit room where visual references, i.e. the screen borders, were barely visible. At the time we collected the data a laboratory that allowed performing experiments in complete darkness was not at our disposal. We acknowledge the possibility that participants could have memorized the target locations relative to the screen borders. The bias of high AQ participants could then be attributed to differences in either encoding, memorization or decoding of the target location relative to the screen borders. However, the potentially abnormal use of visual references must reflect an altered remapping process since we did not find differences in saccade landing in the vertical dimension. A t-test between our group of participants revealed a difference in saccade accuracy for the x dimension (p = 0.03) but not in the y dimension (p = 0.88). We thus agree that in addition to an altered efference copy signal in high AQ participants, altered use of visual references might also affect their saccadic remapping.

In Discussion we now write: “Our findings suggest that a general memory deficit is unlikely to fully explain the observed bias in high-AQ participants' second saccades. As highlighted in Figure 3A, the bias was specific to the horizontal dimension, weakening the argument for a global memory issue affecting both vertical and horizontal encoding of target location. However, it's important to acknowledge that even under non-darkness conditions, participants might rely on a combination of internal updating based on the initial target location and visual cues from the environment, such as screen borders. This potential use of visual references could contribute to the observed bias in the high-AQ group. If high-AQ participants differed in their reliance on visual cues compared to the low-AQ group, it could explain the specific pattern of altered remapping observed in the horizontal dimension. This possibility aligns with our argument for an abnormal remapping process underlying the results. While altered efference copy signals remain a strong candidate, the potential influence of visual cues on remapping in this population warrants further investigation. Future studies could incorporate a darkness condition to isolate the effects of internal updating on the first saccade, and systematically manipulate the availability of visual cues throughout the task. This would allow for a more nuanced understanding of how internal updating and visual reference use interact in the double-step paradigm, particularly for individuals with varying AQ scores “.

The authors write:

According to theories of saccadic suppression, an efference copy is necessary to predict the occurrence of a saccade."

I would also refer to alternative accounts, where saccadic suppression appears to arise as early as the retina, due to the interaction between the visual shift introduced by the eye movement, and the retinal signal associated with the probe used to measure saccadic suppression. This could potentially account for the scaling of saccadic suppression magnitude with saccade amplitude.

Idrees, S., Baumann, M.P., Franke, F., Münch, T.A. and Hafed, Z.M., 2020. Perceptual saccadic suppression starts in the retina. Nature communications, 11(1), p.1977. 

We thank the reviewer. Now on page 4 of Introduction we write:

“Some theories consider saccadic omission and saccadic suppression as resulting from an active mechanism. In this view an efference copy would signal the occurrence of a saccade, yielding a transient decrease in visual sensitivity20-22. Others however have pointed out the possibility that a purely passive mechanism suffices to induce saccadic omission23. A recent study has found evidence for saccadic suppression already in the retina. Idrees et al.24 demonstrated that retinal ganglion cells in isolated retinae of mice and pigs respond to saccade-like displacements, leading to the suppression of responses to additional flashed visual stimuli through visually triggered retinal-circuit mechanisms. Importantly, their findings suggest that perisaccadic modulations of contrast sensitivity may have a purely visual origin, challenging the need for an efference copy in the early stages of saccadic suppression. However, the suppression they measured lasted much longer than time-courses observed in behavioral data. An efference copy signal could thus be necessary to release perception from suppression.”

Reviewer #3 (Public Review): 

Summary:

This work examined efference copy related to eye movements in healthy adults who have high autistic traits. Efference copies allow the brain to make predictions about sensory outcomes of self-generated actions, and thus serve important roles in motor planning and maintaining visual stability. Consequently, disrupted efference copies have been posited as a potential mechanism underlying motor and sensory symptoms in psychopathology such as Autism Spectrum Disorder (ASD), but so far very few studies have directly investigated this theory. Therefore, this study makes an important contribution as an attempt to fill in this knowledge gap. The authors conducted two eye-tracking experiments examining the accuracy of motor planning and visual perception following a saccade and found that participants with high autistic traits exhibited worse task performance (i.e., less accurate second saccade and biased perception of object displacement), consistent with their hypothesis of less impact of efference copies on motor and visual updating. Moreover, the motor and visual biases are positively correlated, indicative of a common underlying mechanism. These findings are promising and can have important implications for clinical intervention if they can be replicated in a clinical sample.

Strengths:

The authors utilized well-established and rigorously designed experiments and sound analytic methods. This enables easy translations between similar work in non-human primates and humans and readily points to potential candidates for underlying neural circuits that could be further examined in follow-up studies (e.g., superior colliculus, frontal eye fields, mediodorsal thalamus). The finding of no association between initial saccade accuracy and level of autistic trait in both experiments also serves as an important control analysis and increases one's confidence in the conclusion that the observed differences in task performance were indeed due to disrupted efference copies, not confounding factors such as basic visual/motor deficits or issues with working memory. The strong correlation between the observed motor and visual biases further strengthens the claim that the findings from both experiments may be explained by the same underlying mechanism - disrupted efference copies. Lastly, the authors also presented a thoughtful and detailed mechanistic theory of how efference copy impairment may lead to ASD symptomatology, which can serve as a nice framework for more research into the role of efference copies in ASD.

Weaknesses:

Although the paper has a lot of strengths, the main weakness of the paper is that a direct link with ASD symptoms (i.e., sensory overload and motor inflexibility as the authors suggested) cannot be established. First of all, the participants are all healthy adults who do not meet the clinical criteria for an ASD diagnosis. Although they could be considered a part of the broader autism phenotype, the results cannot be easily generalized to the clinical population without further research. Secondly, the measure used to quantify the level of autistic traits, Autistic Quotient (AQ), does not actually capture any sensory or motor symptoms of ASD. Therefore, it is unknown whether those who scored high on AQ in this study experienced high, or even any, sensory or motor difficulties. In other words, more evidence is needed to demonstrate a direct link between disrupted efference copies and sensory/motor symptoms in ASD.

This is a valid point, and we thank the reviewer for raising it up. Moving forward, complementing AQ evaluations in the general population with other questionnaires, such as those assessing camouflaging abilities (Hull, L., Mandy, W., Lai, MC., et al., 2019), or motor skills in everyday situation (MOSES-test, Hillus J, Moseley R, Roepke S, Mohr B. 2019 ) becomes crucial for a comprehensive understanding of autistic traits.”

We now address this point in Discussion page 9.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Minor comments

- The pothole example in the introduction was really hard to follow. I wonder if there is a better example. 

We now used a different example. And on page 3 of Introduction, we now write:

“During a tennis game, rapid oculomotor saccades are employed to track the high-velocity ball across the visual display. In the absence of a functional efference copy mechanism, the brain would encounter difficulty in anticipating the precise retinal location of the ball following each saccade. This could result in a transient period of visual disruption as the visual system adjusts to the new eye position. The efference copy, by predicting the forthcoming sensory consequences of the saccade, would bridge this gap and facilitate the maintenance of a continuous and accurate representation of the ball's trajectory.”

- This is really minor; I would say that saccades are not the most frequent movement that humans perform. Some of the balance-related adjustments and even heartbeats are faster. Maybe just add "voluntary". 

We thank the reviewer for the suggestion, now added.

- "Severe consequences" on page 4 is a bit strong. If that were true, there would be pretty severe impairments in eye movement behavior in ASD, which I don't think is the case.

We agree with the reviewer. We now eliminated the term “severe”.

- The results section would read better if each experiment had a short paragraph reiterating its overall goal and the specific approach each experiment took to achieve that goal. 

Now on page 5, for the first experiment, we write:

”We investigated the influence of autistic traits on visual updating during saccadic eye movements using a classic double-step saccade task. This task relies on participants making two consecutive saccades to briefly presented targets. The accuracy of the second saccade serves as an indirect measure of how effectively the participant's brain integrated the execution of the first saccade into their internal representation of visual space. Participants were divided into quartiles based on the severity of their autistic traits, as assessed by the Autistic quotient questionnaire (cite). We hypothesized that individuals with higher autistic traits would exhibit greater difficulty in visual updating compared to those with lower autistic traits. This would be reflected in reduced accuracy of their second saccades in the double-step task. Figure 2C illustrates examples from participants at the extremes of the autistic trait distribution (Autistic quotient = 3, in orange and Autistic quotient = 31, in magenta). As shown, both participants were instructed to make saccades to the locations indicated by two brief target appearances (T1 and T2), as quickly and accurately as possible, following the order of presentation. However, successful execution of the second saccade requires accurate internal compensation for the first saccade, without any visual references or feedback available during the saccade itself.”

On page 6, for experiment 2, we write:

”With a trans-saccadic localization task, we explored how autistic traits affect the integration of eye movements into visual perception. Participants were presented with stimuli before and after a single saccade, creating an illusion of apparent motion. We measured the perceived direction of this displacement, which is influenced by how well the participant's brain accounts for the saccadic eye movement. We predicted that individuals with higher autistic traits would show a stronger bias in the perceived displacement direction, suggesting a less accurate integration of the eye movement into their visual perception.”

- On page 6, the text about "vertical displacement" is confusing. The spatial displacements in this experiment were horizontal? 

Yes, they were. The spatial displacement is horizontal, but the perceived trajectory (due to the saccade) is vertical. We now changed “vertical displacement” to “vertical trajectory”.

- Page 6, grammatical problems in "while we report a slightly slant of the dots trajectory". 

Thank you. Now fixed.

- It would be helpful to discuss the apparent motion part of Experiment 2 in the main text. This important part is not made clear. 

We now in Introduction, page 4, write:

“In this paradigm, one stimulus is shown before and another after saccade execution. Together these two stimuli produce the perception of “apparent motion”. If stimuli are placed such that the apparent motion path is orthogonal to the saccade path, then the orientation of the apparent motion path indicates how the saccade vector is integrated into vision. The apparent motion trajectory can only appear vertical if the movement of the eyes is perfectly accounted for, that is the retinotopic displacement is largely compensated, ensuring spatial stability. However, small biases of motion direction – implying under- (or over-) compensation of the eye movement – can indicate relative failures in this stabilization process. In a seminal study, Szinte and Cavanagh 27 found a slight over-compensation of the saccade vector leading to apparent motion slightly tilted against the direction of the saccade. More importantly, when efference copies are not available, i.e. localization occurring at the time of a second saccade in a double step task, a strong saccade under-compensation occurs 28.

This phenomenon cannot be explained by perisaccadic mislocalization of flashed visual stimuli 29,30, but the two phenomena may be related in that they may both depend upon efference copy information.”

- Figure 1 could be improved. For example, the text talks about the motor plan, but this is not clearly shown in the figure.

We now added the motor plan into the model. Thank you.

- Figure 2A, the scale is off (the pictures make it look like the horizontal movement was longer than the vertical). 

Now fixed.

- Figure 4, it would be helpful if the task was also described in the figure. 

We thank the reviewer for the comment. We now tried to modify the figure by also adding the perceptual judgment task.

- Figure 5A, the y-axis shows p(correct), but that is not what the y-axis shows (the legend makes the same mistake). 

We apologize, it’s the proportion of time participants reported the second dot to be more to the right compared to the first one. We now changed the figure and the text accordingly.

- A recent study on motion and eye movement prediction in ASD is very relevant to the work presented here.: Park et al. (2021). Atypical visual motion-prediction abilities in autism spectrum disorder. Clinical Psychological Science, 9(5), 944-960.

Indeed. We now refer to the cited study in Discussion, on page 9.

Reviewer #2 (Recommendations For The Authors):

Statistics and plotting.

I believe some of the reported statistics are not clear. For example, the authors write:

"Saccade landing positions of participants in the lower quartile (mean degree {plus minus} SEM: 10.17{plus minus} 0.50) did not deviate significantly from those in the upper quartile (mean degree {plus minus} SEM: 9.65 {plus minus} 0.77). This result was also confirmed by a paired sample t-test (t(7) = 0.66; p = 0.66, BF10 = 0.40)"

Maybe I am missing something, but why use a paired-sample t-test when the upper and lower quartiles constitute different groups of participants? Shouldn't a two-sample t-test be used in this case?

We apologize for the confusion. It is indeed a two-sample t-test.

Along the same lines, I do not understand the link between the number of degrees of freedom reported in the t-test (7) and the number of participants reported in the study (41).

This is also evident when looking at the scatterplot in Figure 3C. How many participants formed the averages and standard errors reported in Figures 3B and 3D? Please clarify.

I have the same comment(s) also for the visual updating task (and related figures), where 13 degrees of freedom are reported in the t-tests. Please clarify. 

We thank the reviewer for pointing this out. The number of participants reported in the scatter plots were indeed 42.  However, we opted to compare the averages only in the lower and upper quartile of the AQ distribution to avoid dealing with a median split (which would imply a skewed distribution). Of our sample of participants in Exp1, 8 fell into the lower quartile of the AQ distribution and 8 in the upper quartile (14 deg of freedom); from Exp 2, 8 participants fell in the lower and 7 in the upper (13 deg of freedom).

We now fixed the values accordingly.

Reviewer #3 (Recommendations For The Authors):

(1) The language can be a bit misleading (especially the title and abstract) as it wasn't always clear that the participants don't actually have clinical ASD. I'd suggest avoiding using words like "symptom" as that would indicate clinical severity, and using words like "traits/characteristics" instead for more precise language. 

We apologize for the misleading terminology used. Now fixed.

(2) In the Intro: "...perfect compensation results in a vertical trajectory, while small biases indicate stabilization issues23-25." This is a bit confusing without knowing the details of the paradigm. Consider clarifying or at least referring to Figure 4. 

Thank you.

(3) In the Results: "This result was also confirmed by a paired sample t-test (t(7) = 0.66;..." This is confusing as a two-sample t-test is the appropriate test here. Also, the degree of freedom seems very low - could the authors clarify how many participants are in each subgroup (i.e., low vs. high AQ quartile), for both experiments? 

Of our sample of participants in Exp1 8 fell into the lower quartile of the AQ distribution and 8 in the upper quartile (14 deg of freedom); from Exp 2, 8 participants fell in the lower and 7 in the upper (13 deg of freedom).

(4) In the Methods: Experiment 2: "The first dot could appear randomly above or below gaze level at a fixed horizontal location, halfway between the two fixations (x = 0, y = -5{degree sign} or +5{degree sign} depending on the trial). The second dot was then shown orthogonal to the first one at a variable horizontal location (x = 5{degree sign} {plus minus} 2.5{degree sign})." This would mean that the position of the 2nd dot relative to the 1st one would be 2.5{degree sign}- 7.5{degree sign}, but the task description in Results and Figure 5A would suggest the horizontal location of the second dot is x = 0{degree sign} {plus minus} 2.5{degree sign}. Which one is correct? 

The second option is the correct one. We now fixed the typo in the Methods part.

(5) There is another study that examined oculomotor efference copies in children with ASD using a similar trans-saccadic perception task (Yao et al., 2021, Journal of Vision). In that study, they found a correlation between task performance and an ASD motor symptom (repetitive behavior). This seems quite relevant to the authors' hypothesis and discussion. 

We thank the reviewer for the suggestion. We now added the mentioned paper in the discussion.

(6) Please proofread the entire paper carefully as there were multiple grammatical and spelling errors.

Thank you.

eLife assessment

This study offers a useful advance by introducing a cord blood DNA methylation score for maternal smoking effects, with the inclusion of cohorts from diverse backgrounds. However, the overall strength of evidence is deemed incomplete, due to concerns regarding low exposure levels and low statistical power, which hampers the generalisability of their findings. The study provides an interesting basis for future studies, but would benefit from the addition of more cohorts to validate the findings and a focus on more diverse health outcomes.

Reviewer #2 (Public Review):

Summary:

The authors generated a DNA methylation score in cord blood for detecting exposure to cigarette smoke during pregnancy. They then asked if it could be used to predict height, weight, BMI, adiposity and WHR throughout early childhood.

Strengths:

The study included two cohorts of European ancestry and one of South Asian ancestry.

Weaknesses:

(1) Numbers of mothers who self-reported any smoking was very low likely resulting in underpowered analyses.

(2) Although it was likely that some mothers were exposed to second-hand smoke and/or pollution, data on this was not available.

(3) One of the European cohorts and half of the South Asian cohort had DNA methylation measured on only 2500 CpG sites including only 125 sites previously linked to prenatal smoking.

Reviewer #3 (Public Review):

Summary:

Deng et al. assess neonatal cord blood methylation profiles and the association with (self-reported) maternal smoking in multiple populations, including two European (CHILD, FAMILY) and one South Asian (START), via two approaches: 1) they perform an independent epigenome-wide association study (EWAS) and meta-analysis across the CHILD and FAMILY cohort, during which they also benchmark previously reported maternal-smoking associated sites, and 2) they generate new composite methylation risk scores for maternal smoking, and assess their performance and association with phenotypic characteristics in the three populations, in addition to previously described maternal smoking methylation risk scores.

Strengths and weaknesses:

Their meta-analysis across multiple cohorts and comparison with previous findings represents a strength. In particular the inclusion of a South Asian birth cohort is commendable as it may help to bolster generalizability. However, their conclusions are limited by several important weaknesses:

(1) the low number of (self-reported) maternal smokers in particular their South Asian population, resulting in an inability to conduct benchmarking of maternal smoking sites in this cohort. As such, the inclusion of the START cohort in certain figures is not warranted (e.g., Figure 3) and the overall statement that smoking-associated MRS are portable across populations are not fully supported;<br /> (2) different methylation profiling tools were used: START and CHILD methylation profiles were generated using the more comprehensive 450K array while the FAMILY cohort blood samples were profiled using a targeted array covering only 3,000, as opposed to 450,000 sites, resulting in different coverage of certain sites which affects downstream analyses and MRS, and importantly, omission of potentially relevant sites as the array was designed in 2016 and substantial additional work into epigenetic traits has been conducted since then;<br /> (3) the authors train methylation risk scores (MRS) in CHILD or FAMILY populations based on sites that are associated with maternal smoking in both cohorts and internally validate them in the other cohort, respectively. As START cohort due to insufficient numbers of self-reported maternal smokers, the authors cannot fully independently validated their MRS, thus limiting the strength of their results.

Overall strength of evidence and conclusions:

Despite these limitations, the study overall does explore the feasibility of using neonatal cord blood for the assessment of maternal smoking. However, their conclusion on generalizability of the maternal smoking risk score is currently not supported by their data as they were not able to validate their score in a sufficiently large number of maternal smokers and never smokers of South Asian populations.

While their generalizability remains limited due to small sample numbers and previous studies with methylation risk scores exist, their findings may nonetheless provide the basis for future work into prenatal exposures which will be of interest to the research community. In particular their finding that the maternal smoking-associated MRS was associated with small birth sizes and weights across birth cohorts, including the South Asian birth cohort that had very few self-reported smokers, is interesting and the author suggest these findings could be associated with factors other than smoking alone (e.g., pollution), which warrant further investigation and would be highly novel.<br /> Future exploration should also include a strong focus on more diverse health outcomes, including respiratory conditions that may have long-lasting health consequences.

Author response:

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

We thank the reviewers for their time and the thoughtful reviews on our manuscript. The reviewers brought good points regarding the sample size, and the low exposure in the South Asian cohort owing to their unique cultural and social practices. We recognize these as limitations of the paper and discussed these in the revised version. In the revised manuscript, we have taken the key suggestions by reviewers to 1) better illustrate the analytical flow and statistical methods, in particular, to show which datasets had been used in discovery, validation, and testing of the score – as a main figure in the manuscript and in the graphical abstract; 2) demonstrate there is no possibility of overfitting in our approach using statistical metrics of performance; 3) emphasize the goal was not for discovery (e.g. our own EWAS was not used for deriving the score), but to compare with existing EWASs and contrast the results from the white European and SA populations; 4) and supplement the analysis with previously derived maternal smoking, smoking and air pollution methylation score and to explore additional health outcomes in relation to lung health in newborns. Finally, we would also like to take this opportunity to re-iterate that it was not our objective to derive the most powerful methylation score of smoking nor to demonstrate the causal role of maternal smoking on birth weight via DNAm. We have restructure the manuscript as well as the discussion to clarify this. Please find below a point-by-point response to the comments below.

Reviewer #1:

The manuscript could benefit from a more detailed description of methods, especially those used to derive MRS for maternal smoking, which appears to involve overfitting. In particular, the addition of a flow chart would be very helpful to guide the reader through the data and analyses. The FDR correction in the EWAS corresponds to a fairly liberal p-value threshold. 

We thank the reviewer for these good suggestions. In the revised manuscript, we have provided a flow chart as the new Figure 1, more detailed description of the method (added a subsection “Statistical analysis” under Materials and Methods) as well as metrics including measures of fit indices such as AUC and adjusted R2 for each validation and testing dataset to illustrate there is no danger of overfitting (in new Supplementary Table 5).

The choice of use FDR was indeed arbitrary as there has been no consensus on what significance threshold, if any, should be used in the context of EWAS. Here we simply followed the convention in previous studies to contrast the top associated signals for their effects between different populations and with reported effect sizes. Throughout the manuscript, we have removed the notion of significant associations and used the phrase “top associated signals” or “top associations” when discussion EWAS results for individual CpGs.

Reviewer #2:

(1) The number of mothers who self-reported any smoking was very low, much lower than in the general population and practically non-existent in the South Asian population. As a result, all analyses appeared to have been underpowered. It is possibly for this reason that the authors chose to generate their DNA methylation model using previously published summary statistics. The resulting score is not of great value in itself due to the low-powered dataset used to estimate covariance between CpG sites. In fact, a score was generated for a much larger, better-powered dataset several years ago (Reese, EHP, 2017, PMID 27323799). 

We thank the reviewer for pointing out the low exposure in the South Asian population, which we believe is complementary to the literature on maternal smoking that almost exclusively focused on white Europeans. However, the score was validating in the white European cohort (CHILD; current smoking 3.1%), which was reasonably similar to the trend that maternal cigarettes smoking is on the decline from 2016 to 2021, from 7.2% to 4.6% (Martin, Osterman, & Driscoll, 2023). This is also consistent with the fact that CHILD participants were recruited from major metropolitans of Canada with relatively high SES and education as compared to FAMILY.

We do agree with the reviewers that a higher prevalence of maternal smoking in the validating sample could potential improve the power of the score. Our original analytical pipeline focused on CHILD as the validation dataset; FAMILY (see the new Figure 1) was used as the testing data. We alternatively provided an analytical scheme using FAMILY as the validation dataset, as it had a higher proportion of current smokers, however, this is limited by the number of CpGs available (128 in FAMILY vs. 2,619 in CHILD out of the 2,620 CpGs from (Joubert et al., 2016)). The results of all possible combinations of validation vs. testing and restriction of targeted array vs. HM450 are summarized in the new new Supplementary Table 5 and Supplementary Figure 5.

To clarify, our choice to construct DNAm score using published summary statistics was not an ad-hoc decision due to the observed low power from CHILD EWAS. We agree with the reviewer that our study was indeed underpowered and was not originally intended for EWAS discovery. Thus, we specifically proposed to adopt a multivariate strategy from the literature of polygenic risk scores. This approach enabled us to leverage well-powered association signals without individual-level access to data with a sample size of n > 5,000 (Joubert et al., 2016). In comparison, the Reese maternal smoking score (Reese et al., 2017) had a discovery sample size of only n = 1,057. Our score was not out-performed, in fact, the AUC in both FAMILY (external validating dataset; n=411) and CHILD (external testing dataset; n=352) and was larger than that based on the Reese score as tabulated below (part of the new Supplementary Table 5).

Author response table 1.

Further, regarding the comment on the covariance matrix. Indeed, lassosum via elastic-net and summary data requires a reference covariance matrix that is consistent between the discovery data and external validation data. In fact, for moderately sized correlation/covariance values (r2 > 0.1), a sample size of >100 is sufficiently powered to detect it being different from 0 and thus used for estimation. Similar to the linkage disequilibrium of genotype data, the CpGs also exhibit a block-wise correlation structure and thus the theoretical framework of lassosum extends naturally to MRS.

In the revised manuscript, we included the Reese score, as well as a few additional scores to compare their predictiveness of smoking phenotypes in white European cohorts. We note that the applicability was limited in the FAMILY cohort that was profiled using a targeted array and only 7 out of 28 of the CpGs in the Reese score were available. As a result, though the Reese score had similar performance than our derived score in CHILD (0.94 vs. 0.95), its performance in FAMILY was compromised (0.72 vs. 0.89).

(2) The conclusion that "even minimal smoking exposure in South Asian mothers who were not active smokers showed a DNAm signature of small body size and low birthweight in newborns" is not warranted because no analyses were performed to show that the association between DNA methylation and birth size/weight was driven by maternal smoking. 

We thank the reviewer for this subtle point – it was not our intention to suggest there was a causal relationship between DNA methylation and birth size that was mediated by maternal smoking. We meant to suggest that the maternal smoking methylation score was consistently associated with negative outcomes in newborns of both white European and South Asian mothers despite no maternal smoking was present in South Asian mothers. It is possible that maternal smoking MRS was capturing a lot more than just smoking and second-hand smoking, such as other environmental exposures that also lead to oxidative stress. These together are associated with reduced birth size/weight.

In the revised manuscript, we have modified the conclusion above to:

“Notably, these results indicate a consistent association between the DNAm signature of maternal smoking and a small body size and low birthweight in newborns, in both white European mothers who exhibited some amount of smoking and in South Asian mothers who themselves were not active smokers.”

(3) Although it was likely that some mothers were exposed to second-hand smoke and/or pollution, data on this was either non-existent or not included in this study. Including this would have allowed a more novel investigation of the effects of smoke exposure on the pregnancies of non-smoking mothers.

We agree with this comment – second-hand smoking was captured by self-reported weekly smoking exposure by the mothers. We reported the association with smoking exposure and found that it was not consistently associated with our methylation scores across the cohorts (cohort specific association p-values of 5.4×10-5, 3.4×10-5, and 0.58, for CHILD, FAMILY, and START; original Table 3), possibly due to the low exposure in South Asian population (max weekly exposure was 42 hrs in contrast to 168 hrs in FAMILY and 98 hrs in CHILD). Meanwhile, air pollution data are currently not available. Here we additionally performed the association between maternal smoking and air pollution methylation score, using key CpGs from the largest air pollution EWAS to-date (Gondalia et al., 2021). However, there was no association between the air pollution score and any maternal smoking phenotypes (ps > 0.4).

(4) One of the European cohorts and half of the South Asian cohort had DNA methylation measured on only 2500 CpG sites. This set of sites included only 125 sites previously linked to prenatal smoking. The resulting model of prenatal smoking was small (only 11 CpG sites). It is possible that a large model may have been more powerful.

That is correct – also see our response to R2 comment #1. In our previous analysis, we validated two scores (one based on CpGs on the < 3,000 CpGs array and the other one for the full HM450K). The score with more CpGs indeed had slightly better performance. We included this as one of the limitations of the paper. Nevertheless, it does not impact the conclusion that the scores (based on a larger or smaller model) are transferrable to diverse populations and can be used to comparatively study the DNAm influence of maternal smoking in newborns.

The following was added in the discussion:

“First, the customized array with a limited number of CpGs (<3,000) was designed in 2016 and many large EWASs on smoking and maternal smoking conducted more recently had not been included.”

(5) The health outcomes investigated are potentially interesting but there are other possibly more important outcomes of interest such as birth complications, asthma, and intellectual impairment which are known to be associated with prenatal smoking.

We thank the reviewer for bring up this point. One of the key health outcomes in the CHILD study was asthma, and data at later time points are available. However, we do not have similar outcomes collected in the other two studies (FAMILY and START), which focused on cardiometabolic health in young children. Thus, we did not initially include outcomes that were not available across all cohorts as the intention was to contrast the effects between populations.

We recognize that this is an important question and decided to provide the association results for asthma and allergy at available time points in CHILD, FAMILY, and START. We also included mode of delivery via emergency C-section as an additional proxy outcome of birth complications. However, none of these were marginally (p < 0.05) associated with the DNAm smoking score. These are now included in the updated Supplementary Table 8.

Reviewer #1 (Recommendations For The Authors):

(1) The number of samples in the South Asian birth cohort given in the abstract (n = 887) does not match the sample size of the START cohort from the results section (results, page 7, line 139, n = 880). It is also different from the final analytical dataset size from the methods section (page 17, line 386, n = 890). Please clarify. 

We thank the reviewer for pointing this out. In the abstract, it was the final sample sized used for EWAS (no missingness in smoking history). The 880 in result was a typo for 890, which contains three individuals with missing smoking data. These have been updated with the correct sample size for START cohort that had full epigenome-wide methylation data (n = 504, and 503 with non-missing smoking history).

(2) Page 3, line 54: "consistent signal from the GFI1 gene (ps < 5×10-5)". Is ps a typo? If not then it might be clearer to state how many sites this included. 

No, these summarized the six CpG sites in the GFI1 gene as outlined in Table 2. We have clarified in the abstract to show the number of CpG sites included.

(3) Please report effect sizes together with information about the statistical significance (p values). 

We have updated the manuscript with (standardized) effect sizes whenever possible along with p-values.

(4) Page 4, line 80. This paragraph could be improved by adding a sentence explaining DNA methylation. 

We thank the reviewer for this suggestion. A sentence was included to introduce DNAm at the beginning of the second paragraph:

“DNA methylation is one of the most commonly studied epigenetic mechanisms by which cells regulate gene expression, and is increasingly recognized for its potential as a biomarker (13).”

(5) Page 4, line 84. Sentence difficult to understand, please rephrase: "Our recent systematic review of 17 cord blood epigenome-wide association studies (EWAS) demonstrated that out of the 290 CpG sites reported, 19 sites were identified in more than one study; all of them associated with maternal smoking". 

We have revised to clarify the review was on cord blood EWAS with five outcomes: maternal diabetes, pre-pregnancy body mass index, diet during pregnancy, smoking, and gestational age.

“Our recent systematic review of 17 cord blood epigenome-wide association studies (EWAS) found that out of the 290 CpG sites reported to be associated with at least one of the following: maternal diabetes, pre-pregnancy body mass index (BMI), diet during pregnancy, smoking, and gestational age, 19 sites were identified in more than one study and all of them associated with maternal smoking.”

(6) Page 5, line 93. The second part of the sentence is not necessary: "The majority of cohort studies have focused on participants of European ancestry, but few were designed to assess the influence of maternal exposures on DNA methylation changes in non-Europeans". 

We have revised accordingly to:

“Only a handful of cohort studies were designed to assess the influence of maternal exposures on DNA methylation changes in non-Europeans.”

(7) Page 5, line 95. "It has been suggested that ancestral background could influence both systematic patterns of methylation (27), such as cell composition and smoking behaviours (28)". The sentence is slightly unclear. Could it be rephrased to say that cell composition differences may be present by ancestry, which can lead to differential DNAm patterns? 

We have revised accordingly to:

“It has been suggested that systematic patterns of methylation (Elliott et al., 2022), such as cell composition, could differ between individuals of different ancestral backgrounds, which could in turn confound the association between differential DNAm and smoking behaviours (Choquet et al., 2021).”

(8) Page 5, line 108. How does reducing the number of predictors lead to more interpretable effect sizes? 

This was meant as a general comment in the context of variable selection, whereby the fewer predictors there are, the effect size of each predictor becomes more interpretable. However, we recognize this comment might be irrelevant to the specific approaches we adopted. We have revised it to motivate methylation score as a powerful instrument for analysis:

“Reducing the number of predictors and measurement noise in the data can lead to better statistical power and a more parsimonious instrument for subsequent analyses.”

(9) Page 5, line 112. Health consequences seem a bit strong, given that the analysis describes correlations/associations. 

We have revised it to “association with”:

“In this paper, we investigated the epigenetic signature of maternal smoking on cord blood DNA methylation in newborns, as well as its influence on newborn and later life outcomes in one South Asian which refers to people who originate from the Indian subcontinent, and two predominantly European-origin birth cohorts.”

Results

(10) It would be very helpful to have a flow diagram to detail all of your analyses.

We thank the reviewer for this suggestion. In the revised manuscript, we have provided a flow chart as the new Figure 1, updated the summary of analysis in . Table 3, and added a new Supplementary Table 5 for the DNAm score derivation, as well as more detailed description of the statistical analysis in the Materials and Methods under the subsection “Statistical analysis”.

(11) Page 7, line 138. Please add a reference to the CHILD study. 

We have added a reference of the CHILD study.

(12) Tables in results and in supplemental data a) contain a mixture of fields describing the newborn and its mother (this is not true for Supplementary Table 2), b) lack column descriptions, c) lack descriptions of abbreviations and formatting used in tables, d) use different font types, e) lack descriptions of statistical tests that were used to obtain p-values, f) use inconsistent rounding. Please correct and add the missing information.

We have consolidated the notation and nomenclature in all Tables and text. All numerical results are now rounded to 2 decimal places. The tests used were included in the Table headers as well as described in the Materials and Methods:

“For continuous phenotypes, an analysis of variance (ANOVA) using the F-statistics or a two-sample t-test was used to compare the mean difference across the three cohorts or two groups, respectively. For categorical phenotypes, a chi-square test of independence was used to compare the difference in frequencies of observed categories. Note that three of the categories under smoking history in the START cohort had expected cell counts less than 5, and was thus excluded from the comparison, the reported p-value was for CHILD and FAMILY.”

(13) Table 1. Sample sizes given in column descriptions do not add up to 1,650 (legend text).

We thank the reviewer for pointing this out. The updated sample size is 1,267, based on the 352 CHILD samples, 411 FAMILY samples, and 352 START samples. Notice that we did not remove those without full smoking history data as Table 1 was intended for the epigenetic subsamples.

(14) Page 7, line 156. Supplementary Tables are incorrectly numbered. In the text, Supplementary Table 4 comes after Supplementary Table 2.

We thank the reviewer for catching this and have corrected the ordering of the Supplementary Tables and Figures. 

(15) Page 7, line 158. "cell compositions" - do you mean estimated white cell proportions? 

We have revised it to “estimated cord blood cell proportions” in the text throughout.

(16) Smoking EWAS - do you see any overlap/directional consistency with the top findings from adult EWASs of smoking such as AHRR? 

We annotated the top EWAS signals from the literature in the meta-analysis (new Figure 2; Supplementary Figures 1 and 3), but was only able to confirm associations in the GFI1 gene. The AHRR signals were also annotated, but below the FDR correction threshold as seen in new Figure 2 at the start of chromosome 5. We further added a new Supplementary Figure 3 to show the directional consistency with top findings (2,620 CpGs reported and 128 CpGs overlapped with our meta-analysis) from Joubert et al., 2016. The Pearson’s correlation coefficient with meta-analyzed effect for maternal smoking was 0.72 and for smoking exposure was 0.60.

We added the following to Results:

“Further, we observed consistency in the direction of association for the 128 CpGs that overlapped between our meta-analysis and the 2,620 CpGs with evidence of association for maternal smoking (19) (Supplementary Figure 3). Specifically, the Pearson’s correlation coefficient for maternal smoking and weekly smoking exposure was 0.72 and 0.60, respectively.”

(17) Page 8, line 169. "also coincided with the GFI1 gene" this is a bit imprecise. Please report the correlation with the CpG from the maternal smoking analysis. 

The CpG was inside the GFI1 gene, we have included the Pearson’s correlation with the top hit in the text below:

“There were no CpGs associated with the ever-smoker status at an FDR of 0.05, though the top signal (cg09935388) was also mapped to the GFI1 gene (Pearson’s r2 correlation with cg12876356 = 0.75 and 0.68 in CHILD and FAMILY, respectively; Supplementary Figure 1).”

(18) Page 8, line 171. Typo "ccg": "ccg01798813". 

It has been corrected to “cpg01798813”.

(19) Page 8, line 176. Please be clear about the phenotype used in these analyses. 

The EWAS of weekly smoking exposure in START was removed in this version of the manuscript, in reflection of the results and the reviewer’s comments, as a result of this phenotyping being skewed and possibly leading to only spurious results (also see response to comment #20).

We have clarified the phenotypes for these results under “Epigenetic Association of Maternal Smoking in White Europeans” below:

“The maternal smoking and smoking exposure EWASs in CHILD did not yield any CpGs after FDR correction (Supplementary Figure 3).”

(20) What was the genomic inflation for the EWASs? 474 loci in the South Asian EWAS seems like a lot of findings. Perhaps a more robust method (e.g., OSCA MOMENT) might help to control the false positive rate. 

The genomic inflation factor was moderately across the cohorts for smoking exposure: 1.02 in CHILD, 0.94 in FAMILY, and 1.00 in START. However, there was more inflation in the tail of the distribution in START than the European cohorts. The empirical type I error rates at 0.01, 0.001, 0.00001, were high in START (x1.7, x5.7, and x165 times at each respective threshold), in contrast to CHILD (x1.06, x1.05, and x0.6) or FAMILY (x1.6, x1.9, and 0). The smoking exposure EWAS based on START was thus removed as these are likely false positives and there was very low smoking exposure to start with (11 reported weekly exposure between 2–42 hrs/week out of 462 with non-missing data). We have added the QQ-plots as well as the genomic inflation factor for the reported meta-analysis in the new Supplementary Figure 2. The following was added to the Results:

“There was no noticeable inflation of empirical type I error in the association p-values from the meta-analysis, with the median of the observed association test statistic roughly equal to the expected median (Supplementary Figure 2).”

(21) What is the targeted array? I don't think it has been introduced prior to this point. 

We introduced it in the Materials and Methods under subsection “Methylation data processing and quality controls”. Considering this comment and previous comments on the ordering of Tables and Figures, we have decided to place Materials and Methods after Introduction and before Results.

(22) The MRS section is described poorly in the results section. It is not clear where the 11 or 114 CpGs come from.

We now include an analytical summary of all scores (derived or external from literature) in the new Supplementary Table 5. Further, we updated the description of scores in Materials and Methods under the subsection “Using DNA Methylation to Construct Predictive Models for Maternal Smoking” to clarify the source and types of MRSs derived:

“To evaluate whether the targeted GMEL-EPIC array design has comparable performance as the epigenome-wide array to evaluate the epigenetic signature of maternal smoking, a total of three MRSs were constructed, two using the 128 CpGs available in all cohorts – across the HM450K and targeted GMEL-EPIC arrays – and with either CHILD (n = 347 with non-missing smoking history) or FAMILY (n = 397) as the validation cohort, and another using 2,107 CpGs that were only available in CHILD and START samples with CHILD as the validation cohort. Henceforth, we referred to these derived maternal smoking scores as the FAMILY targeted MRS, CHILD targeted MRS, and the HM450K MRS, respectively.”

(23) Page 9, line 187. "There was no statistically significant difference between the two scores in all samples (p = 1.00) or among non-smokers (p = 0.24).". How was the significance assessed? Please describe the models (outcome, covariates, model type) used for comparing the two models. It would also be good to report the correlation between the scores.

We have added a subsection “Statistical analysis” under Materials and Methods that described the tests. The correlation between scores is now summarized as a heatmap across all cohorts in the new Supplementary Figure 6.

“For each cohort, we contrasted the three versions of the derived scores using an analysis of variance analysis (ANOVA) along with pairwise comparisons using a two-sample t-test to examine how much information might be lost due to the exclusion of more than 10-fold CpGs at the validation stage. We also examined the correlation structure between all derived and external MRSs using a heatmap summarizing their pairwise Pearson’s correlation coefficient.”

(24) Please include the number of samples in the training/validation and in the test set in the methods and in the results.

We thank the reviewer for this suggestion. In the revised manuscript, we have provided a flow chart as the new Figure 1 and more detailed description of the method in the Materials and Methods. Please also see response to comment #22. The training sample size is based on Joubert et al., (2016), which is 5,647. For our main analyses, the validation sample with non-missing phenotypes remained the CHILD cohort (n=347), while the FAMILY (n=397) and START (n=503) samples were the independent testing data. We alternatively provided another scenario, in which the FAMILY sample was the validation cohort, while CHILD and START were the testing cohorts. The exact sample size and performance metrics for each scenario and score are clearly summarized in the new Supplementary Table 5.

(25) Table 3. Please clarify the type of information contained in the four last columns (p-value?).

Yes – these are the individual cohort p-values. We have taken the suggestion from comment #12 to fully describe all columns and fields.

(26) Page 10, line 215: "The meta-analysis revealed no heterogeneity in the direction nor the effect size of associations between populations". Please quote/refer to the results. 

In the revision, the heterogeneity p-values were quoted and the relevant tables (Supplementary Table 8) were added to this sentence.

(27) Figure 2 has issues with x labels. Due to the low number of ever smokers in START, the boxplot may not be the best visualisation method. It would also benefit from listing n's per group.

We appreciate this comment to improve the figure presentation. We increased the font size for the X-labels. The sample size for each group in START was also labeled in the new Figure 3 (previously Figure 2).

Discussion

(28) Studying the association between maternal smoking and cord blood DNAm is interesting from a biological perspective as it allows for assessing the immediate and long-term effects of maternal smoking on newborn health. However, in terms of calculating the MRS, what are the benefits of using cord blood over the mother's blood? We know that blood-based DNAm smoking score is a powerful predictor of long-term smoking status. 

The reviewer raises an interesting point – abundant literature supports that DNAm changes are tissue-specific. While mother’s blood DNAm smoking score reflect the long-term exposure to smoking in mothers, the cord blood DNAm captures the consequence of such long-term exposure for newborn health. One of the key results of our study is showing that established DNAm signatures of maternal smoking, which is known to mediate birth size and weight in white Europeans (these references were cited in the original manuscript), carries the same effect of reducing birth weight and size in the South Asian population. This is a critical finding from a DoHaD and public health perspective, as DNAm signatures of maternal smoking, irrespective of the smoking status of the mother, can influence the health trajectory of the newborns.

We have expanded our discussion based on this suggestion to highlight the unique features of studying maternal smoking via different tissues and their implications. The following was added to the discussion:

“There are several advantages of using a cord blood based biomarker from the DoHaD perspective. Firstly, cord blood provides a direct reflection of the in utero environment and fetal exposure to maternal smoking. Additionally, since cord blood is collected at birth, it eliminates potential confounding factors such as postnatal exposures that may affect maternal blood samples. Furthermore, studying cord blood DNAm allows for the assessment of epigenetic changes specifically relevant to the newborn, offering valuable information on the potential long-term health implications.”

(29) Page 13, line 285: "Fourth" without "third".

It has been revised accordingly.

Methods 

(30) The methods section does not contain all the details required to replicate the analysis. Whenever statistical analysis is conducted, this section should clearly describe the type of the analysis (linear regression, t-test, etc.) and name the dependent and independent variables. Sample sizes should also be given. 

We added further details of test used and sample size for each analysis. We have also included a new “Statistical analysis” subsection under Materials and Methods.

(31) Please describe MRS testing in the methods.

We tested MRS with respect to binary and continuous smoking phenotypes using a logistic and linear regression, respectively. The predictive value was assessed using area under the roc curve for the binary outcome and an adjusted R2 for the continuous outcome. These were added to the new “Statistical analysis” subsection under Materials and Methods. See response to comments #22-24, and #30.

(32) Please describe the methods used to compare the two versions of MRS for maternal

smoking.

It was a two-sample t-test, which was described in the Figure legends. We have now added this to the new “Statistical analysis” subsection under Materials and Methods.

(33) Please describe testing the associations between MRS and Offspring Anthropometrics in more detail.

We added further details on the regression model and the test for association in the methods. We have now added this to the new “Statistical analysis” subsection under Materials and Methods.

(34) Meta analysing the 450k and GMEL arrays is going to substantially reduce the number of CpGs under investigation.

We agree with the reviewer that this is not optimal for signal discovery. However, this is the only way we could synthesize evidence across the cohorts as FAMILY samples were only processed using the customized array. We added the following as a limitation of the study in the discussion.

“First, the customized array with a limited number of CpGs (<3,000) was designed in 2016 and many large EWASs on smoking and maternal smoking conducted more recently had not been included.”

(35) Page 16, line 364: GDM abbreviation was used in the results section (line 145), yet it is introduced in line 364. 

Thank you for catching this, we have removed the duplicate.

(36) Page 17, line 381: Given the stated importance of ancestry, why not restrict the sample to genetically confirmed groups?

The reviewer has a valid point that ancestry, either perceived or genetic, can introduce additional heterogeneity due to potential differences in genetics, cultural and social practices, and lifestyles. Genetic data are indeed available for a subset of the individuals. In the original version of the manuscript, we used a stringent ancestry calling method by mapping all individuals with the 1000 Genomes samples from continental populations. The final definition was based on a combination of self-reported and genetically confirmed ancestry. However, if we restricted only to genetically confirmed groups, the sample size would be reduced to 312 (vs. 411), 268 (vs. 352), and 488 (vs. 504) in FAMILY, CHILD, and START, respectively.

We compared the mean difference in the beta-values of the top associated CpGs and the derived MRS between those genetically confirmed vs. self-reported ancestral groups, and observed no material difference. These results are now included in the Supplementary Materials as part of the sensitivity analysis. Thus, given these considerations, we decided to use this complementary approach to retain the maximum number of samples while ensuring some aspect of ancestral homogeneity.

“To maximize sample size in FAMILY and CHILD, we retained either self-identified or genetically confirmed Europeans based on available genetic data (Supplementary Table 1).”

(37) Page 18, line 397: sensitivity analysis not sensitive analysis.

Thank you for catching this, we have revised accordingly.

(38) Page 18, line 409: smoking was rank transformed however, it would be good to see regression diagnostics for the lead loci in the EWAS to check that assumptions were met. 

We thank the reviewer for this suggestion. Smoking exposure is indeed skewed and in fact very much zero-inflated across the cohorts. The raw phenotype violated several model assumptions in terms of variance heteroskedasticity, outlying values (influential points), and linearity. The diagnostics suggested improved deviation from model assumption, yet some aspects of the violation remained at a lesser degree. We included a comparison of results before and after transformation and model diagnostics for the lead CpG using CHILD and FAMILY data in the Supplementary Materials. The following was added to the results:

“As a sensitivity analysis, we repeated the analysis for the continuous smoking exposure under rank transformation vs. raw phenotype for the associated CpG in GFI1 and examined the regression diagnostics (Supplementary Material), and found that the model under rank-transformation deviated less from assumptions.”

(39) Page 19, line 418: FDR seems quite a lenient threshold, especially when genome-wide significance thresholds exist. I would be inclined to view the EWAS findings as null.

The choice of use FDR to was indeed arbitrary as there has been no consensus on what significance threshold, if any, should be used in the context of EWAS. The significance threshold for GWAS (Pe’er et al., 2008) probably does not apply directly to EWAS as the number of effective tests will likely differ between genome-wide genetic variants and CpGs. The Bonferroni corrected p-value threshold in this context would be 0.05/200,050=2.5´10-7, which is still less stringent than the GWAS significance threshold. We originally decided to follow the convention of previous studies and use FDR to filter out a subset of plausible associations to contrast the top association signals for their effects between different populations and with reported effect sizes.

We have revised the manuscript throughout by removing the notion of significant associations, and instead used the phrase “top associated signals” or “top associations” when discussion EWAS results for individual CpGs. The following was added to Materials and Methods to clarify the choice of our threshold:

“For each EWAS or meta-analysis, the false discovery rate (FDR) adjustment was used to control multiple testing and we considered CpGs that passed an FDR-adjusted p-value < 0.05 to be relevant for maternal smoking.”

(40) I do not understand Supplementary Figure 6 - how have the data been standardised? Why not plot the CpGs on the beta-value scale?

The standardized values were plotted as the reported p-values for the mean and variance equality tests (i.e. ANOVA F-test, Levene’s test, Anderson-Darling test) were based on these transformed values to reduce inflation due to non-normality. We have since removed this comparison and kept only the comparison of the overall score as the number of CpGs in the HM450k score (143 CpGs) for comparison is too high to be visually interpretable.

(41) It is my understanding, that the MRS for maternal smoking was constructed using external weights projected and regularised using elastic net (effectively trained) in CHILD cohort. The results section discusses associations between maternal smoking history and outcomes in CHILD, FAMILY, and START. Training and testing the score in the same sample (cohort) may result in overfitting and therefore should not be implemented.

The original MRS was constructed using external weights from an independent discovery sample (Joubert et al., 2016; n > 5,000) and the LASSO validation was done in CHILD (n = 352), external testing was in FAMILY and START. This was the lassosum framework whereby we leverage larger sample size from external studies to select more plausible CpGs as candidates to include in the model. Thus, training, validation, and testing were not done in the same samples. We have included a Figure 1 to illustrate the updated analytical flow and a graphical abstract to summarize the methods.

(42) Is it a concern that the findings don't seem to replicate Joubert's results, which came from a much larger study?

Replication is usually done in samples much larger than the discovery samples, thus it is not a concern that we were unable to confirm all signals from Joubert et al., (2016). However, 6/7 of the top associations (FDR adjusted p-value < 0.05) in the meta-analysis were declared as significant in Joubert et al. (2016). In addition, the fact that using Joubert’s summary statistics, we were able to derive MRSs that were strongly associated with both smoking history and weekly exposure suggests shared signals. Also see response to  R1 comment #16 for a comparison of effect consistency.

(43) Please check that all analysis scripts have been uploaded to Github and that the EWAS results are publicly available.

We thank the reviewer for this suggestion. All updated scripts and EWAS results are available on Github. We are working to have the results also submitted to EWAS catalog.

Reviewer #2 (Recommendations For The Authors):

The impact of this study is reduced due to previous findings:

(1) Previous studies have already shown that DNA methylation may mediate the effect of maternal smoking on birth size/weight (see e.g.https://doi.org/10.1098/rstb.2018.0120; https://doi.org/10.1093/ije/dyv048).

We thank the reviewer for this point and would like to take the opportunity to clarify that it was not our objective to examine whether there was a causal relationship, between DNA methylation and birth size that was mediated by maternal smoking. One of the key messages of our study is to evaluate whether epigenetic associations – at individual CpGs and aggregated as a score – are consistent between white European and South Asian populations. One way to examine this is through using established DNAm signatures of maternal smoking, which is known to mediate birth size and weight in white Europeans (these references were cited in the original manuscript), and confirm whether they also carry the same effect on birth outcomes in the South Asian population.

Indeed, our results support that maternal smoking methylation score was consistently associated with negative outcomes in newborns of both white European and South Asian mothers despite no maternal smoking was present in South Asian mothers. These collective point to the possibility that the maternal smoking MRS was capturing a lot more than just smoking and second-hand smoking, but potentially other environmental exposures that also lead to oxidative stress. These together are associated with health consequences, including reduced birth size/weight. One of the candidates for such exposure is air pollution as some of the maternal smoking CpGs were previously linked to air pollution. However, we were unable to assess this hypothesis directly without the air pollution data, and the air pollution methylation score was not associated with smoking history (Supplementary Figure 5) nor smoking exposure (p > 0.4 in CHILD, FAMILY and START).

The following was added to Materials and Methods under the subsection Using DNA Methylation to Construct Predictive Models for Maternal Smoking:

“To benchmark and compare with existing maternal smoking MRSs, we calculated the Reese score using 28 CpGs (48,49),  Richmond score using 568 CpGs (49), Rauschert score using 204 CpGs (50), Joubert score using all 2,620 CpGs with evidence of association for maternal smoking (19), and finally a three-CpG score for air pollution (51). The details of these scores and score weight can be found in Supplementary Table 4.”

The following was added to Results

“Both produced methylation scores that were significantly associated with maternal smoking history (ANOVA F-test p-values =1.0×10-6 and 2.4×10-14 in CHILD and  6.9×10-16 and <2.2×10-16 in FAMILY), and the best among alternative scores for CHILD and FAMILY (Supplementary Table 5). With the exception of the air pollution MRS, all remaining scores were marginally associated with smoking history in both CHILD and FAMILY (Supplementary Figure 5).”

(2) Due to the small study size and low levels of prenatal smoke exposure, the model derived here is of little value and is, in fact, superseded by a previously published model (PMID: 27323799). At the very least, the model should be evaluated here. A novel aspect of this study is the inclusion of a South Asian cohort. Unfortunately, smoke exposure is practically non-existent, so it is unclear how it can be used. The more interesting finding in this study is the possibility that environmental factors such as second-hand smoke or pollution may have similar effects on pregnancies as maternal smoking. Are these available? If so, they could be evaluated for associations with DNA methylation. This would be novel. 

In the revised manuscript, we included the Reese score (Reese et al., 2017) and a few other maternal smoking scores for comparison. In the CHILD cohort, the performance was comparable to our derived score (AUC of 0.95 vs. 0.94 for Reese score), but its applicability was limited since the FAMILY dataset was profiled using a targeted array and only 7 out of 28 of the CpGs in the Reese score were available (AUC of 0.89 vs. 0.72 for Reese). As compared to the remaining scores from literature (see the new Supplementary Table 5 for complete results), Reese’s score has generally favorable performance.

We did examine second-hand smoking in the original manuscript, showing a significant association with weekly maternal smoking exposure (original Table 3 and Supplementary Table 8). However, air pollution data is not available for assessment.

(3) The other novel aspect is the evaluation of associations with outcomes later in life. Height and weight are interesting but impact could be gained by including other relevant outcomes such as birth complications, asthma, and intellectual impairment which are known to be associated with prenatal smoking. 

We thank the reviewer for bring up this point. One of the key health outcomes in the CHILD study was asthma, and data at later time points are available. However, we do not have similar outcomes collected in the other two studies (FAMILY and START), which focused on cardiometabolic health in young children. Thus, we did not initially include outcomes that were not available across all cohorts as the intention was to contrast the effects between populations.

We recognize that this is an important question and decided to provide the association results for mother reported asthma and allergy, but based on different definitions as these outcomes cannot be harmonized across the cohorts. We also included mode of delivery via emergency C-section as an additional proxy outcome of birth complication.

The following was added to Materials and Methods:

“Mode of delivery (emergency c-section vs. other) was collected at the time of delivery.”

“Additional phenotypes included smoking exposures (hours per week) at home, potential allergy based on mother reporting any of: eczema, hay fever, wheeze, asthma, food allergy (egg, cow milk, soy, other) for her child in FAMILY and START, and asthma based on mother’s opinion in CHILD (“In your opinion, does the child have any of the following? Asthma”).”

The following was added to Results:

“The maternal smoking MRS was consistently associated with increasing weekly smoking exposure in children reported by mothers at the 1-year (0.51±0.15, FDR adjusted p= 0.0052) , 3-year (0.53±0.16, FDR adjusted p= 0.0052), and 5-year (0.40±0.15, FDR adjusted p= 0.021) visits with similar effects.”

“We did not find any association with self-reported allergy or asthma in children at later visits (Supplementary Table 8). Further, there was no evidence of association between the MRS and any maternal outcomes (Supplementary Table 8).”

REFERENCES:

Gondalia, R., Baldassari, A., Holliday, K. M., Justice, A. E., Stewart, J. D., Liao, D., . . . Whitsel, E. A. (2021). Epigenetically mediated electrocardiographic manifestations of sub-chronic exposures to ambient particulate matter air pollution in the Women's Health Initiative and Atherosclerosis Risk in Communities Study. Environ Res, 198, 111211. doi:10.1016/j.envres.2021.111211

Joubert, B. R., Felix, J. F., Yousefi, P., Bakulski, K. M., Just, A. C., Breton, C., . . . London, S. J. (2016). DNA Methylation in Newborns and Maternal Smoking in Pregnancy: Genome-wide Consortium Meta-analysis. Am J Hum Genet, 98(4), 680-696. doi:10.1016/j.ajhg.2016.02.019

Martin, J. A., Osterman, M. J. K., & Driscoll, A. K. (2023). Declines in Cigarette Smoking During Pregnancy in the United States, 2016-2021. NCHS Data Brief(458), 1-8. Retrieved from https://www.ncbi.nlm.nih.gov/pubmed/36723453

Reese, S. E., Zhao, S., Wu, M. C., Joubert, B. R., Parr, C. L., Haberg, S. E., . . . London, S. J. (2017). DNA Methylation Score as a Biomarker in Newborns for Sustained Maternal Smoking during Pregnancy. Environ Health Perspect, 125(4), 760-766. doi:10.1289/EHP333

eLife assessment

This important manuscript shows that axonal transport of Wnd is required for its normal degradation by the Hiw ubiquitin ligase. These are interesting findings supported by solid data. However, the summary and conclusions are over-interpreted and how Rab11 is involved in Golgi processing or axonal transport of Wnd is not resolved and would require additional experiments to support the claims. Alternatively, the authors should dial back on their interpretation.

Reviewer #1 (Public Review):

Summary:

The manuscript by Kim et al. describes a role for axonal transport of Wnd (a dual leucine zipper kinase) for its normal degradation by the Hiw ubiquitin ligase pathway. In Hiw mutants, the Wnd protein accumulates dramatically in nerve terminals compared to the cell body of neurons. In the absence of axonal transport, Wnd levels rise and lead to excessive JNK signaling that makes neurons unhappy.

Strengths:

Using GFP-tagged Wnd transgenes and structure-function approaches, the authors show that palmitoylation of the protein at C130 plays a role in this process by promoting golgi trafficking and axonal localization of the protein. In the absence of this transport, Wnd is not degraded by Hiw. The authors also identify a role for Rab11 in the transport of Wnd, and provide some evidence that Rab11 loss-of-function neuronal degenerative phenotypes are due to excessive Wnd signaling. Overall, the paper provides convincing evidence for a preferential site of action for Wnd degradation by the Hiw pathway within axonal and/or synaptic compartments of the neuron. In the absence of Wnd transport and degradation, the JNK pathway becomes hyperactivated. As such, the manuscript provides important new insights into compartmental roles for Hiw-mediated Wnd degradation and JNK signaling control.

Weaknesses:

It is unclear if the requirement for Wnd degradation at axonal terminals is due to restricted localization of HIW there, but it seems other data in the field argues against that model. The mechanistic link between Hiw degradation and compartmentalization is unknown.

Reviewer #2 (Public Review):

Summary:

Utilizing transgene expression of Wnd in sensory neurons in Drosophila, the authors found that Wnd is enriched in axonal terminals. This enrichment could be blocked by preventing palmitoylation or inhibiting Rab1 or Rab11 activity. Indeed, subsequent experiments showed that inhibiting Wnd can prevent toxicity by Rab11 loss of function.

Strengths:

This paper evaluates in detail Wnd location in sensory neurons, and identifies a novel genetic interaction between Rab11 and Wnd that affects Wnd cellular distribution.

Weaknesses:

The authors report low endogenous expression of wnd, and expressing mutant hiw or overexpressing wnd is necessary to see axonal terminal enrichment. It is unclear if this overexpression model (which is known to promote synaptic overgrowth) would be relevant to normal physiology.

Palmitoylation of the Wnd orthologue DLK in sensory neurons has previously been identified as important for DLK trafficking in a cell culture model.

The authors find genetic interaction between Wnd and Rab11, but these studies are incomplete and they do not support the authors' mechanistic interpretation.

eLife assessment

Manley and Vaziri introduce an important new method for brain-wide imaging of cellular activity in zebrafish and provide evidence for the applicability of this technique. They use this method to explore the question of how neural variability gives rise to variability in behavior. The analyses used are mostly convincing, with some central results that are currently incomplete and difficult to interpret.

Reviewer #1 (Public Review):

Summary:

In this paper, Manley and Vaziri investigate whole-brain neural activity underlying behavioural variability in zebrafish larvae. They combine whole brain (single cell level) calcium imaging during the presentation of visual stimuli, triggering either approach or avoidance, and carry out whole brain population analyses to identify whole brain population patterns responsible for behavioural variability. They show that similar visual inputs can trigger large variability in behavioural responses. Though visual neurons are also variable across trials, they demonstrate that this neural variability does not degrade population stimulus decodability. Instead, they find that the neural variability across trials is in orthogonal population dimensions to stimulus encoding and is correlated with motor output (e.g. tail vigor). They then show that behavioural variability across trials is largely captured by a brain-wide population state prior to the trial beginning, which biases choice - especially on ambiguous stimulus trials. This study suggests that parts of stimulus-driven behaviour can be captured by brain-wide population states that bias choice, independently of stimulus encoding.

Strengths:

-The strength of the paper principally resides in the whole brain cellular level imaging in a well-known but variable behaviour.

- The analyses are reasonable and largely answer the questions the authors ask.

- Overall the conclusions are well warranted.

Weaknesses:

A more in-depth exploration of some of the findings could be provided, such as:

- Given that thousands of neurons are recorded across the brain a more detailed parcelation of where the neurons contribute to different population coding dimensions would be useful to better understand the circuits involved in different computations.

- Given that the behaviour on average can be predicted by stimulus type, how does the stimulus override the brain-wide choice bias on some trials? In other words, a better link between the findings in Figures 2 and 3 would be useful for better understanding how the behaviour ultimately arises.

- What other motor outputs do the noise dimensions correlate with?

The dataset that the authors have collected is immensely valuable to the field, and the initial insights they have drawn are interesting and provide a good starting ground for a more expanded understanding of why a particular action is determined outside of the parameters experimenters set for their subjects.

Reviewer #2 (Public Review):

Overview

In this work, Manley and Vaziri investigate the neural basis for variability in the way an animal responds to visual stimuli evoking prey-capture or predator-avoidance decisions. This is an interesting problem and the authors have generated a potentially rich and relevant data set. To do so, the authors deployed Fourier light field microscopy (Flfm) of larval zebrafish, improving upon prior designs and image processing schemes to enable volumetric imaging of calcium signals in the brain at up to 10 Hz. They then examined associations between neural activity and tail movement to identify populations primarily related to the visual stimulus, responsiveness, or turn direction - moreover, they found that the activity of the latter two populations appears to predict upcoming responsiveness or turn direction even before the stimulus is presented. While these findings may be valuable for future more mechanistic studies, issues with resolution, rigor of analysis, clarity of presentation, and depth of connection to the prior literature significantly dampen enthusiasm.

Imaging

- Resolution: It is difficult to tell from the displayed images how good the imaging resolution is in the brain. Given scattering and lensing, it is important for data interpretation to have an understanding of how much PSF degrades with depth.

- Depth: In the methods it is indicated that the imaging depth was 280 microns, but from the images of Figure 1 it appears data was collected only up to 150 microns. This suggests regions like the hypothalamus, which may be important for controlling variation in internal states relevant to the behaviors being studied, were not included.

- Flfm data processing: It is important for data interpretation that the authors are clearer about how the raw images were processed. The de-noising process specifically needs to be explained in greater detail. What are the characteristics of the noise being removed? How is time-varying signal being distinguished from noise? Please provide a supplemental with images and algorithm specifics for each key step.

- Merging: It is noted that nearby pixels with a correlation greater than 0.7 were merged. Why was this done? Is this largely due to cross-contamination due to a drop in resolution? How common was this occurrence? What was the distribution of pixel volumes after aggregation? Should we interpret this to mean that a 'neuron' in this data set is really a small cluster of 10-20 neurons? This of course has great bearing on how we think about variability in the response shown later.

- Bleaching: Please give the time constants used in the fit for assessing bleaching.

Analysis

- Slow calcium dynamics: It does not appear that the authors properly account for the slow dynamics of calcium-sensing in their analysis. Nuclear-localized GCaMP6s will likely have a kernel with a multiple-second decay time constant for many of the cells being studied. The value used needs to be given and the authors should account for variability in this kernel time across cell types. Moreover, by not deconvolving their signals, the authors allow for contamination of their signal at any given time with a signal from multiple seconds prior. For example, in Figure 4A (left turns), it appears that much of the activity in the first half of the time-warped stimulus window began before stimulus presentation - without properly accounting for the kernel, we don't know if the stimulus-associated activity reported is really stimulus-associated firing or a mix of stimulus and pre-stimulus firing. This also suggests that in some cases the signals from the prior trial may contaminate the current trial.

- Partial Least Squares (PLS) regression: The steps taken to identify stimulus coding and noise dimensions are not sufficiently clear. Please provide a mathematical description.

- No response: It is not clear from the methods description if cases where the animal has no tail response are being lumped with cases where the animal decides to swim forward and thus has a large absolute but small mean tail curvature. These should be treated separately.

Results

- Behavioral variability: Related to Figure 2, within- and across-subject variability are confounded. Please disambiguate. It may also be informative on a per-fish basis to examine associations between reaction time and body movement.

- Data presentation clarity: All figure panels need scale bars - for example, in Figure 3A there is no indication of timescale (or time of stimulus presentation). Figure 3I should also show the time series of the w_opt projection.

- Pixel locations: Given the poor quality of the brain images, it is difficult to tell the location of highlighted pixels relative to brain anatomy. In addition, given that the midbrain consists of much more than the tectum, it is not appropriate to put all highlighted pixels from the midbrain under the category of tectum. To aid in data interpretation and better connect this work with the literature, it is recommended that the authors register their data sets to standard brain atlases and determine if there is any clustering of relevant pixels in regions previously associated with prey-capture or predator-avoidance behavior.

Interpretation

- W_opt and e_1 orthogonality: The statement that these two vectors, determined from analysis of the fluorescence data, are orthogonal, actually brings into question the idea that true signal and leading noise vectors in firing-rate state-space are orthogonal. First, the current analysis is confounding signals across different time periods - one could assume linearity all the way through the transformations, but this would only work if earlier sources of activation were being accounted for. Second, the transformation between firing rate and fluorescence is most likely not linear for GCaMP6s in most of the cells recorded. Thus, one would expect a change in the relationship between these vectors as one maps from fluorescence to firing rate.

- Sources of variability: The authors do not take into account a fairly obvious source of variability in trial-to-trial response - eye position. We know that prey capture responsiveness is dependent on eye position during stimulus (see Figure 4 of PMID: 22203793). We also expect that neurons fairly early in the visual pathway with relatively narrow receptive fields will show variable responses to visual stimuli as the degree of overlap with the receptive field varies with eye movement. There can also be small eye-tracking movements ahead of the decision to engage in prey capture (Figure 1D, PMID: 31591961) that can serve as a drive to initiate movements in a particular direction. Given these possibilities indicating that the behavioral measure of interest is gaze, and the fact that eye movements were apparently monitored, it is surprising that the authors did not include eye movements in the analysis and interpretation of their data.

Reviewer #3 (Public Review):

Summary:

In this study, Manley and Vaziri designed and built a Fourier light-field microscope (fLFM) inspired by previous implementations but improved and exclusively from commercially available components so others can more easily reproduce the design. They combined this with the design of novel algorithms to efficiently extract whole-brain activity from larval zebrafish brains.

This new microscope was applied to the question of the origin of behavioral variability. In an assay in which larval zebrafish are exposed to visual dots of various sizes, the fish respond by turning left or right or not responding at all. Neural activity was decomposed into an activity that encodes the stimulus reliably across trials, a 'noise' mode that varies across trials, and a mode that predicts tail movements. A series of analyses showed that trial-to-trial variability was largely orthogonal to activity patterns that encoded the stimulus and that these noise modes were related to the larvae's behavior.

To identify the origins of behavioral variability, classifiers were fit to the neural data to predict whether the larvae turned left or right or did not respond. A set of neurons that were highly distributed across the brain could be used to classify and predict behavior. These neurons could also predict spontaneous behavior that was not induced by stimuli above chance levels. The work concludes with findings on the distributed nature of single-trial decision-making and behavioral variability.

Strengths:

The design of the new fLFM microscope is a significant advance in light-field and computational microscopy, and the open-source design and software are promising to bring this technology into the hands of many neuroscientists.

The study addresses a series of important questions in systems neuroscience related to sensory coding, trial-to-trial variability in sensory responses, and trial-to-trial variability in behavior. The study combines microscopy, behavior, dynamics, and analysis and produces a well-integrated analysis of brain dynamics for visual processing and behavior. The analyses are generally thoughtful and of high quality. This study also produces many follow-up questions and opportunities, such as using the methods to look at individual brain regions more carefully, applying multiple stimuli, investigating finer tail movements and how these are encoded in the brain, and the connectivity that gives rise to the observed activity. Answering questions about variability in neural activity in the entire brain and its relationship to behavior is important to neuroscience and this study has done that to an interesting and rigorous degree.

Points of improvement and weaknesses:

The results on noise modes may be a bit less surprising than they are portrayed. The orthogonality between neural activity patterns encoding the sensory stimulus and the noise modes should be interpreted within the confounds of orthogonality in high-dimensional spaces. In higher dimensional spaces, it becomes more likely that two random vectors are almost orthogonal. Since the neural activity measurements performed in this study are quite high dimensional, a more explicit discussion is warranted about the small chance that the modes are not almost orthogonal.

The conclusion that sparsely distributed sets of neurons produce behavioral variability needs more investigation because the way the results are shown could lead to some misinterpretations. The prediction of behavior from classifiers applied to neural activity is interesting, but the results are insufficiently presented for two reasons.

(1) The neurons that contribute to the classifiers (Figures 4H and J) form a sufficient set of neurons that predict behavior, but this does not mean that neurons outside of that set cannot be used to predict behavior. Lasso regularization was used to create the classifiers and this induces sparsity. This means that if many neurons predict behavior but they do so similarly, the classifier may select only a few of them. This is not a problem in itself but it means that the distributions of neurons across the brain (Figures 4H and J) may appear sparser and more distributed than the full set of neurons that contribute to producing the behavior. This ought to be discussed better to avoid misinterpretation of the brain distribution results, and an alternative analysis that avoids the confound could help clarify.

(2) The distribution of neurons is shown in an overly coarse manner in only a flattened brain seen from the top, and the brain is divided into four coarse regions (telencephalon, tectum, cerebellum, hindbrain). This makes it difficult to assess where the neurons are and whether those four coarse divisions are representative or whether the neurons are in other non-labeled deeper regions. For these two reasons, some of the statements about the distribution of neurons across the brain would benefit from a more thorough investigation.

Reviewer #1 (Public Review):

Summary:

This research group has consistently performed cutting-edge research aiming to understand the role of hormones in the control of social behaviors, specifically by utilizing the genetically tractable teleost fish, medaka, and the current work is no exception. The overall claim they make, that estrogens modulate social behaviors in males and females is supported, with important caveats. For one, there is no evidence these estrogens are generated by "neurons" as would be assumed by their main claim that it is NEUROestrogens that drive this effect. While indeed the aromatase they have investigated is expressed solely in the brain, in most teleosts, brain aromatase is only present in glial cells (astrocytes, radial glia). The authors should change this description so as not to mislead the reader. Below I detail more specific strengths and weaknesses of this manuscript.

Strengths:

• Excellent use of the medaka model to disentangle the control of social behavior by sex steroid hormones.

• The findings are strong for the most part because deficits in the mutants are restored by the molecule (estrogens) that was no longer present due to the mutation.

• Presentation of the approach and findings are clear, allowing the reader to make their own inferences and compare them with the authors'.

• Includes multiple follow-up experiments, which lead to tests of internal replication and an impactful mechanistic proposal.

• Findings are provocative not just for teleost researchers, but for other species since, as the authors point out, the data suggest mechanisms of estrogenic control of social behaviors may be evolutionarily ancient.

Weaknesses:

• As stated in the summary, the authors attribute the estrogen source to neurons and there isn't evidence this is the case. The impact of the findings doesn't rest on this either.

• The d4 versus d8 esr2a mutants showed different results for aggression. The meaning and implications of this finding are not discussed, leaving the reader wondering.

• Lack of attribution of previously published work from other research groups that would provide the proper context of the present study.

• There are a surprising number of citations not included; some of the ones not included argue against the authors' claims that their findings were "contrary to expectation".

• The experimental design for studying aggression in males has flaws. A standard test like a resident-intruder test should be used.

• While they investigate males and females, there are fewer experiments and explanations for the female results, making it feel like a small addition or an aside.

• The statistics comparing "experimental to experimental" and "control to experimental" aren't appropriate.

Reviewer #2 (Public Review):

The novelty of this study stems from the observations that neuro-estrogens appear to interact with brain androgen receptors to support male-typical behaviors. The study provides a step forward in clarifying the somewhat contradictory findings that, in teleosts and unlike other vertebrates, androgens regulate male-typical behaviors without requiring aromatization, but at the same time estrogens appear to also be involved in regulating male-typical behaviors. They manipulate the expression of one aromatase isoform, cyp19a1b, that is purported to be brain-specific in teleosts. Their findings are important in that brain estrogen content is sensitive to the brain-specific cyp19a1b deficiency, leading to alterations in both sexual behavior and aggressive behavior. Interestingly, these males have relatively intact fertility rates, despite the effects on the brain.

That said, the framing of the study, the relevant context, and several aspects of the methods and results raise concerns. Two interpretations need to be addressed/tempered:

(1) that the rescue of cyp19a1b deficiency by tank-applied estradiol is not necessarily a brain/neuro-estrogen mode of action, and<br /> (2) the large increases in peripheral and brain androgen levels in the cyp19a1b deficient animals imply some indirect/compensatory effects of lifelong cyp19a1b deficiency.

Reviewer #3 (Public Review):

Summary:

Taking advantage of the existence in fish of two genes coding for estrogen synthase, the enzyme aromatase, one mostly expressed in the brain (Cyp19a1b) and the other mostly found in the gonads (Cyp19a1a), this study investigates the role of neuro-estrogens in the control of sexual and aggressive behavior in teleost fish. The constitutive deletion of Cyp19a1b reduced brain estrogen content by 87% in males and about 50% in females. It led to reduced sexual and aggressive behavior in males and reduced sexual behavior in females. These effects are reversed by adult treatment with estradiol thus indicating that they are activational in nature. The deletion of Cyp19a1b is associated with a reduced expression of the genes coding for the two androgen receptors, ara, and arb, in brain regions involved in the regulation of social behavior. The analysis of the gene expression and behavior of mutants of estrogen receptors indicates that these effects are likely mediated by the activation of the esr1 and esr2a isoforms. These results provide valuable insight into the role of neuro-estrogens in social behavior in the most abundant vertebrate taxa. While estrogens are involved in the organization of the brain and behavior of some birds and rodents, neuro-estrogens appear to play an activational role in fish through a facilitatory action of androgen signaling.

Strengths:

- Evaluation of the role of brain "specific" Cyp19a1 in male teleost fish, which as a taxa are more abundant and yet proportionally less studied than the most common birds and rodents. Therefore, evaluating the generalizability of results from higher vertebrates is important. This approach also offers great potential to study the role of brain estrogen production in females, an understudied question in all taxa.

- Results obtained from multiple mutant lines converge to show that estrogen signaling drives aspects of male sexual behavior.

- The comparative discussion of the age-dependent abundance of brain aromatase in fish vs mammals and its role in organization vs activation is important beyond the study of the targeted species.

Weaknesses:

- The new transgenic lines are under-characterized. There is no evaluation of the mRNA and protein products of Cyp19a1b and ESR2a.

- The stereotypic sequence of sexual behavior is poorly described, in particular, the part played by the two sexual partners, such that the conclusions are not easily understandable, notably with regards to the distinction between motivation and performance. The behavior of females is only assessed from the perspective of the male, which raises questions about the interpretation of the reduced behavior of the males.<br /> At no point do the authors seem to consider that a reduced behavior of one sex could result from a reduced sensory perception from this sex or a reduced attractivity or sensory communication from the other sex.

- Aspects of the methods are not detailed enough to allow proper evaluation of their quality or replication of the data.

- It seems very dangerous to use the response to a mutant abnormal behavior (ESR2-KO females) as a test, given that it is not clear what is the cause of the disrupted behavior.

- Most experiments are weakly powered (low sample size) and analyzed by multiple T-tests while 2 way ANOVA could have been used in several instances. No mention of T or F values, or degrees of freedom.

- The variability of the mRNA content for the same target gene between experiments (genotype comparison vs E2 treatment comparison) raises questions about the reproducibility of the data (apparent disappearance of genotype effect).

- The discussion confuses the effects of estrogens on sexual differentiation (developmental programming = permanent) and activation (= reversible activation of brain circuits in adulthood) of the brain and behavior. Whether sex differences in the circuits underlying social behaviors exist is not clear.

Conclusions :

Overall, the claims regarding the activational role of neuro-estrogens on male sexual behavior are supported by converging evidence from multiple mutant lines. The role of neuroestrogens on gene expression in the brain is mostly solid too. The data for females are comparatively weaker. Conclusions regarding sexual differentiation should be considered carefully.

eLife assessment

This is a potentially valuable study suggesting that neuronal-specific loss of function of the RNA splicing factor Ptbp1 in striatal neurons induces dopaminergic markers and alleviates motor defects in a 6-hydroxydopamine (6-OHDA) mouse model of Parkinson's Disease. If properly replicated, the claims of the manuscript are remarkable and identify a straightforward mechanism with therapeutic relevance for the treatment of motor deficits in Parkinson's Disease. However, while the rescue of motor deficits with Ptbp1 manipulation is solid, the strength of the evidence supporting the induction of a dopaminergic neuronal identity is incomplete. The study nevertheless addresses recent controversial literature on cell reprogramming in Parkinson's Disease and will be of interest to researchers with a focus on the application of gene therapy to rescue neurodegeneration.

Reviewer #1 (Public Review):

Summary:

Recent years have seen spectacular and controversial claims that loss of function of the RNA splicing factor Ptbp1 can efficiently reprogram astrocytes into functional neurons that can rescue motor defects seen in 6-hydroxydopamine (6-OHDA)-induced mouse models of Parkinson's disease (PD). This latest study is one of a series that fails to reproduce these observations, but remarkably also reports that neuronal-specific loss of function of Ptbp1 both induces expression of dopaminergic neuronal markers in striatal neurons and rescues motor defects seen in 6-OHDA-treated mice. The claims, if replicated, are remarkable and identify a straightforward and potentially translationally relevant mechanism for treating motor defects seen in PD models. However, while the reported behavioral effects are strong and were collected without sample exclusion, other claims made here are less convincing. In particular, no evidence that Ptbp1 loss of function actually occurs in striatal neurons is provided, and the immunostaining data used to claim that dopaminergic markers are induced in striatal neurons is not convincing. Furthermore, no characterization of the molecular identity of Ptbp1-deficient striatal neurons is provided using single-cell RNA-Seq or spatial transcriptomics, making it difficult to conclude that these cells are indeed adopting a dopaminergic phenotype.

Overall, while the claims of behavioral rescue of 6-OHDA-treated mice appear compelling, it is essential that these be independently replicated as soon as possible before further studies on this topic are carried out. Insights into the molecular mechanisms by which neuronal-specific loss of function of Ptbp1 induces behavioral rescue are lacking, however. Moreover, the claims of induction of neuronal identity in striatal neurons by Ptbp1 require considerable additional work to be convincing.

Strengths of the study:

(1) The effect size of the behavioral rescue in the stepping and cylinder tests is strong and significant, essentially restoring 6-OHDA-lesioned mice to control levels.

(2) Since the neurotoxic effects of 6-OHDA treatment are highly variable, the fact that all behavioral data was collected blinded and that no samples were excluded from analysis increases confidence in the accuracy of the results reported here.

Weaknesses of the study:

(1) Neurons express relatively little Ptbp1. Indeed, cellular expression levels as measured by scRNA-Seq are substantially below those of astrocytes and other non-neuronal cell types, and Ptbp1 immunoreactivity has not been observed in either striatal or midbrain neurons (e.g. Hoang, et al. Nature 2023). This raises the question of whether any recovery of Th expression is indeed mediated by the loss of function of Ptbp1 rather than by off-target effects. AAV-mediated rescue of Ptbp1 expression could help clarify this.

(2) It is not clear why dopaminergic neurons, which are not normally found in the striatum, are observed following Ptbp1 knockout. This is very similar to the now-debunked claims made in Zhou, et al. Cell 2020, but here performed using the hSyn rather than GFAP mini promoter to control AAV expression. While this is the most dramatic and potentially translationally relevant claim of the study, this claim is extremely surprising and lacks any clear mechanistic explanation for why it might happen in the first place. This observation is even more surprising in light of reports that antisense oligonucleotide-mediated knockdown of Ptbp1, which should have affected both neuronal and glial Ptbp1 expression, failed to induce expression of dopaminergic neuronal markers in the striatum (Chen, et al. eLife 2022). Selective loss of function of Ptbp1 in striatal and midbrain astrocytes likewise results in only modest changes in gene expression It is critically important that this claim be independently replicated, and that additional data be provided to conclusively show that striatal neurons are indeed expressing dopaminergic markers.

(3) More generally, since multiple spectacular and irreproducible claims of single-step glial-to-neuron reprogramming have appeared in high-profile journals in recent years, a consensus has emerged that it is essential to comprehensively characterize the identity of "transformed" cells using either single-cell RNA-Seq or spatial transcriptomics (e.g. Qian, et al. FEBS J 2021; Wang and Zhang, Dev Neurobiol 2022). These concerns apply equally to claims of neuronal subtype conversion such as those advanced here, and it is essential to provide these same datasets.

(4) Low-power images are generally lacking for immunohistochemical data shown in Figures 3 and 4, which makes interpretation difficult. DAPI images in Figure 3C do not appear nuclear. Immunostaining for Th, DAT, and Dcx in Figure 4 shows a high background and is difficult to interpret.

(5) Insights into the mechanism by which neuronal-specific loss of Ptbp1 function induces either functional recovery, or dopaminergic markers in striatal neurons, is lacking.

Reviewer #2 (Public Review):

Summary:

The manuscript by Bock and colleagues describes the generation of an AAV-delivered adenine base editing strategy to knockdown PTBP1 and the behavioral and neurorestorative effects of specifically knocking down striatal or nigral PTBP1 in astrocytes or neurons in a mouse model of Parkinson's disease. The authors found that knocking down PTBP1 in neurons, but not astrocytes, and in striatum, but not nigra, results in the phenotypic reorganization of neurons to TH+ cells sufficient to rescue motor phenotypes, though insufficient to normalize responses to dopaminomimetic drugs.

Strengths:

The manuscript is generally well-written and adds to the growing literature challenging previous findings by Qian et al., 2020 and Zhou et al., 2020 indicating that astrocytic downregulation of PTBP1 can induce conversion to dopaminergic neurons in the midbrain and improve parkinsonian symptoms. The base editing approach is interesting and potentially more therapeutically relevant than previous approaches.

Weaknesses:

The manuscript has several weaknesses in approach and interpretation. In terms of approach, the animal model utilized, the 6-OHDA model, though useful to examine dopaminergic cell loss, exhibits accelerated neurodegeneration and none of the typical pathological hallmarks (synucleinopathy, Lewy bodies, etc.) compared to the typical etiology of Parkinson's disease, limiting its translational interpretation. In addition, there is no confirmation of a neuronal or astrocytic knockdown of PTBP1 in vivo; all base editing validation experiments were completed in cell lines. Finally, it is unclear why the base editing approach was used to induce loss-of-function rather than a cell-type specific knockout, if the goal is to assess the effects of PTBP1 loss in specific neurons. In terms of interpretation, the conclusion by the authors that PTBP1 knockdown has little likelihood to be therapeutically relevant seems overstated, particularly since they did observe a beneficial effect on motor behavior. We know that in PD, patients often display negligible symptoms until 50-70% of dopaminergic input to the striatum is lost, due to compensatory activity of remaining dopaminergic cells. Presumably, a small recovery of dopaminergic neurons would have an outsized effect on motor ability and may improve the efficacy of dopaminergic drugs, particularly levodopa, at lower doses, averting many problematic side effects. Since striatal dopamine was assessed by whole-tissue analysis, which is not necessarily reflective of synaptic dopamine availability, it is difficult to assess whether the ~10% increase in TH+ cells in the striatum was sufficient to improve dopamine function. However, the improvement in motor activity suggests that it was.

Reviewer #3 (Public Review):

This study explores the use of an adenine base editing strategy to knock down PTBP1 in astrocytes and neurons of a Parkinson's disease mouse model, as a potential AAV-BE therapy. The results indicate that editing Ptbp1 in neurons, but not astrocytes, leads to the formation of tyrosine hydroxylase (TH)+ cells, rescuing some motor symptoms.

Several aspects of the manuscript stand out positively. Firstly, the clarity of the presentation. The authors communicate their ideas and findings in a clear and understandable manner, making it easier for readers to follow.

The Materials and methods section is well-elaborated, providing sufficient detail for reproducibility.

The logical flow of the manuscript makes sense, with each section building upon the previous one coherently.

The ABE strategy employed by the authors appears sound, and the manuscript presents a coherent and well-supported argument.

Positively, some of the data in this study effectively counteracts previous work in line with more recent publications, demonstrating the authors' ability to contribute to the ongoing conversation in the field.

However, while the in vitro data yields promising results, it may have been overly optimistic to assume that the efficiencies observed in dividing cells will directly translate to in vivo conditions. This consideration is important given the added complexities of vector optimization, different cell types targeted in vitro versus in vivo, as well as unknown intrinsic limitations of the base editing technology.

In addition, certain aspects of the manuscript would benefit from a more in-depth and comprehensive discussion rather than being only briefly touched upon. Such a discussion would enhance the relevance of the obtained results and provide the foundation for improvement when using similar approaches.

eLife assessment

This valuable study provides insights and strategies for assessing laminar structure in vivo in the visual cortex of the macaque monkey with high-density linear electrode arrays. The paper provides solid evidence demonstrating that signals in higher frequency bands, related to the discharge of action potentials, are of substantially better use for achieving well-resolved cortical layer identification than are signals in lower frequency bands typically associated with local field potentials and standard-practice Current Source Density (CSD) analyses. These findings are of interest to electrophysiologists seeking to make comparisons between cortical layers.

Reviewer #1 (Public Review):

Summary:

In this study, Zhang et al., presented an electrophysiology method to identify the layers of macaque visual cortex with high density Neuropixels 1.0 electrode. They found several electrophysiology signal profiles for high-resolution laminar discrimination and described a set of signal metrics for fine cortical layer identification.

Strengths:

There are two major strengths. One is the use of high density electrodes. The Neuropixels 1.0 probe has 20 um spacing electrodes, which can provide high resolution for cortical laminar identification. The second strength is the analysis. They found multiple electrophysiology signal profiles which can be used for laminar discrimination. Using this new method, they could identify the most thin layer in macaque V1. The data support their conclusion.

Weaknesses:

While this electrophysiology strategy is much easier to perform even in awake animals compared to histological staining methods, it provides an indirect estimation of cortical layers. A parallel histological study can provide a direct matching between the electrode signal features and cortical laminar locations. However, there are technical challenges, for example the distortions in both electrode penetration and tissue preparation may prevent a precise matching between electrode locations and cortical layers. In this case, additional micro wires electrodes binding with Neuropixels probe can be used to inject current and mark the locations of different depths in cortical tissue after recording.

Reviewer #2 (Public Review):

Summary:

This paper documents an attempt to accurately determine the locations and boundaries of the anatomically and functionally defined layers in macaque primary visual cortex using voltage signals recorded from a high-density electrode array that spans the full depth of cortex with contacts at 20 um spacing. First, the authors attempt to use current source density (CSD) analysis to determine layer locations, but they report a striking failure because the results vary greatly from one electrode penetration to the next and because the spatial resolution of the underlying local field potential (LFP) signal is coarse compared to the electrical contact spacing. The authors thus turn to examining higher frequency signals related to action potentials and provide evidence that these signals reflect changes in neuronal size and packing density, response latency and visual selectivity.

Strengths:

There is a lot of nice data to look at in this paper that shows interesting quantities as a function of depth in V1. Bringing all of these together offers the reader a rich data set: CSD, action potential shape, response power and coherence spectrum, and post-stimulus time response traces. Furthermore, data are displayed as a function of eye (dominant or non-dominant) and for achromatic and cone-isolating stimuli.

This paper takes a strong stand in pointing out weaknesses in the ability of CSD analysis to make consistent determinations about cortical layering in V1. Many researchers have found CSD to be problematic, and the observations here may be important to motivate other researchers to carry out rigorous comparisons and publish their results, even if they reflect negatively on the value of CSD analysis.

The paper provides a thoughtful, practical and comprehensive recipe for assigning traditional cortical layers based on easily-computed metrics from electophysiological recordings in V1, and this is likely to be useful for electrophysiologists who are now more frequently using high-density electrode arrays.

Weaknesses:

Much effort is spent pointing out features that are well known, for example, the latency difference associated with different retinogeniculate pathways, the activity level differences associated with input layers, and the action potential shape differences associated with white vs. gray matter. These have been used for decades as indicators of depth and location of recordings in visual cortex as electrodes were carefully advanced. High density electrodes allow this type of data to now be collected in parallel, but at discrete, regular sampling points. Rather than showing examples of what is already accepted, the emphasis should be placed on developing a rigorous analysis of how variable vs. reproducible are quantitative metrics of these features across penetrations, as a function of distance or functional domain, and from animal to animal. Ultimately, a more quantitative approach to the question of consistency is needed to assess the value of the methods proposed here.

Another important piece of information for assessing the ability to determine layers from spiking activity is to carry out post-mortem histological processing so that the layer determination made in this paper could be compared to anatomical layering.

On line 162, the text states that there is a clear lack of consistency across penetrations, but why should there be consistency: how far apart in the cortex were the penetrations? How long were the electrodes allowed to settle before recording, how much damage was done to tissue during insertion? Do you have data taken over time - how consistent is the pattern across several hours, and how long was the time between the collection of the penetrations shown here?

The impact of the paper is lessened because it emphasizes consistency but not in a consistent manner. Some demonstrations of consistency are shown for CSDs, but not quantified. Figure 4A is used to make a point about consistency in cell density, but across animals, whereas the previous text was pointing out inconsistency across penetrations. What if you took a 40 or 60 um column of tissue and computed cell density, then you would be comparing consistency across potentially similar scales. Overall, it is not clear how all of these different metrics compare quantitatively to each other in terms of consistency.

In many places, the text makes assertions that A is a consistent indicator of B, but then there appear to be clear counterexamples in the data shown in the figures. There is some sense that the reasoning is relying too much on examples, and not enough on statistical quantities.

Overall

Overall, this paper makes a solid argument in favor of using action potentials and stimulus driven responses, instead of CSD measurements, to assign cortical layers to electrode contacts in V1. It is nice to look at the data in this paper and to read the authors' highly educated interpretation and speculation about how useful such measurements will be in general to make layer assignments. It is easy to agree with much of what they say, and to hope that in the future there will be reliable, quantitative methods to make meaningful segmentations of neurons in terms of their differentiated roles in cortical computation. How much this will end up corresponding to the canonical layer numbering that has been used for many decades now remains unclear.

Reviewer #3 (Public Review):

Summary:

Zhang et al. explored strategies for aligning electrophysiological recordings from high-density laminar electrode arrays (Neuropixels) with the pattern of lamination across cortical depth in macaque primary visual cortex (V1), with the goal of improving the spatial resolution of layer identification based on electrophysiological signals alone. The authors compare the current commonly used standard in the field - current source density (CSD) analysis - with a new set of measures largely derived from action potential (AP) frequency band signals. Individual AP band measures provide distinct cues about different landmarks or potential laminar boundaries, and together they are used to subdivide the spatial extent of array recordings into discrete layers, including the very thin layer 4A, a level of resolution unavailable when relying on CSD analysis alone for laminar identification. The authors compare the widths of the resulting subdivisions with previously reported anatomical measurements as evidence that layers have been accurately identified. This is a bit circular, given that they also use these anatomical measurements as guidelines limiting the boundary assignments; however, the strategy is overall sensible and the electrophysiological signatures used to identify layers are generally convincing. Furthermore, by varying the pattern of visual stimulation to target chromatically sensitive inputs known to be partially segregated by layer in V1, they show localized response patterns that lend confidence to their identification of particular sublayers.

The authors compellingly demonstrate the insufficiency of CSD analysis for precisely identifying fine laminar structure, and in some cases its limited accuracy at identifying coarse structure. CSD analysis produced inconsistent results across array penetrations and across visual stimulus conditions and was not improved in spatial resolution by sampling at high density with Neuropixels probes. Instead, in order to generate a typical, informative pattern of current sources and sinks across layers, the LFP signals from the Neuropixels arrays required spatial smoothing or subsampling to approximately match the coarser (50-100 µm) spacing of other laminar arrays. Even with smoothing, the resulting CSDs in some cases predicted laminar boundaries that were inconsistent with boundaries estimated using other measures and/or unlikely given the typical sizes of individual layers in macaque V1. This point alone provides an important insight for others seeking to link their own laminar array recordings to cortical layers.

They next offer a set of measures based on analysis of AP band signals. These measures include analyses of the density, average signal spread, and spike waveforms of single- and multi-units identified through spike sorting, as well as analyses of AP band power spectra and local coherence profiles across recording depth. The power spectrum measures in particular yield compact peaks at particular depths, albeit with some variation across penetrations, whereas the waveform measures most convincingly identified the layer 6-white matter transition. In general, some of the new measures yield inconsistent patterns across penetrations, and some of the authors' explanations of these analyses draw intriguing but rather speculative connections to properties of anatomy and/or responsivity. However, taken as a group, the set of AP band analyses appear sufficient to determine the layer 6-white matter transition with precision and to delineate intermediate transition points likely to correspond to actual layer boundaries.

Strengths:

The authors convincingly demonstrate the potential to resolve putative laminar boundaries using only electrophysiological recordings from Neuropixels arrays. This is particularly useful given that histological information is often unavailable for chronic recordings. They make a clear case that CSD analysis is insufficient to resolve the lamination pattern with the desired precision and offer a thoughtful set of alternative analyses, along with an order in which to consider multiple cues in order to facilitate others' adoption of the strategy. The widths of the resulting layers bear a sensible resemblance to the expected widths identified by prior anatomical measurements, and at least in some cases there are satisfying signatures of chromatic visual sensitivity and latency differences across layers that are predicted by the known connectivity of the corresponding layers. Thus, the proposed analytical toolkit appears to work well for macaque V1 and has strong potential to generalize to use in other cortical regions, though area-targeted selection of stimuli may be required.

Weaknesses:

The waveform measures, and in particular the unit density distribution, are likely to be sensitive to the criteria used for spike sorting, which differ widely among experimenters/groups, and this may limit the usefulness of this particular measure for others in the community. The analysis of detected unit density yields fluctuations across cortical depth which the authors attribute to variations in neural density across layers; however, these patterns seemed particularly variable across penetrations and did not consistently yield peaks at depths that should have high neuronal density, such as layer 2. Therefore, this measure has limited interpretability.

More generally, although the sizes of identified layers comport with typical sizes identified anatomically, a more powerful confirmation would be a direct per-penetration comparison with histologically identified boundaries. Ultimately, the absence of this type of independent confirmation limits the strength of their claim that veridical laminar boundaries can be identified from electrophysiological signals alone.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

In this study, Hoops et al. showed that Netrin-1 and UNC5c can guide dopaminergic innervation from nucleus accumbens to cortex during adolescence in rodent models. 

We showed this with respect to Netrin-1 only. With respect to UNC5c, we showed that the timing of its expression suggests that it may be involved, but did not conduct the UNC5cmanipulation experiments necessary to prove it. We state this clearly in the manuscript.

They found that these dopamine axons project to the prefrontal cortex in a Netrin-1 dependent manner and knocking down Netrin-1 disrupted motor and learning behaviors in mice. 

We would like to clarify that we did not show that learning or motor behaviors are affected. We showed that inhibitory control, measured in the Go/No-Go task, is altered in adulthood.

Furthermore, the authors used hamsters, a seasonal model that is affected by the length of daylight, to demonstrate that the guidance of dopamine axons is mediated by the environmental factor such as daytime length and in sex dependent manner. 

We agree with this characterization of our hamster experiments, but want to emphasize that it is the timing of the adolescent dopamine axon input to the prefrontal cortex what is impacted by daytime length in a sex dependent manner.

Regarding the cell type specificity of Netrin-1 expression, the authors began by stating "this question is not the focus of the study and we consider it irrelevant to the main issue we are addressing, which is where in the forebrain regions we examined Netrin-1+ cells are present." This statement contradicts the exact issue regarding the specificity issue I raised.

We are not sure why the identities of the cell types expressing Netrin-1 are at issue. As a secreted protein, Netrin-1 can be attached to the extracellular cell surface or in the extracellular matrix, where it interacts with its receptors, which are embedded in the cell surfaces of growing axons (Finci et al., 2015; Rajasekharan & Kennedy, 2009). Netrin-1 is expressed by a wide variety of cell types, for example it is expressed in medium spiny neurons in the striatum of rodents as well as in cholinergic neurons (Shatzmiller et al., 2008). However, we cannot see why showing exactly what type(s) of cells have Netrin-1 on their surfaces, or have secreted them into the matrix, would be at issue for our study.

They then went on to show the RNAscope data for Netrin-1 in Figure 2, which showed Netrin-1 mRNA was actually expressed quite ubiquitously in anterior cingulate cortex, dorsopeduncular cortex, infralimbic cortex, prelimbic cortex, etc. 

Figure 2 - this is referring to Author response image 2 of our first response to reviewers.

We agree that Netrin-1 mRNA is present throughout the forebrain. In particular, its presence in the regions mentioned by Reviewer #1 is a key component of our theory for how dopamine axons grow to the prefrontal cortex in adolescence.

In addition, contrary to the authors' statement that Netrin-1 is a "secreted protein", the confocal images in Figure 1 in the rebuttal letter actually show Netrin-1 present in "granule-like" organelles inside the cytoplasm of neurons. 

The rebuttal letter’s Figure 1 is not sufficient to determine the subcellular location of the Netrin-1, however we agree that it is likely that Netrin-1 is present in the cytoplasm of neurons. Indeed, its presence in vesicles in the cytoplasm is to be expected as this is a common mechanism for cells to secrete proteins into the extracellular space (Glasgow et al., 2018). We are not sure whether Reviewer #1’s “granule-like” organelles are in fact secretory vesicles or not, and we do not think our immunohistochemical images are an appropriate method by which to determine this kind of question. We find, however, that a detailed characterization of the subcellular distribution of Netrin-1 is beyond the scope of our study. 

That Netrin-1 is a secreted protein is well-established in the literature (for example, see Glasgow et al., 2018). The confocal images we provide suggest, but do not prove, that it is likely Netrin-1 is present both extracellularly and intracellularly, which is entirely consistent with its synthesis, secretion, and function. It is also consistent with our methodology and findings. 

Finally, the authors presented Figure 7 to indicate the location where virus expressing Netrin-1 shRNA might be located. Again, the brain region targeted was quite focal and most likely did not cover all the Netrin-1+ brain regions in Figure 2. 

Figure 2 - this is referring to Author response image 2 of our first response to reviewers.

Figure 7 - this is referring to Author response image 4 of our first response to reviewers.

We agree with Reviewer #1’s characterization of our experiment. We intended to interrupt the Netrin-1 pathway to the prefrontal cortex, like removing a bridge along a road. The Netrin-1 signal remained intact along the dopamine axon’s route before and after the location of the viral injection, however it was lost at the site of the virus injection. This is like a road remaining intact on either side of a destroyed bridge, but becoming impassable at the location where the bridge was destroyed. We are glad that Reviewer 1 agrees our experimental design achieved the desired outcome (a focal reduction in Netrin-1 expression).

Collectively, these results raised more questions regarding the specificity of Netrin-1 expression in brain regions that are behaviorally relevant to this study.

We do not agree with this assessment. Our manipulation of Netrin-1 expression was highly localized and specific, as Reviewer #1 seems to acknowledge. We are not clear on what questions this might raise that would call into question our findings as described in our manuscript. We have now added the following paragraph to our manuscript:  

“It remains unknown exactly what types of cells are expressing Netrin-1 along the dopamine axon route, and how this expression is regulated to produce the Netrin-1 gradients that guide the dopamine axons. It also remains unclear where the misrouted axons end up in adulthood. Future experiments aimed at addressing these questions will provide further valuable insight into the nature of the “Netrin-1 pathway”. Nonetheless, our results allow us to conclude that Netrin-1 expressing cells “pave the way” for dopamine axons growing to the medial prefrontal cortex.”

With respect to the effectiveness of Netrin-1 knockdown in the animals in this study, the authors cited data in HEK293 cells (Cuesta et al., 2020. Figure 2a), which did not include any statistics, and previously published in vivo data in a separate, independent study (Cuesta et al., 2020. Figure 2c). They do not provide any data regarding the effectiveness of Netrin-1 knockdown in THIS study.

Indeed, we understand the concerns of Reviewer 1 here. This issue was discussed at the time all the experiments (both in the current manuscript and in Cuesta et al., (2020)) were conducted, and we decided that it was sufficient to show the virus was capable of knocking down Netrin-1 in vitro and in vivo in the forebrain. These characterization experiments were published in the first manuscript to present results using the virus, which was Cuesta et al., 2020. However, all experiments from both manuscripts were conducted contemporaneously.

We do not see how repeating the same characterization experiments again is useful. 

Similar concerns regarding UNC5C knockdown (points #6, #7, and #8) were not adequately addressed.

There is no UNC5c knockdown in this manuscript. Furthermore, points #6, #7 and #8 do not deal with UNC5c knockdown. Point #6 is regarding the Netrin-1 virus efficacy, which we discuss above. Points #7 and #8 are requesting numerous additional experiments that we feel are worthy of their own manuscripts, and we do not feel that they call into question the findings we present here. Rather, answering points #7 and #8 would further refine our understanding of how dopamine axons grow to the prefrontal cortex beyond our current manuscript.

In brief, while this study provides a potential role of Netrin-1-UNC5C in target innervation of dopaminergic neurons and its behavioral output in risk-taking, the data lack sufficient evidence to firmly establish the cause-effect relationship.

We do not claim a cause-effect relationship here or anywhere in the manuscript. Concrete establishment of a cause-effect relationship will require several more manuscripts worth of experiments.

Reviewer #2 (Public Review):

In this manuscript, Hoops et al., using two different model systems, identified key developmental changes in Netrin-1 and UNC5C signaling that correspond to behavioral changes and are sensitive to environmental factors that affect the timing of development. They found that Netrin-1 expression is highest in regions of the striatum and cortex where TH+ axons are travelling, and that knocking down Netrin-1 reduces TH+ varicosities in mPFC and reduces impulsive behaviors in a Go-No-Go test. 

We want to point out that we examined the Netrin-1 expression in the septum rather than the striatum but otherwise feel the above description is accurate.

Further, they show that the onset of Unc5 expression is sexually dimorphic in mice, and that in Siberian hamsters, environmental effects on development are also sexually dimorophic. This study addresses an important question using approaches that link molecular, circuit and behavioral changes. Understanding developmental trajectories of adolescence, and how they can be impacted by environmental factors, is an understudied area of neuroscience that is highly relevant to understanding the onset of mental health disorders. I appreciated the inclusion of replication cohorts within the study.

We appreciate Reviewer #2’s comments, which we feel accurately describe our experimental approach and findings, including their limitations.

Reviewer #3 (Public Review):

This study from the Flores group aims at understanding neuronal circuit changes during adolescence which is an ill-defined, transitional period involving dramatic changes in behavior and anatomy. They focus on DA innervation of the prefrontal cortex, and their interaction with the guidance cue Netrin1. They propose DA axons in the PFC increase in the postnatal period, and their density is reduced in a Netrin 1 knockdown, suggesting that Netrin abets the development of this mesocortical pathway. 

We feel it necessary to point out that we are not the first to propose that dopamine axons in the prefrontal cortex increase in the postnatal period.  This is well-established and was first documented in rodents in the 1980s (Kalsbeek et al., 1988). Otherwise we agree with Reviewer 3’s characterization.

In such mice impulsivity gauged by a go-no go task is reduced. They then provide some evidence that Unc5c is developmentally regulated in DA axons. Finally they use an interesting hamster model, to study the effect of light hours on mesocortical innervation, and make some interesting observations about the timing of innervation and Unc5c expression, and the fact that females housed in winter day length conditions display an accelerated innervation of the prefrontal cortex.

We agree with Reviewer #3’s characterization of our study and findings here.

Comments on the revision. Several points were addressed; some remain to be addressed.

(4) It's not clear to me that TH doesnt stain noradrenergic axons in the PFC. See Islam and Blaess, 2021, and references therein.

Presuming that Reviewer #3 is referring to Islam et al. (2021), the review they cite supports our position that TH-stained axons in the forebrain are by-and-large dopamine axons.

Nonetheless, Islam et al. do point out that it is important to keep in mind that TH-positive axons have a slight possibility of being noradrenaline axons. We are very conscious of this possibility and are careful to minimize this risk. As we state in the methods, we only examine axons that are morphologically consistent with dopamine axons and are localized to areas within the forebrain where dopamine axons are known to innervate, in addition to being THpositive. The localization and morphology of noradrenaline axons in the forebrain is different from that of dopamine axons. This is stated in our methods on lines 76-94, where we describe in detail the differentiation between dopamine and norepinephrine axons and include a full list of relevant citations.

(6) The Netrin knockdown data provided is from a previous study/samples.

Indeed, however the experiments for the two manuscripts were conducted contemporaneously. We believe two sets of validation experiments are not required.

(8) While the authors make the argument that the behavior is linked to DA, they still haven't formally tested it, in my opinion.

We agree that we have not formally tested this link. However, we disagree that we claim to have established a formal link in our manuscript.

(1). Fig 3, UNc 5c  levels are not yet quantified. Furthermore, I agree with the previous reviewer that Unc5C knockdown would corroborate key aspects of the model.

We present UNC5c quantities for mice in our first response to reviewers (Figure 11 therein) however we did not do so for the hamsters due to the time involved. We are planning further experiments with the hamsters and may include quantification of UNC5c in the nucleus accumbens at such time. However, we do not feel its absence from this manuscript calls into question our findings.

With regards to the UNC5c knockdown, we agree it would be an informative extension of our findings here, but again we do not feel that it is necessary to corroborate our current findings.

New - Developmental trajectory of prefrontal TH-positive axons from early adolescence to adulthood is similar in male and female rats, (Willing Juraska et al., 2017). This needs discussion.

Willing et al. (2017) reported an increase in prefrontal dopamine density during adolescence in male and female rats, with a non-significant trend towards an earlier increase in females.

This is in line with our current results in mice indicating that the timing of dopamine axon targeting and growth is sex specific. We are currently testing this idea directly using intersectional viral tracing methods. We now added the following sentence to the manuscript: 

“Differences in the precise timing of dopamine innervation to the PFC in adolescence have been suggested by findings reported in male and female rats (Willing et al., 2017)”.

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Kalsbeek, A., Voorn, P., Buijs, R. M., Pool, C. W., & Uylings, H. B. M. (1988). Development of the Dopaminergic Innervation in the Prefrontal Cortex of the Rat. The Journal of Comparative Neurology, 269(1), 58–72. https://doi.org/10.1002/cne.902690105

Rajasekharan, S., & Kennedy, T. E. (2009). The netrin protein family. Genome Biology, 10(9), 239. https://doi.org/10.1186/gb-2009-10-9-239

Shatzmiller, R. A., Goldman, J. S., Simard-Émond, L., Rymar, V., Manitt, C., Sadikot, A. F., & Kennedy, T. E. (2008). Graded expression of netrin-1 by specific neuronal subtypes in the adult mammalian striatum. Neuroscience, 157(3), 621–636. https://doi.org/10.1016/j.neuroscience.2008.09.031

Willing, J., Cortes, L. R., Brodsky, J. M., Kim, T., & Juraska, J. M. (2017). Innervation of the medial prefrontal cortex by tyrosine hydroxylase immunoreactive fibers during adolescence in male and female rats. Developmental Psychobiology, 59(5), 583–589. https://doi.org/10.1002/dev.21525

eLife assessment

This study addresses an important, understudied question using approaches that link molecular, circuit, and behavioral changes. The findings that Netrin-1 and UNC5c can guide dopaminergic innervation from the nucleus accumbens to the cortex during adolescence are solid. The data showing that the onset of Unc5 expression is sexually dimorphic in mice, and that in Siberian hamsters environmental effects on development are also sexually dimorphic are also solid. Reviewers identified significant gaps in evidence for specificity of Netrin-1 expression, which, if filled, would strengthen the evidence for some of the claims. Future work would also benefit from Unc5C knockdown to corroborate the results and investigation of the cause-effect relationship. This paper will be of interest to those interested in neural development, sex differences, and/or dopamine function.

Reviewer #1 (Public Review):

In this study, Hoops et al. showed that Netrin-1 and UNC5c can guide dopaminergic innervation from nucleus accumbens to cortex during adolescence in rodent models. They found that these dopamine axons project to the prefrontal cortex in a Netrin-1 dependent manner and knocking down Netrin-1 disrupted motor and learning behaviors in mice. Furthermore, the authors used hamsters, a seasonal model that is affected by the length of daylight, to demonstrate that the guidance of dopamine axons is mediated by the environmental factor such as daytime length and in sex dependent manner.

Regarding the cell type specificity of Netrin-1 expression, the authors began by stating "this question is not the focus of the study and we consider it irrelevant to the main issue we are addressing, which is where in the forebrain regions we examined Netrin-1+ cells are present." This statement contradicts the exact issue regarding the specificity issue I raised. They then went on to show the RNAscope data for Netriin-1 in Figure 2, which showed Netrin-1 mRNA was actually expressed quite ubiquitously in anterior cingulate cortex, dorsopeduncular cortex, infralimbic cortex, prelimbic cortex, etc. In addition, contrary to the authors' statement that Netrin-1 is a "secreted protein", the confocal images in Figure 1 in the rebuttal letter actually show Netrin-1 present in "granule-like" organelles inside the cytoplasm of neurons. Finally, the authors presented Figure 7 to indicate the location where virus expressing Netrin-1 shRNA might be located. Again, the brain region targeted was quite focal and most likely did not cover all the Netrin-1+ brain regions in Figure 2. Collectively, these results raised more questions regarding the specificity of Netrin-1 expression in brain regions that are behaviorally relevant to this study.

With respect to the effectiveness of Netrin-1 knockdown in the animals in this study, the authors cited data in HEK293 cells (Figure 5), which did not include any statistics, and previously published in vivo data in a separate, independent study (Figure 6). They do not provide any data regarding the effectiveness of Netrin-1 knockdown in THIS study.

Similar concerns regarding UNC5C knockdown (points #6, #7, and #8) were not adequately addressed.

In brief, while this study provides a potential role of Netrin-1-UNC5C in target innervation of dopaminergic neurons and its behavioral output in risk-taking, the data lack sufficient evidence to firmly establish the cause-effect relationship.

Reviewer #2 (Public Review):

In this manuscript, Hoops et al., using two different model systems, identified key developmental changes in Netrin-1 and UNC5C signaling that correspond to behavioral changes and are sensitive to environmental factors that affect the timing of development. They found that Netrin-1 expression is highest in regions of the striatum and cortex where TH+ axons are travelling, and that knocking down Netrin-1 reduces TH+ varicosities in mPFC and reduces impulsive behaviors in a Go-No-Go test. Further, they show that the onset of Unc5 expression is sexually dimorphic in mice, and that in Siberian hamsters, environmental effects on development are also sexually dimorophic. This study addresses an important question using approaches that link molecular, circuit and behavioral changes. Understanding developmental trajectories of adolescence, and how they can be impacted by environmental factors, is an understudied area of neuroscience that is highly relevant to understanding the onset of mental health disorders. I appreciated the inclusion of replication cohorts within the study.

Reviewer #3 (Public Review):

This study from the Flores group aims at understanding neuronal circuit changes during adolescence which is an ill-defined, transitional period involving dramatic changes in behavior and anatomy. They focus on DA innervation of the prefrontal cortex, and their interaction with the guidance cue Netrin-1. They propose DA axons in the PFC increase in the postnatal period, and their density is reduced in a Netrin 1 knockdown, suggesting that Netrin abets the development of this mesocortical pathway. In such mice impulsivity gauged by a go-no-go task is reduced. They then provide some evidence that Unc5c is developmentally regulated in DA axons. Finally they use an interesting hamster model, to study the effect of light hours on mesocortical innervation, and make some interesting observations about the timing of innervation and Unc5c expression, and the fact that females housed in winter day length conditions display an accelerated innervation of the prefrontal cortex.

Comments on the revision. Several points were addressed; some remain to be addressed.

4. It's not clear to me that TH doesn't stain noradrenergic axons in the PFC. See Islam and Blaess, 2021, and references therein.

6. The Netrin knockdown data provided is from a previous study/samples.

8. While the authors make the argument that the behavior is linked to DA, they still haven't formally tested it, in my opinion.

13. Fig 3, UNc 5c levels are not yet quantified. Furthermore, I agree with the previous reviewer that Unc5C knockdown would corroborate key aspects of the model.

New - Developmental trajectory of prefrontal TH-positive axons from early adolescence to adulthood is similar in male and female rats, (Willing Juraska et al., 2017). This needs discussion.

Editors note:<br /> should you choose to revise your manuscript, please include degrees of freedom in your statistical reporting.

eLife assessment

This important study uses state-of-the-art, multi-region two-photon calcium imaging to characterize the statistics of functional connectivity between visual cortical neurons. The evidence supporting the conclusions is incomplete; currently, alternative interpretations of the results cannot be ruled out. With new analyses strengthening the conclusions, the work would be of broad interest to neuroscientists interested in the visual cortex and inter-area communication.

Reviewer #1 (Public Review):

Using multi-region two-photon calcium imaging, the manuscript meticulously explores the structure of noise correlations (NCs) across the mouse visual cortex and uses this information to make inferences about the organization of communication channels between primary visual cortex (V1) and higher visual areas (HVAs). Using visual responses to grating stimuli, the manuscript identifies 6 tuning groups of visual cortex neurons and finds that NCs are highest among neurons belonging to the same tuning group whether or not they are found in the same cortical area. The NCs depend on the similarity of tuning of the neurons (their signal correlations) but are preserved across different stimulus sets - noise correlations recorded using drifting gratings are highly correlated with those measured using naturalistic videos. Based on these findings, the manuscript concludes that populations of neurons with high NCs constitute discrete communication channels that convey visual signals within and across cortical areas.

Experiments and analyses are conducted to a high standard and the robustness of noise correlation measurements is carefully validated. However, the interpretation of noise correlation measurements as a proxy from network connectivity is fraught with challenges. While the data clearly indicates the existence of distributed functional ensembles, the notion of communication channels implies the existence of direct anatomical connections between them, which noise correlations cannot measure.

The traditional view of noise correlations is that they reflect direct connectivity or shared inputs between neurons. While it is valid in a broad sense, noise correlations may reflect shared top-down input as well as local or feedforward connectivity. This is particularly important since mouse cortical neurons are strongly modulated by spontaneous behavior (e.g. Stringer et al, Science, 2019). Therefore, noise correlation between a pair of neurons may reflect whether they are similarly modulated by behavioral state and overt spontaneous behaviors. Consequently, noise correlation alone cannot determine whether neurons belong to discrete communication channels.

Behavioral modulation can influence the gain of sensory-evoked responses (Niell and Stryker, Neuron, 2010). This can explain why signal correlation is one of the best predictors of noise correlations as reported in the manuscript. A pair of neurons that are similarly gain-modulated by spontaneous behavior (e.g. both active during whisking or locomotion) will have higher noise correlations if they respond to similar stimuli. Top-down modulation by the behavioral state is also consistent with the stability of noise correlations across stimuli. Therefore, it is important to determine to what extent noise correlations can be explained by shared behavioral modulation.

Reviewer #2 (Public Review):

Summary:

This groundbreaking study characterizes the structure of activity correlations over a millimeter scale in the mouse cortex with the goal of identifying visual channels, specialized conduits of visual information that show preferential connectivity. Examining the statistical structure of the visual activity of L2/3 neurons, the study finds pairs of neurons located near each other or across distances of hundreds of micrometers with significantly correlated activity in response to visual stimulation. These highly correlated pairs have closely related visual tuning sharing orientation and/or spatial and/or temporal preference as would be expected from dedicated visual channels with specific connectivity.

Strengths:

The study presents best-in-class mesoscopic-scale 2-photon recordings from neuronal populations in pairs of visual areas (V1-LM, V1-PM, V1-AL, V1-LI). The study employs diverse visual stimuli that capture some of the specialization and heterogeneity of neuronal tuning in mouse visual areas. The rigorous data quantification takes into consideration functional cell groups as well as other variables that influence trial-to-trial correlations (similarity of tuning, neuronal distance, receptive field overlap). The paper convincingly demonstrates the robustness of the clustering analysis and of the activity correlation measurements. The calcium imaging results convincingly show that noise correlations are correlated across visual stimuli and are strongest within cell classes which could reflect distributed visual channels. A simple simulation is provided that suggests that recurrent connectivity is required for the stimulus invariance of the results. The paper is well-written and conceptually clear. The figures are beautiful and clear. The arguments are well laid out and the claims appear in large part supported by the data and analysis results (but see weaknesses).

Weaknesses:

An inherent limitation of the approach is that it cannot reveal which anatomical connectivity patterns are responsible for observed network structure. The modeling results presented, however, suggest interestingly that a simple feedforward architecture may not account for fundamental characteristics of the data. A limitation of the study is the lack of a behavioral task. The paper shows nicely that the correlation structure generalizes across visual stimuli. However, the correlation structure could differ widely when animals are actively responding to visual stimuli. I do think that, because of the complexity involved, a characterization of correlations during a visual task is beyond the scope of the current study.

An important question that does not seem addressed (but it is addressed indirectly, I could be mistaken) is the extent to which it is possible to obtain reliable measurements of noise correlation from cell pairs that have widely distinct tuning. L2/3 activity in the visual cortex is quite sparse. The cell groups laid out in Figure S2 have very sharp tuning. Cells whose tuning does not overlap may not yield significant trial-to-trial correlations because they do not show significant responses to the same set of stimuli, if at all any time. Could this bias the noise correlation measurements or explain some of the dependence of the observed noise correlations on signal correlations/similarity of tuning? Could the variable overlap in the responses to visual responses explain the dependence of correlations on cell classes and groups?

With electrophysiology, this issue is less of a problem because many if not most neurons will show some activity in response to suboptimal stimuli. For the present study which uses calcium imaging together with deconvolution, some of the activity may not be visible to the experimenters. The correlation measure is shown to be robust to changes in firing rates due to missing spikes. However, the degree of overlap of responses between cell pairs and their consequences for measures of noise correlations are not explored.

Beyond that comment, the remaining issues are relatively minor issues related to manuscript text, figures, and statistical analyses. There are typos left in the manuscript. Some of the methodological details and results of statistical testing also seem to be missing. Some of the visuals and analyses chosen to examine the data (e.g., box plots) may not be the most effective in highlighting differences across groups. If addressed, this would make a very strong paper.

Reviewer #3 (Public Review):

Summary:

Yu et al harness the capabilities of mesoscopic 2P imaging to record simultaneously from populations of neurons in several visual cortical areas and measure their correlated variability. They first divide neurons into 65 classes depending on their tuning to moving gratings. They found the pairs of neurons of the same tuning class show higher noise correlations (NCs) both within and across cortical areas. Based on these observations and a model they conclude that visual information is broadcast across areas through multiple, discrete channels with little mixing across them.

NCs can reflect indirect or direct connectivity, or shared afferents between pairs of neurons, potentially providing insight on network organization. While NCs have been comprehensively studied in neuron pairs of the same area, the structure of these correlations across areas is much less known. Thus, the manuscripts present novel insights into the correlation structure of visual responses across multiple areas.

Strengths:

The study uses state-of-the art mesoscopic two-photon imaging.

The measurements of shared variability across multiple areas are novel.

The results are mostly well presented and many thorough controls for some metrics are included.

Weaknesses:

I have concerns that the observed large intra-class/group NCs might not reflect connectivity but shared behaviorally driven multiplicative gain modulations of sensory-evoked responses. In this case, the NC structure might not be due to the presence of discrete, multiple channels broadcasting visual information as concluded. I also find that the claim of multiple discrete broadcasting channels needs more support before discarding the alternative hypothesis that a continuum of tuning similarity explains the large NCs observed in groups of neurons.

Specifically:

Major concerns:

(1) Multiplicative gain modulation underlying correlated noise between similarly tuned neurons

(1a) The conclusion that visual information is broadcasted in discrete channels across visual areas relies on interpreting NC as reflecting, direct or indirect connectivity between pairs, or common inputs. However, a large fraction of the activity in the mouse visual system is known to reflect spontaneous and instructed movements, including locomotion and face movements, among others. Running activity and face movements are some of the largest contributors to visual cortex activity and exert a multiplicative gain on sensory-evoked responses (Niell et al, Stringer et al, among others). Thus, trial-by-fluctuations of behavioral state would result in gain modulations that, due to their multiplicative nature, would result in more shared variability in cotuned neurons, as multiplication affects neurons that are responding to the stimulus over those that are not responding ( see Lin et al, Neuron 2015 for a similar point).

As behavioral modulations are not considered, this confound affects most of the conclusions of the manuscript, as it would result in larger NCs the more similar the tuning of the neurons is, independently of any connectivity feature. It seems that this alternative hypothesis can explain most of the results without the need for discrete broadcasting channels or any particular network architecture and should be addressed to support its main claims.

(1b) In Figure 5 the observations are interpreted as evidence for NCs reflecting features of the network architecture, as NCs measured using gratings predicted NC to naturalistic videos. However, it seems from Figure 5 A that signal correlations (SCs) from gratings had non-zero correlations with SCs during naturalistic videos (is this the case?). Thus, neurons that are cotuned to gratings might also tend to be coactivated during the presentation of videos. In this case, they are also expected to be susceptible to shared behaviorally driven fluctuations, independently of any circuit architecture as explained before. This alternative interpretation should be addressed before concluding that these measurements reflect connectivity features.

(2) Discrete vs continuous communication channels

(2a) One of the author's main claims is that the mouse cortical network consists of discrete communication channels. This discreteness is based on an unbiased clustering approach to the tuning of neurons, followed by a manual grouping into six categories in relation to the stimulus space. I believe there are several problems with this claim. First, this clustering approach is inherently trying to group neurons and discretise neural populations. To make the claim that there are 'discrete communication channels' the null hypothesis should be a continuous model. An explicit test in favor of a discrete model is lacking, i.e. are the results better explained using discrete groups vs. when considering only tuning similarity? Second, the fact that 65 classes are recovered (out of 72 conditions) and that manual clustering is necessary to arrive at the six categories is far from convincing that we need to think about categorically different subsets of neurons. That we should think of discrete communication channels is especially surprising in this context as the relevant stimulus parameter axes seem inherently continuous: spatial and temporal frequency. It is hard to motivate the biological need for a discretely organized cortical network to process these continuous input spaces.

(2b) Consequently, I feel the support for discrete vs continuous selective communication is rather inconclusive. It seems that following the author's claims, it would be important to establish if neurons belong to the same groups, rather than tuning similarity is a defining feature for showing large NCs.

Finally, as stated in point 1, the larger NCs observed within groups than across groups might be due to the multiplicative gain of state modulations, due to the larger tuning similarity of the neurons within a class or group.

Author Response:

We appreciate the constructive reviews. We have performed additional analysis to address reviewer concerns, and we will submit a full revision in the near future. Our new analysis confirms that the visual stimulus can account for about a third of the variance in population neural activity. Pupil dynamics only account for a small fraction of the trial-to-trial variability, less than six percent. Once we regress out the stimulus responses and the pupil dynamics, we can use the network activity to predict the trial-to-trial variability of single neuron responses, and about eight percent of the variance is explained. Thus it appears as though multiplicative gain cannot account for the results. As for the concerns about missing spikes, we would like to direct readers to the supplementary figure that addresses that concern. The analysis shows that the correlation measurements are robust to the imprecisions of spike inference from calcium imaging data. Finally, we would also like to take the opportunity to clarify that we make no claim as to the discreteness of tuning classes. The GMM analysis was performed to obtain a data-driven, granular categorization of neuron tuning, to support detailed statistical analysis. We take no position on the discreteness or lack thereof of these groups. We agree that it is an interesting question, and we are happy to provide additional analysis in the revision to address this question. Our main result on functional connectivity structure holds regardless of the discreteness of neuron tuning selectivity.

eLife assessment

The authors expand the concept of a new layer to training immunity, which is currently being highlighted by several colleagues in the field. The work provides important hints to understand end-stage renal disease. Overall, the rational approach leads to experimental results that are solid.

Reviewer #1 (Public Review):

In this study, Kim et al. investigated the mechanism by which uremic toxin indoxyl sulfate (IS) induces trained immunity, resulting in augmented pro-inflammatory cytokine production such as TNF and IL-6. The authors claim that IS treatment induced epigenetic and metabolic reprogramming, and the aryl hydrocarbon receptor (AhR)-mediated arachidonic acid pathway is required for establishing trained immunity in human monocytes. They also demonstrated that uremic sera from end-stage renal disease (ESRD) patients can generate trained immunity in healthy control-derived monocytes.

These are interesting results that introduce the important new concept of trained immunity and its importance in showing endogenous inflammatory stimuli-induced innate immune memory. Additional evidence proposing that IS plays a critical role in the initiation of inflammatory immune responses in patients with CKD is also interesting and a potential advance of the field.

Comments on the revised version:

In the revised manuscripts, the authors have addressed essentially almost all of the points raised by the reviewers and have revised the manuscript accordingly. The additional comments improved the manuscript and strengthened the overall impact of the paper.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

In this study, Kim et al. investigated the mechanism by which uremic toxin indoxyl sulfate (IS) induces trained immunity, resulting in augmented pro-inflammatory cytokine production such as TNF and IL6. The authors claim that IS treatment induced epigenetic and metabolic reprogramming, and the aryl hydrocarbon receptor (AhR)-mediated arachidonic acid pathway is required for establishing trained immunity in human monocytes. They also demonstrated that uremic sera from end-stage renal disease (ESRD) patients can generate trained immunity in healthy control-derived monocytes.

These are interesting results that introduce the important new concept of trained immunity and its importance in showing endogenous inflammatory stimuli-induced innate immune memory. Additional evidence proposing that IS plays a critical role in the initiation of inflammatory immune responses in patients with CKD is also interesting and a potential advance of the field. This study is in large part well done, but some components of the study are still incomplete and additional efforts are required to nail down the main conclusions.

Thank you very much for your positive feedback.

Specific comments:

(1) Of greatest concern, there are concerns about the rigor of these experiments, whether the interpretation and conclusions are fully supported by the data. (1) Although many experiments have been sporadically conducted in many fields such as epigenetic, metabolic regulation, and AhR signaling, the causal relationship between each mechanism is not clear. (2) Throughout the manuscript, no distinction was made between the group treated with IS for 6 days and the group treated with the second LPS (addressed below). (3) Besides experiments using non-specific inhibitors, genetic experiments including siRNA or KO mice should be examined to strengthen and justify central suggestions.

We are grateful for the invaluable constructive feedback provided. 

(1) In response to the reviewer's feedback, we conducted additional experiments employing appropriate inhibitors to investigate the causal relationship among the AhR pathway, epigenetic modifications, and metabolic rewiring in IS-induced trained immunity. Notably, metabolic rewiring, particularly the upregulation of aerobic glycolysis via the mTORC1 signaling pathway, stands as a pivotal mechanism underlying the induction of trained immunity through the modulation of epigenetic modifications (Riksen NP et al. Figure 1). Initially, we assessed the enrichment of H3K4me3 at 6-day on promoters of TNFA and IL6 loci after treatment of zileuton, an inhibitor of ALOX5, and 2-DG, a glycolysis inhibitor. Additionally, we evaluated the alteration in the activity of S6K, a downstream molecule of mTORC1, following zileuton treatment. Our findings indicate that AhR-dependent arachidonic acid (AA) signaling induces epigenetic modifications, albeit without inducing metabolic rewiring, in IS-induced trained immunity (Author response image 1). However, IS stimulation promotes mTORC1-mediated glycolysis in an AhR-independent manner. Notably, inhibition of glycolysis with 2-DG impacts epigenetic modifications. We have updated Figure 7 of the revised manuscript to incorporate these additional experimental findings, elucidating the correlation between the diverse mechanisms implicated in IS-induced innate immune memory (Fig. 7 in the revised manuscript). These data have been integrated into the revised manuscript as Figure 3D and 5I, and supplementary Figure 5I.

(2) We apologize for any confusion arising from the unclear description regarding the distinction between the group treated with IS for 6 days and the group subjected to secondary lipopolysaccharide (LPS) stimulation. It is imperative to clarify that induction of trained immunity necessitates 1 day of IS stimulation followed by 5 days of rest, rendering the 6th day sample representative of a trained state. Subsequent to this, a 24-hour LPS stimulation is applied, designating the 7th day sample as a secondary LPS-stimulated cell. This clarification is now explicitly indicated throughout the entirety of Figure 1A and Figure 3A in the revised manuscript.

(3) In accordance with your feedback, we performed siRNA knockdown of AhR and ALOX5 in primary human monocytes. AhR knockdown markedly attenuated the mRNA expression of TNF-α and IL-6, which are augmented in IS-trained macrophages. Similarly, knockdown of ALOX5 using ALOX5 siRNA abrogated the increase in TNF-α and IL-6 levels upon LPS stimulation in IS-trained macrophages (Author response image 2). Our experiments utilizing AhR siRNA corroborate the involvement of AhR in the expression of AA pathway-related molecules, such as ALOX5, ALOX5AP, and LTB4R1, in IS-induced trained immunity. These data have been incorporated into the revised manuscript as Figure 4E and 5G, and supplementary Figure 5H.  

Author response image 1.

Epigenetic modification is regulated by arachidonic acid (AA) pathway and metabolic rewiring, but metabolic rewiring is not affected by the AA pathway. A-B. Monocytes were pre-treated with zileuton (ZLT), an inhibitor of ALOX5, or 2DG, a glycolysis inhibitor, followed by stimulation with IS for 24 hours. After a resting period of 5 days, the enrichment of H3K4me3 on the promoters of TNFA and IL6 loci was assessed. Normalization was performed using 2% input. C. Monocytes were pre-treated with zileuton (ZLT) and stimulated with IS for 24 hr. Cell lysates were immunoblotted for phosphorylated S6 Kinase, with β-actin serving as a normalization control. Band intensities in the immunoblots were quantified using densitometry. D, A schematic representation of the mechanistic framework underlying IS-trained immunity. Bar graphs show the mean ± SEM. * = p < 0.05, **= p < 0.01, and *** = p < 0.001 by two-tailed paired t-test.

Author response image 2.

Inhibition of IS-trained immunity by knockdown of AhR or ALOX5 in human monocytes. A-C. Human monocytes were transfected with siRNA targeting AhR (siAhR), ALOX5 (siALOX5), or negative control (siNC) for 1 day, followed by stimulation with IS for 24 hours. After a resting period of 5 days, cells were re-stimulated with LPS for 24 hours. mRNA expression levels of AhR and ALOX5 at 1 day after transfection, and TNF-α and IL-6 at 1 day after LPS treatment, were assessed using RT-qPCR. D. Human monocytes were transfected with AhR siRNA or negative control (NC) siRNA for 1 day, followed by stimulation with IS for 24 hours. After resting for 5 days, mRNA expression levels of ALOX5, ALOX5AP, and LTB4R1 were analyzed using RT-qPCR. Bar graphs show the mean ± SEM. * = p < 0.05, ** = p < 0.01, and *** = p < 0.001 by two-tailed paired t-test.  

(2) The authors showed that IS-trained monocytes showed no change in TNF or IL-6, but increased the expression levels of TNF and IL-6 in response to the second LPS (Fig. 1B). This suggests that the different LPS responsiveness in IS-trained monocytes caused altered gene expression of TNF and IL6. However, the authors also showed that IS-trained monocytes without LPS stimulation showed increased levels of H3K4me3 at the TNF and IL-6 loci, as well as highly elevated ECAR and OCR, leading to no changes in TNF and IL-6. Therefore, it is unclear why or how the epigenetic and metabolic states of IS-trained monocytes induce different LPS responses. For example, increased H3K4me3 in HK2 and PFKP is important for metabolic rewiring, but why increased H3K4me3 in TNF and IL6 does not affect gene expression needs to be explained.

We acknowledge the constructive critiques provided by the reviewer. While epigenetic modifications in the promoters of TNF-α, IL-6, HK2, and PFKP (Figure 3B and Supplementary Figure 3C in the revised manuscript), and metabolic rewiring (Figure 2A-D in the revised manuscript) were observed in IS-trained macrophages at 6 days prior to LPS stimulation, these macrophages do not exhibit an increase in TNF-α and IL-6 mRNA and protein levels before LPS stimulation. This lack of response is attributed to a 5-day resting period, allowing the macrophages to revert to a non-activated state, as depicted in Author response image 3 and 4. This phenomenon aligns with the concept of typical trained immunity.

Trained immunity is characterized by the long-term functional reprogramming of innate immune cells, which is evoked by various primary insults and which leads to an altered response towards a second challenge after the return to a non-activated state. Metabolic and epigenetic reprogramming events during the primary immune response persist partially even after the initial stimulus is removed. Upon a secondary challenge, trained innate immune cells exhibit a more robust and more prompt response than the initial response (Netea MG et al. Defining trained immunity and its role in health and disease. Nat Rev Immunol. 2020 Jun;20(6):375-388).

Numerous studies have demonstrated the observation of epigenetic modifications in the promoters of TNF-α and IL-6, and metabolic rewiring prior to LPS stimulation as a secondary challenge. However, cytokine production is contingent on LPS stimulation (Arts RJ et al. Glutaminolysis and Fumarate Accumulation Integrate Immunometabolic and Epigenetic Programs in Trained Immunity. Cell Metab. 2016 Dec 13;24(6):807-819; Arts RJW et al. Immunometabolic Pathways in BCG-Induced Trained Immunity. Cell Rep. 2016 Dec 6;17(10):2562-2571; Ochando J et al. Trained immunity - basic concepts and contributions to immunopathology. Nat Rev Nephrol. 2023 Jan;19(1):23-37). The prolonged presence of higher levels of H3K4me3 on immune gene promoters, even after returning to baseline, is associated with open chromatin and results in a more rapid and stronger response, such as cytokine production, upon a secondary insult (Netea MG et al. Defining trained immunity and its role in health and disease. Nat Rev Immunol. 2020 Jun;20(6):375-388).

The results in Figure 1B may be interpreted as indicating different LPS responsiveness in IStrained monocytes caused altered gene expression of TNF and IL-6. However, it is plausible that trained immune cells respond more robustly even to low concentrations of LPS. In fact, the aim of this experiment was to determine the appropriate LPS concentration.

Author response image 3.

The changes in mRNA and protein level of TNF-α and IL-6 during induction of IS-trained immunity. Human monocytes were treated with or without IS (1 mM) for 24 hrs, succeeded by 5-day resting period to induce trained immunity. Cells were stimulated with LPS for 24 hrs. Protein and mRNA levels were assessed by ELISA and RT-qPCR, respectively. Bar graphs show the mean ± SEM. * = p < 0.05 and **= p < 0.01, by two-tailed paired t-test.

Author response image 4.

The changes in mRNA of HK2 and PFKP induced by IS during induction of IS-trained immunity. Human monocytes were treated with or without IS (1 mM) for 24 hrs, succeeded by 5-day resting period to induce trained immunity. mRNA levels were assessed by RT-qPCR. Bar graphs show the mean ± SEM. * = p < 0.05 by two-tailed paired ttest.

(3) The authors used human monocytes cultured in human serum without growth factors such as MCSF for 5-6 days. When we consider the short lifespan of monocytes (1-3 days), the authors need to explain the validity of the experimental model.

We appreciate the reviewer’s constructive critiques. As pointed out by the reviewer, human circulating CD14+ monocytes exhibit a relatively short lifespan (1-3 days) when cultured in the absence of growth factors (Patel AA et al. The fate and lifespan of human monocyte subsets in steady state and systemic inflammation. J Exp Med. 2017 Jul 3;214(7):1913-1923). In this study, purified CD14+ monocytes were subjected to adherent culture for a duration of 7 days in RPMI1640 media supplemented with 10% human AB serum, a standard in vitro culture protocol widely employed in studies focusing on trained immunity (Domínguez-Andrés J et al. In vitro induction of trained immunity in adherent human monocytes. STAR Protoc. 2021 Feb 24;2(1):100365). In response to the reviewer's suggestions, we assessed cell viability on days 0, 1, 4, and 6, utilizing the WST assay. Despite a marginal reduction in cell viability observed at day 1, attributed to detachment from the culture plate, the cultured monocytes exhibited a notable enhancement in cell viability on days 4 and 6 when compared to days 0 or 1 (Author response image 5).

It has been demonstrated that the adhesion of human monocytes to a cell culture dish leads to their activation and induces the synthesis of substantial amounts of IL-1β mRNA as observed in monocytes adherent to extracellular matrix components such as fibronectin and collagen.

Morphologically, human adherent monocytes cultured with 10% human serum appear to undergo partial differentiation into macrophages by day 6, potentially explaining the observed lack of decrease in monocyte viability. Notably, Safi et al. have reported that adherent monocytes cultured with 10% human serum exhibit no significant difference in cell viability over a 7-day period when compared to cultures supplemented with growth factors such as M-CSF and IL-3 (Safi W et al. Differentiation of human CD14+ monocytes: an experimental investigation of the optimal culture medium and evidence of a lack of differentiation along the endothelial line. Exp Mol Med. 2016 Apr 15;48(4):e227).

Author response image 5.

Viability of human monocytes during the induction of trained immunity. Purified human monocytes were seeded on plates with RPIM1640 media supplemented with 10% human AB serum. Cell viability was assessed on days 0, 1, 4, and 6 utilizing the WST assay (Left panel). Cell morphology was examined under a light-inverted microscope at the indicated times (Right panel).

(4) The authors' ELISA results clearly showed increased levels of TNF and IL-6 proteins, but it is well established that LPS-induced gene expression of TNF and IL-6 in monocytes peaked within 1-4 hours and returned to baseline by 24 hours. Therefore, authors need to investigate gene expression at appropriate time points.

We appreciate the valuable constructive feedback provided by the reviewer. As indicated by the reviewer, the LPS-induced gene expression of TNF-α and IL-6 in IS-trained monocytes exhibited a peak within the initial 1 to 4 hours, followed by a decrease by the 24-hour time point, as illustrated in Author response image 6. Nevertheless, the mRNA expression levels of TNFα and IL-6 were still elevated at the 24-hour mark. Furthermore, the protein levels of both TNFα and IL-6 apparently increased 24 hours after LPS stimulation. Due to technical constraints, sample collection had to be conducted at a single time point, and the 24-hour post-stimulation interval was deemed optimal for this purpose.

Author response image 6.

Kinetics of protein and mRNA expression of TNF-α and IL-6 after treatment of LPS as secondary insult in IS-trained monocytes. IS-trained cells were re-stimulated by LPS (10 ng/ml) for the indicated time. The supernatant and lysates were collected for ELISA assay and RT-qPCR analysis, respectively. Bar graphs show the mean ± SEM. * = p <0.05 and **= p < 0.01, by two-tailed paired t-test.

(5) It is a highly interesting finding that IS induces trained immunity via the AhR pathway. The authors also showed that the pretreatment of FICZ, an AhR agonist, was good enough to induce trained immunity in terms of the expression of TNF and IL-6. However, from this point of view, the authors need to discuss why trained immunity was not affected by kynurenic acid (KA), which is a well-known AhR ligand accumulated in CKD and has been reported to be involved in innate immune memory mechanisms (Fig. S1A).

We appreciate the constructive criticism provided by the reviewer, and we comprehend the raised points. In our initial experiments, we hypothesized that kynurenic acid (KA), an aryl hydrocarbon receptor (AhR) ligand, might instigate trained immunity in monocytes, despite KA not being our primary target uremic toxin. However, our findings, as depicted in Fig. S1A, demonstrated that KA did not induce trained immunity. Notably, KA-treated monocytes exhibited induction of CYP1B1, an AhR-responsive gene, and elevated levels of TNF-α and IL-6 mRNA at 24 hours post-treatment, comparable to FICZ-treated monocytes. This observation underscores KA's role as an AhR ligand in human monocytes, as emphasized by the reviewer. 

Of particular interest, proteins associated with the arachidonic acid pathway, such as ALOX5 and ALOX5AP - integral to the mechanisms underlying IS-induced trained immunity - did not exhibit an increase at day 6 following KA treatment, in contrast to the significant elevation observed with IS and FICZ treatments (Author response image 7). The rationale behind this disparity remains unknown, necessitating further investigation to elucidate the underlying factors. These data have been incorporated into the revised manuscript as Supplementary Figure 5C.

Author response image 7.

Divergent impact of AhR agonists, especially IS, FICZ, and KA on the AhR-ALOX5 pathway. Purified ytes underwent treatment with IS (1 mM), FICZ (100 nM), or KA (0.5 mM) for 1 day, followed by 5-day resting period to trained immunity. Activation of AhR through ligand binding was assessed by examining the induction of CYP1B1, an AhR ene, and cytokines one day post-treatment. The expression of genes related to the arachidonic acid pathway, such as ALOX5, 5AP, and LTB4R1, was analyzed via RT-qPCR six days after inducing trained immunity. Bar graphs show the mean ± SEM. * .05, **= p < 0.01, and ***= p < 0.001 by two-tailed paired t-test.

Indeed, it has been demonstrated that FICZ and TCDD, two high-affinity AhR ligands, exert opposite effects on T-cell differentiation, with TCDD inducing regulatory T cells and FICZ inducing Th17 cells. This dichotomy has been attributed to ligand-intrinsic differences in AhR activation (Ho PP et al. The aryl hydrocarbon receptor: a regulator of Th17 and Treg cell development in disease. Cell Res. 2008 Jun;18(6):605-8; Ehrlich AK et al. TCDD, FICZ, and Other High Affinity AhR Ligands Dose-Dependently Determine the Fate of CD4+ T Cell Differentiation. Toxicol Sci. 2018 Feb 1;161(2):310-320). These outcomes imply the involvement of an intricate interplay involving metabolic rewiring, epigenetic reprogramming, and the AhR-ALOX5 pathway in IS-induced trained immunity within monocytes.

(6) The authors need to clarify the role of IL-10 in IS-trained monocytes. IL-10, an anti-inflammatory cytokine that can be modulated by AhR, whose expression (Fig. 1E, Fig. 4D) may explain the inflammatory cytokine expression of IS-trained monocytes.

We appreciate the reviewer’s valuable comment, recognizing its significant importance. IL-10, characterized by potent anti-inflammatory attributes, assumes a pivotal role in constraining the host immune response against pathogens. This function serves to mitigate potential harm to the host and uphold normal tissue homeostasis. In the context of atherosclerosis (Mallat Z et al. Protective role of interleukin-10 in atherosclerosis. Circ Res. 1999 Oct 15;85(8):e17-24.) and kidney disease (Wei W et al. The role of IL-10 in kidney disease. Int Immunopharmacol. 2022 Jul;108:108917), IL-10 exerts potent deactivating effects on macrophages and T cells, influencing various cellular processes that could impact the development and stability of atherosclerotic plaques. Additionally, it is noteworthy that IL-10-deficient macrophages exhibit an augmentation in the proinflammatory cytokine TNF-α (Smallie T et al. IL-10 inhibits transcription elongation of the human TNF gene in primary macrophages. J Exp Med. 2010 Sep 27;207(10):2081-8; Couper KN et al. IL-10: the master regulator of immunity to infection. J Immunol. 2008 May 1;180(9):5771-7). As emphasized by the reviewer, the reduced gene expression of IL-10 by IS-trained monocytes may contribute to the heightened expression of proinflammatory cytokines. We have thoroughly addressed and discussed this specific point in response to the reviewer's comment (Line 394-399 of page 18 in the revised manuscript).

(7) The authors need to show H3K4me3 levels in TNF and IL6 genes in all conditions in one figure. (Fig. 2B). Comparing Fig. 2B and Fig. S2B, H3K4me3 does not appear to be increased at all by LPS in the IL6 region. 

We are grateful for the constructive criticism provided by the reviewer. In response to the reviewer's comment, we endeavored to conduct an experiment demonstrating H3K4me3 enrichment on the promoters of TNF-α and IL-6 across all experimental conditions. However, due to limitations in the availability of purified human monocytes, we conducted an additional three independent experiments for ChIP-qPCR across all conditions. Despite encountering a notable variability among individuals, even within the healthy donor cohort, our results demonstrated an increase in H3K4me3 enrichment on the TNF-α and IL-6 promoters in IS-trained groups, irrespective of subsequent LPS treatment (Author response image 8).

Author response image 8.

Analysis of H3K4me3 enrichment on the promoters of TNFA and IL6 Loci in IS-trained macrophages. ChIP-qPCR was employed to assess the enrichment of H3K4me3 on the promoters of TNFA and IL6 loci before (day 6) and after LPS stimulation (day 7) in IS-trained macrophages. The normalization control utilized 2% input. Bar graphs show the mean ± SEM. The data presented are derived from three independent experiments utilizing samples from different donors.

(8) The authors need to address the changes of H3K4me3 in the presence of MTA.

We appreciate the constructive criticism provided by the reviewer. In response to the reviewer's feedback, we conducted an analysis of the changes in H3K4me3 in the presence of MTA, a general methyltransferase inhibitor, using identical conditions as depicted in Figure 2C of the original manuscript. Our findings revealed that MTA exerted inhibitory effects on the levels of H3K4me3, as isolated through the acid histone extraction method, which were otherwise increased by IS-training, as illustrated in Author response image 9. 

Author response image 9.

The reduction of H3K4me3 by MTA treatment in IS-trained macrophages. IS-trained cells were restimulated by LPS (10 ng/ml) as a secondary challenge for 24 hrs, followed by isolation of histone and WB analysis for H3K4me3, Histone 3 (H3), and β-actin. The blot data from two independent experiments with different donors were shown.

(9) Interpretation of ChIP-seq results is not entirely convincing due to doubts about the quality of sequencing results. First, authors need to provide information on the quality of ChIP-seq data in reliable criteria such as Encode Pipeline. It should also provide representative tracks of H3K4me3 in the TNF and IL-6 genes (Fig. 2F). And in Fig. 2F, the author showed the H3K4me3 track of replicates, but the results between replicates were very different, so there are concerns about reproducibility. Finally, the authors need to show the correlation between ChIP-seq (Fig. 2) and RNA-seq (Fig. 5).

We appreciate the constructive criticism provided by the reviewer. 

As indicated by the reviewer, for evaluation of sample read quality, analysis was performed using the histone ChIP-seq standard from the ENCODE project, focusing on metrics such as read depth, PCR bottleneck coefficient (PBC)1, PBC2, and non-redundant fraction (NRF). Five of the total samples were displayed moderate bottleneck levels (0.5 ≤ PBC1 < 0.8, 1 ≤ PBC2 < 3) with acceptable (0.5 ≤ NRF < 0.8) complexity. One sample showed mild bottlenecks (0.8 ≤ PBC1 < 0.9, 3 ≤ PBC2 < 10) with compliance (0.8 ≤ NRF < 0.9) complexity. This quality metrics indicated ChIP-seq data quality meets at least the standards required for downstream analysis according to ENCODE project criteria (Author response image 10A).

To examine the differences in H3K4me3 enrichment patterns between two groups, we normalized the read counts around the TSS ±2 kb of human genes to CPM. Sequentially, we compared the average values of IS-treated macrophage compare to control and displayed in waterfall plots. In addition, we marked genes of interest in red including the phenotypes of IStrained macrophages (TNF and IL6), the activation of the innate immune responses (XRCC5, IFI16, PQBP1), and the regulation of ornithine decarboxylase (OAZ3, PSMA3, PSMA1) (Author response image 10B and C). Also, H3K4me3 peak tracks of TNF and IL6 loci and H3K4me3 enrichment pattern were added in supplementary Figure 3D and 3F in the revised manuscript.

Next, to evaluate the consistency among replicates within a group, we analyzed enrichment values, expressed as Counts per Million (CPM) using edgeR R-package, by applying Spearman's correlation coefficients. we analyzed two sets included total 7,136 H3K4me3 peak sets, as described in Figure 3E in the revised manuscript and 2 kbp around transcription start sites (TSS) from hg19 human genomes. The resulting Spearman's correlation coefficients and associated P-values demonstrated a concordance between replicates, confirming reproducibility and consistent performance (Author response image 10D). 

Finally, the correlation between gene expression and H3K4me3 enrichment around transcription start sites (TSS) has been reported in previous research (Reshetnikov VV et al. Data of correlation analysis between the density of H3K4me3 in promoters of genes and gene expression: Data from RNA-seq and ChIP-seq analyses of the murine prefrontal cortex. Data Brief. 2020 Oct 2;33:106365). To verify this association in our study, we applied Spearman's correlation for comparative analysis and conducted linear regression to determine if a consistent global trend in RNA expression existed. In our analysis, count values from regions extending 2 kbp around the TSSs in H3K4me3 ChIP-seq data were converted to Counts per Million (CPM) using edgeR R-package. These were then contrasted with the Transcripts Per Million (TPM) values of genes. Our results revealed a significant positive correlation, reinforcing the consistent relationship between H3K4me3 enrichment and gene expression (Author response image 10E and Supplementary Fig. 6D in revised manuscripts).

Author response image 10.

The information on quality of ChIP-seq data and correlation between ChIP-seq and RNA-seq. A, information on quality of ChIP-seq data. B, H3K4me3 peak of promoter region on TNFA and IL6. C, The differences in H3K4me3 enrichment patterns between control group and IS-training group. D, The consistency among replicates within a group. E, Correlation between ChIP-seq and RNA-seq in IS-induced trained immunity.

(10) AhR changes in the cell nucleus should be provided (Fig. 4A).

We appreciate the constructive feedback from the reviewer. In response to the reviewer's suggestions, we investigated the nuclear translocation of AhR on 6 days after the induction of ISmediated trained immunity, as illustrated in Author response image 11. For this purpose, the lysate from IS-trained monocytes was fractionated into the nucleus and cytosol, and AhR protein was subsequently immunoblotted. The results depicted in Figure X demonstrate that IS-trained monocytes exhibited a higher level of AhR protein in the nucleus compared to non-trained monocytes. Notably, the nuclear translocation of AhR was significantly attenuated in IS-trained monocytes treated with GNF351. These findings imply that the activation of AhR, facilitated by the binding of IS, persisted partially up to 6 days, indicating that IS-mediated degradation of AhR was not fully recovered even on day 6 after the induction of IS training. Consequently, we have replaced Figure 4A in the revised manuscript.

Author response image 11.

The activation of AhR, facilitated by IS binding, is persisted partially up to 6 days during induction of trained immunity. The lysate of IS-trained cells treated with or without GNF351, were separated into nuclear and cytosol fraction, followed by WB analysis for AhR protein (Left panel). Band intensity in immunoblots was quantified by densitometry (Right panel). β-actin was used as a normalization control. Bar graphs show the mean ± SEM. * = p < 0.05, by two-tailed paired t-test.

(11) Do other protein-bound uremic toxins (PBUTs), such as PCS, HA, IAA, and KA, change the mRNA expression of ALOX5, ALOX5AP, and LTB4R1? In the absence of genetic studies, it is difficult to be certain of the ALOX5-related mechanism claimed by the authors.

We are grateful for the constructive criticism provided by the reviewer. In response to the reviewer's comment, we investigated whether uremic toxins, specifically PBUTs such as PCS, HA, IAA, and KA, induce changes in the mRNA expression of ALOX5, ALOX5AP, and LTB4R1 in trained monocytes. Intriguingly, the examination revealed no discernible induction in the mRNA expression of these genes by PBUTs, with the exception of IS, as depicted in Author response image 12 of the letter. These findings once again underscore the implication of the AhR-ALOX5 pathway in the induction of trained immunity in monocytes by IS.

Author response image 12.

No obvious impact of PBUTs except IS on the expression of arachidonic acid pathway-related genes on 6 days after treatment with PBUTs. Purified monocytes were treated with several PBUTs including IS, PCS, HA, IAA, and KA for 24 hrs., following by 5-day resting period to induce trained immunity. The mRNA expression of ALOX5, ALOX5AP, and LTB4R1 were quantified using RT-qPCR. Bar graphs show the mean ± SEM. * = p < 0.05, by two-tailed paired t-test.

(12) Fig.6 is based on the correlated expression of inflammatory genes or AA pathway genes. It does not clarify any mechanisms the authors claimed in the previous figures. 

We express our sincere appreciation for the constructive criticism provided by the reviewer, and we have taken careful note of the points raised. In response to the reviewer's feedback, we adopted two distinct approaches utilizing samples obtained from ESRD patients and IS-trained mice. Initially, we investigated the correlation between ALOX5 protein expression in monocytes and IS concentration in the plasma of ESRD patients presented in Figure 6E of the original manuscript. Despite the limited number of samples, our analysis revealed a nonsignificant correlation between IS concentration and ALOX5 expression; however, it demonstrated a positive trend (Author response image 13A). Subsequently, we examined the potential inhibitory effects of zileuton, an ALOX5 inhibitor, on the production of TNF-α and IL-6 in LPSstimulated splenic myeloid cells derived from IS-trained mice. Our findings indicate that zileuton significantly inhibits the production of TNF-α and IL-6 induced by LPS in splenic myeloid cells from IS-trained mice (Author response image 13B). These data were added in Figure 6N of the revised manuscript (Line 350-354 of page 16 in the revised manuscript).

Author response image 13.

Assessment of the correlation between ALOX5 and the concentration of IS in ESRD patients, and investigation of ALOX5 effects in mouse splenic myeloid cells in IS-trained mice. A. Examination of the correlation between ALOX5 protein expression in monocytes and IS concentration in the plasma of ESRD patients. B. C57BL/6 mice were administered daily injections of 200 mg/kg IS for 5 days, followed by a resting period of another 5 days. Subsequently, IS-trained mice were sacrificed, and spleens were mechanically dissociated. Isolated splenic myeloid cells were subjected to ex vivo treatment with LPS (10 ng/ml), along with zileuton (100 µM). The levels of TNF-α and IL-6 in the supernatants were quantified using ELISA. The graphs show the mean ± SEM. * = p < 0.05, by two-tailed paired t-test between zileuton treatment group and no-treatment group.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Minor corrections to the figures

(1) No indicators for the control group in Fig. 1B.

We thank you for the reviewer’s comment. According to the reviewer’s comment, the control group was indicated with (-).

(2) The same paper is listed twice in the references section. (No. 19 and 28)

We thank you for the reviewer’s comment. We deleted the reference No. 28.

Reviewer #2 (Public Review):

Manuscript entitled "Uremic toxin indoxyl sulfate (IS) induces trained immunity via the AhR-dependent arachidonic acid pathway in ESRD" presented some interesting findings. The manuscript strengths included use of H3K4me3-CHIP-Seq, AhR antagonist, IS treated cell RNA-Seq, ALOX5 inhibitor, MTA inhibitor to determine the roles of IS-AhR in trained immunity related to ESRD inflammation and trained immunity.

Thank you very much for your positive feedback.

Reviewer #2 (Recommendations For The Authors):

However, the manuscript needs to be improved by fixing the following concerns.

There are concerns:

(1) The experiments in Figs. 1G, 1H and 1I need to have AhR siRNA, and siRNA control to demonstrate that the results in uremic toxins-containing serum-treated experiments were related to IS;

We extend our gratitude to the reviewer for their invaluable comment, acknowledging its significant relevance to our study. In accordance with the reviewer's suggestion, we endeavored to conduct additional experiments utilizing AhR siRNA to elucidate the direct impact of IS present in the serum of end-stage renal disease (ESRD) patients on the induction of IS-mediated trained immunity. 

Regrettably, owing to limitations in the availability of monocytes post-siRNA transfection, we were unable to establish a direct relationship between the observed outcomes in experiments utilizing uremic toxins-containing serum and IS in AhR siRNA knockdown monocytes. However, treatment with GNF351, an AhR antagonist, resulted in the inhibition of TNF-α production in trained monocytes exposed to uremic toxins-containing serum (Author response image 14).

In our previous studies, we have already reported that uremic serum-induced TNF-α production in human monocytes is dependent on the AhR pathway, using GNF351 (Kim HY et al. Indoxyl sulfate (IS)-mediated immune dysfunction provokes endothelial damage in patients with end-stage renal disease (ESRD). Sci Rep. 2017 Jun 8;7(1):3057). Additionally, we have provided evidence demonstrating an augmentation in the activity of the AhR pathway within monocytes derived from ESRD patients, indicative of a significant reduction in AhR protein levels (Kim HY et al. Indoxyl sulfate-induced TNF-α is regulated by crosstalk between the aryl hydrocarbon receptor, NF-κB, and SOCS2 in human macrophages. FASEB J. 2019 Oct;33(10):10844-10858). It is noteworthy that other major protein-bound uremic toxins (PBUTs), such as PCS, HA, IAA, and KA, failed to induce trained immunity in human monocytes (Supplementary Figure 1A in the revised manuscript). Nevertheless, knockdown of AhR via siRNA effectively impeded the induction of IS-mediated trained immunity in human monocytes (Figure 4E in the revised manuscript). 

Taken collectively, our findings suggest a critical role for IS present in the serum of ESRD patients in the induction of trained immunity in human monocytes. 

Author response image 14.

Inhibition of uremic serum (US)-induced trained immunity by AhR antagonist, GNF351. Monocytes were pre-treated with or without GNF351 (AhR antagonist; 10 µM) for 1 hour, followed by treatment with pooled normal serum (NS) or uremic serum (US) at a concentration of 30% (v/v) for 24 hours. After a resting period of 5 days, cells were stimulated with LPS for 24 hours. The production of TNF-α and IL-6 in the supernatants was quantified using ELISA. The data presented are derived from three independent experiments utilizing samples from different donors.

(2) Fig. 3 needs to be moved as Fig. 2

We express appreciation for the constructive suggestion provided by the reviewer. In response to the reviewer's comment, the sequence of Figure 3 and Figure 2 was adjusted in the revised manuscript.

(3, 4) The connection between bioenergetic metabolism pathways and H3K4me3 was missing; The connection between bioenergetic metabolism pathways and ALOX5 was missing;

We appreciate the reviewer’s constructive criticism and fully understood the reviewer's points. In response to the reviewer's feedback, we conducted additional experiments employing appropriate inhibitors to elucidate the interrelation between bioenergetic metabolism and H3K4me3 and between bioenergetic metabolism and ALOX5. Initially, we assessed the enrichment of H3K4me3 at 6-day on promoters of TNFA and IL6 loci after treatment of 2-DG, a glycolysis inhibitor. Additionally, we evaluated the alteration in the activity of S6K, a downstream molecule of mTORC1, following treatment with zileuton, an inhibitor of ALOX5. Our findings indicate that AhR-dependent arachidonic acid (AA) signaling induces epigenetic modifications, albeit without inducing metabolic rewiring, in IS-induced trained immunity (Author response image 15). However, IS stimulation promotes mTORC1-mediated glycolysis in an AhR-independent manner. Notably, inhibition of glycolysis with 2-DG impacts epigenetic modifications. We have updated Figure 7 of the revised manuscript to incorporate these additional experimental findings, elucidating the correlation between the diverse mechanisms implicated in IS-induced innate immune memory (Fig. 7 in the revised manuscript).

Author response image 15.

Epigenetic modification is regulated by arachidonic acid (AA) pathway and metabolic rewiring, but metabolic rewiring is not affected by the AA pathway. A-B. Monocytes were pre-treated with zileuton (ZLT), an inhibitor of ALOX5, or 2DG, a glycolysis inhibitor, followed by stimulation with IS for 24 hours. After a resting period of 5 days, the enrichment of H3K4me3 on the promoters of TNFA and IL6 loci was assessed. Normalization was performed using 2% input. C. Monocytes were pre-treated with ziluton (ZLT) and stimulated with IS for 24 hr. Cell lysates were immunoblotted for phosphorylated S6 Kinase, with β-actin serving as a normalization control. Band intensities in the immunoblots were quantified using densitometry. D, A schematic representation of the mechanistic framework underlying IS-trained immunity. Bar graphs show the mean ± SEM. * = p < 0.05, **= p < 0.01, and *** = p < 0.001 by two-tailed paired t-test.

(5) It was unclear whether histone acetylations such as H3K27acetylation and H3K14 acetylation are involved in IS-induced epigenetic reprogramming or IS-induced trained immunity is highly histone methylation-specific.

We appreciate the constructive comment provided by the reviewer. As highlighted by the reviewer, alterations in epigenetic histone markers, specifically H3K4me3 or H3K27ac, have been recognized as the underlying molecular mechanism in trained immunity. Due to limitations in the availability of trained cells, this study primarily focused on histone methylation. In response to the reviewer's inquiry, we briefly investigated the impact of histone acetylation using C646, a histone acetyltransferase inhibitor, on IS-induced trained immunity (Author response image 16). Our experiments revealed that C646 treatment effectively hinders the production of TNF-α and IL-6 by IS-trained monocytes in response to LPS stimulation, comparable to the effects observed with MTA (5’methylthioadenosine), a non-selective methyltransferase inhibitor. This suggests that histone acetylation also contributes to the epigenetic modifications associated with IS-induced trained immunity. We sincerely appreciate the valuable input from the reviewer.

Author response image 16.

The role of histone acetylation in epigenetic modifications in IS-induced trained immunity. Monocytes were pretreated with MTA (methylthioadenosine, methyltransferase inhibitor) or C646 (histone acetyltransferase p300 inhibitor), followed treatment with IS 1 mM for 24 hrs. After resting for 5 days, trained cells were re-stimulated by LPS 10 ng/ml as secondary insult. TNF-α and IL-6 in supernatants were quantified by ELISA. Bar graphs show the mean ± SEM. * = p < 0.05 and **= p < 0.01 by two-tailed paired t-test.

Reviewer #3 (Public Review):

The manuscript entitled, "Uremic toxin indoxyl sulfate induces trained immunity via the AhRdependent arachidonic acid pathway in ESRD" demonstrates that indoxyl sulfate (IS) induces trained immunity in monocytes via epigenetic and metabolic reprogramming, resulting in augmented cytokine production. The authors conducted well-designed experiments to show that the aryl hydrocarbon receptor (AhR) contributes to IS-trained immunity by enhancing the expression of arachidonic acid (AA) metabolism-related genes such as arachidonate 5-lipoxygenase (ALOX5) and ALOX5 activating protein (ALOX5AP). Overall, this is a very interesting study that highlights that IS mediated trained immunity may have deleterious outcomes in augmented immune responses to the secondary insult in ESRD. Key findings would help to understand accelerated inflammation in CKD or RSRD.

We greatly appreciate your positive feedback.

Reviewer #3 (Recommendations for The Authors):

This reviewer, however, has the following concerns.

Major comments:

(1) Figure 1B: IS is known to induce the expression of TNF-a and IL-6. This reviewer wonders why these molecules were not detected in the IS (+) LPS (-) condition.

We appreciate the constructive comment provided by the reviewer. In our prior investigation, it was observed that the expression of TNF-α and IL-6 was induced 24 hours after IS treatment in human monocytes and macrophages (Couper KN et al. IL-10: the master regulator of immunity to infection. J Immunol. 2008 May 1;180(9):5771-7). In adherence to the trained immunity protocol, the medium was replaced at the 24 hours post-IS treatment to eliminate IS, with a subsequent change after a 5-day resting period. Probably, TNF-α and IL-6 are accumulated and detected in the IS (+) LPS (-) culture supernatant if the media was not changed at these specific time points. Our primary objective, however, was to ascertain the role of IS in the induction of trained immunity, prompting an investigation into whether IS contributes to an increase in the production of TNF-α and IL-6 in response to LPS stimulation as a secondary insult. 

(2) 1' stimulus is IS followed by 2' stimulus LPS/Pam3. It would be interesting to know what the immune profile is when other uremic toxin is used for secondary insult, this would be more relevant in clinical context of ESRD.

The reviewer's insightful comment is greatly appreciated. To address their feedback, IStrained macrophages were subjected to additional stimulation using protein-bound uremic toxins (PBUTs) as a secondary challenge. As illustrated in Letter figure 17, the examined uremic toxins, namely p-cresyl sulfate (PCS), Hippuric acid (HA), Indole 3-acetic acid (IAA), and kynurenic acid (KA), failed to elicit the production of proinflammatory cytokines, specifically TNF-α and IL-6, by IS-trained monocytes.

Author response image 17.

No obvious effect of protein-bound uremic toxin (PBUTs) as secondary insults on the production of proinflammatory cytokines in IS-trained monocytes. IS-trained monocytes were re-stimulated with several PBUTs, such as IS (1 mM), PCS (1 mM), HA (2 mM), IAA. (0.5 mM), and KA (0.5 mM) as a secondary challenge for 24 hrs. TNF-α and IL-6 in supernatants were quantified by ELISA. The data from two independent experiments with different donors were shown. ND indicates ‘not detected’.

(3) The authors need to explain a rationale why RNA and protein data used different markers.

We appreciate the constructive input provided by the reviewer. Given that TNF-α and IL6 represent prototypical cytokines synthesized by trained monocytes in humans, we conducted a comprehensive analysis of their mRNA and protein levels. In human macrophages, the release of active IL-1β necessitates a second priming event, such as the presence of ATP. Consequently, we posited that assessing the mRNA levels of IL-1β would suffice to demonstrate the induction of trained immunity in our experimental protocol. Nevertheless, in response to the reviewer's comment, we proceeded to assess the protein levels of IL-1β, IL-10, and MCP-1 as illustrated in Author response image 189. These data have been incorporated into the revised manuscript as supplementary Figure 1E. 

Author response image 18.

Modulation of cytokine levels in IS-trained macrophages in response to secondary stimulation with LPS. Human monocytes were stimulated with the IS for 24 hr, followed by resting period for 5 days. On day 6, the cells were re-stimulated with LPS for 24 hr. The levels of each cytokine in the supernatants were quantified using ELISA. Bar graphs show the mean ± SEM. ** = p < 0.01 and ***= p < 0.001 by two-tailed paired t-test.

(4) Epigenetic modification primarily involves histone modification and DNA methylation. The authors presented convincing data on histone modification (Figure 2), but did not provide any insights in the promoter DNA methylation status.

We express our gratitude to the reviewer for providing valuable comments, which highlight a crucial aspect of our study. Despite the well-established primary role of DNA methylation in epigenetic modifications, recent suggestions propose that histone modifications, particularly H3K4me3 or H3K27ac, play a predominant role in the induction of trained immunity. In this context, our primary inquiry was focused on determining whether IS, as an endogenous insult, induces trained immunity in monocytes, and if so, whether IS-trained immunity is mediated through metabolic and epigenetic modifications - recognized as the major mechanisms underlying the generation of trained immunity. It is imperative to note that our study's primary objective did not encompass the identification of various epigenetic changes. In response to the reviewer's inquiry, we conducted a brief examination of the impact of DNA methylation using ZdCyd (5-aza-2’-deoxycytidine), a DNA methylation inhibitor, on IS-induced trained immunity. Our experimental findings indicate that ZdCyd treatment exerts no discernible effect on the production of TNF-α and IL-6 by IS-trained monocytes upon stimulation with LPS, as illustrated in Author response image 19. However, a recent study has shed light on the role of DNA methylation in BCG vaccine-induced trained immunity in human monocytes (Bannister S et al. Neonatal BCG vaccination is associated with a long-term DNA methylation signature in circulating monocytes. Sci Adv. 2022 Aug 5;8(31):eabn4002). Consequently, further investigations utilizing DNA methylation sequencing are warranted to elucidate whether DNA methylation is implicated in the induction of IS-trained immunity.

Author response image 19.

The effect of DNA methylation on IS-induced trained immunity. Monocytes were pretreated with ZdCyd (5-aza-2’-deoxycytidine, DNA methylation inhibitor), followed by treatment with IS 1 mM for 24 hrs. After resting for 5 days, cells were re-stimulated by LPS 10 ng/ml as secondary insult. TNF-α and IL-6 in supernatants were quantified by

ELISA. Bar graphs show the mean ± SEM. * = p < 0.05 and **= p < 0.01 by two-tailed paired t-test.

               

(5) Metabolic rewiring in trained immunity cells undergo metabolic changes which involved intertwined pathways of glucose and cholesterol metabolism. The authors presented nice data on glucose pathway (Figure 3) but failed to show any changes related to cholesterol metabolism.

We express our gratitude to the reviewer for providing valuable comments, which underscore a noteworthy observation. In the current investigation, our primary emphasis has been on glycolytic reprogramming, recognized as a principal mechanism for inducing trained immunity in monocytes. This focus stems from preliminary experiments wherein Fluvastatin, a cholesterol synthesis inhibitor, demonstrated no discernible impact on TNF-α production by IS-trained monocytes, as illustrated in Author response image 20. Intriguingly, Fluvastatin treatment exhibited a partial inhibitory effect on the production of IL-6 by IS-trained monocytes. Subsequent investigations are imperative to elucidate the role of cholesterol metabolism in the induction of IS-trained immunity.

Author response image 20.

The effect of cholesterol metabolism on IS-induced trained immunity. Monocytes were pretreated with Fluvastatin (cholesterol synthesis inhibitor, HMG-CoA reductase inhibitor), followed treatment with IS 1 mM for 24 hrs. After resting for 5 days, cells were re-stimulated by LPS 10 ng/ml as secondary insult. TNF-α and IL-6 in supernatants were quantified by ELISA. Bar graphs show the mean ± SEM. * = p < 0.05 and **= p < 0.01 by two-tailed paired t-test.

(6) Trained immunity involves neutrophils in addition to monocyte/macrophages. It is evident from the RNAseq data that neutrophil degranulation (Figure 5B) is the top enriched pathway. This reviewer wonders why the authors did not perform any assays on neutrophils.

We appreciate the reviewer for valuable comment. IS represents a major uremic toxin that accumulates in the serum of patients with chronic kidney disease (CKD), correlating with CKD progression and the onset of CKD-related complications, including cardiovascular diseases (CVD). Our prior investigations have demonstrated that IS promotes the production of TNF-α and IL-1β by human monocytes and macrophages. Additionally, macrophages pre-treated with IS exhibit a significant augmentation in TNF-α production when exposed to a low dose of lipopolysaccharide (LPS). Considering the pivotal role of proinflammatory macrophages and TNF-α, a principal cardiotoxic cytokine, in CVD pathogenesis, our focus in this study has primarily focused on elucidating the trained immunity of monocytes/macrophages. Consequently, all experiments were meticulously conducted using highly purified monocytes and monocytederived macrophages derived from both healthy controls and end-stage renal disease (ESRD) patients. The reviewer's observation regarding the potential involvement of neutrophils in trained immunity has been duly noted. Subsequent investigations will be imperative to explore the conceivable role of IS-trained neutrophils in the pathogenesis of CVD. Once again, we appreciate the reviewer for their valuable comment.

(7) Figure 5C (GSEA plots): This reviewer is not sure if one can present the plots assigned with groups (eg. IS(T) vs Control). More details are required in the Methods related to this.

We apologize for any ambiguity resulting from the previously unclear description of methods concerning Gene Set Enrichment Analysis (GSEA) plots. To provide clarification, additional details pertaining to this aspect have been explained upon in the revised manuscript's Methods section. 

(8) In vivo data (Figure 6 I-M): Instead of serum profile and whole set of spleen myeloid cells, it would be interesting to see changes of markers on peritoneal macrophages or bone marrow-derived macrophages since the in vitro findings are on monocyte-derived macrophages.

We appreciate comment and the insightful suggestion provided by the reviewer. In response to the reviewer's feedback, we conducted additional in vivo experiments to examine the production of TNF-α and IL-6 in bone marrow-derived macrophages (BMDMs) derived from IStrained mice. Upon LPS stimulation, we observed an increase in the production of TNF-α and IL-6 in spleen myeloid cells from IS-trained mice. However, no such increase in these cytokines was noted in BMDMs derived from the same mice (Author response image 22, A and B). In fact, we already observed that that the expression of ALOX5 was not elevated in BM cells derived from IS-trained mice presented in Figure 6L and M of the original manuscript (Author response image 22C). 

Recent studies have indicated that trained immunity can be induced in circulating immune cells, such as monocytes or resident macrophages (peripheral trained immunity), as well as in hematopoietic stem and progenitor cells (HSPCs) within the bone marrow (central trained immunity) (Kaufmann E et al. BCG Educates Hematopoietic Stem Cells to Generate Protective Innate Immunity against Tuberculosis. Cell. 2018 Jan 11;172(1-2):176-190.e19; Riksen NP et al. Trained immunity in atherosclerotic cardiovascular disease. Nat Rev Cardiol. 2023 Dec;20(12):799-811). It is plausible that central trained immunity in BM progenitor cells may not be elicited in our mouse model, which is relatively acute in nature. Further investigations are warranted to explore the role of IS in inducing central trained immunity, utilizing appropriate chronic disease models.

We have included this additional data as supplementary figures in the revised manuscript (Suppl. Fig. 7, D and E, and line 355-362 of page 16 in the revised manuscript).

Author response image 21.

Absence of trained immunity in bone marrow derived macrophages (BMDMs) derived from IStrained mice. A-B, IS was intraperitoneally injected daily for 5 days, followed by training for another 5 days. Isolated BM progenitor cells and spleen myeloid cells were differentiated or treated with LPS for 24 hr. The supernatants were collected for ELISA. C, The level of ALOX5 protein in BM cells isolated from IS-trained or control mice was analyzed by western blot. The graph illustrates the band intensity quantified by densitometry. Bar graphs show the mean ± SEM. * = p < 0.05 and **= p < 0.01, by unpaired t-test.

(9) Figure 7: There are no data on signaling pathway(s) that links IS and epigenetic changes, the authors therefore may want to add "?" to the proposed mechanism.

We extend our sincere appreciation to the reviewer for providing valuable feedback. In light of the constructive comments provided by three reviewers, we have undertaken a series of additional experiments. These efforts have enabled us to propose a more elucidating schematic representation of the proposed mechanism, free of any ambiguous elements (Figure 7 in the revised manuscript). We are grateful for your insightful input.

(10) Demographic data (Table S2): ESRD patients have co-morbidities including diabetes (33% of subjects), CAD (28%). How did the authors factor out the co-morbidities in the overall context of their findings?

We express gratitude to the reviewer for providing valuable comments, particularly on a noteworthy and significant aspect. The investigation employed an End-Stage Renal Disease (ESRD) Cohort involving approximately 60 subjects undergoing maintenance hemodialysis at Severance Hospital in Seoul, Korea. The subset of participants subjected to analysis consisted of stable individuals who provided informed consent and had not undergone hospitalization for reasons related to infection or acute events within the preceding three months.

(11) There are no data on the purity of IS.

According to the reviewer's suggestion, we have included information regarding the purity (99%) of IS in the Methods section.

(12) Figure 6L: Immunoblot on b-actin were merged. This reviewer wonders how the authors analyzed these blots. 

We express gratitude for the constructive criticism provided by the reviewer, and we acknowledge and comprehend the concerns raised. In response to the reviewer's comments, a reanalysis of the ALOX5 expression level in Figure 6M was conducted, employing immunoblot analysis on β-actin, as depicted in Figure 6L, with a short exposure time (Author response image 22).

Author response image 22.

ALOX5 protein exhibited an elevation in splenic myeloid cells obtained from IS-trained mice.

(13) qPCR data throughout the manuscript have control group with no error bar. The authors may not set all controls arbitrarily equal to 1 (Example Figure 1H and I). Data should be normalized in a test standard way. The average of a single datapoint may be scaled to 1, but variation must remain within the control groups.

We express gratitude to the reviewer for their valuable feedback, acknowledging a comprehensive understanding of their perspectives. Our qPCR assays predominantly investigated the impact of various treatments on the expression of specific target genes (e.g., TNF-α, IL-6, Alox5) within monocytes/macrophages obtained from the same donors.

Subsequently, normalization of gene expression levels occurred relative to ACTINB expression, followed by relative fold-increase determination using the comparative CT method (ΔΔCT).

Statistical significance was assessed through a two-tailed paired analysis in these instances. Additionally, a substantial portion of the qPCR data was validated at the protein level through ELISA and immunoblotting techniques.

Minor Comments:

(1) Molecular weight markers are missing in immunoblots throughout the manuscript.

According to the reviewer's comment, molecular weight markers are added into immunoblots

(2)  ESRD should be spelled out in the title.

According to the reviewer's comment, we spelled out ESRD in the title.

eLife assessment

This important study expands generally upon our understanding of the role of hnRNP proteins in lncRNA function through analysis of ASAR genes that are present on all chromosomes and of profound significance. The findings provide convincing evidence linking ASARs with the phenomenon of RNA retention on chromosomes, including X inactivation, thereby providing an expanded context for studies in these areas. This manuscript will be of interest to researchers studying gene regulation and the interactions and functional roles of hnRNP and lncRNAs.

Reviewer #1 (Public Review):

Summary:

Thayer et al build upon their prior findings that ASAR long noncoding RNAs (lncRNAs) are chromatin-associated and are implicated in control of replication timing. To explore the mechanism of function of ASAR transcripts, they leveraged the ENCODE RNA binding protein eCLIP datasets to show that a 7kb region of ASAR6-141 is bound by multiple hnRNP proteins. Deletion of this 7kb region resulted in delayed chromosome 6 replication. Furthermore, ectopic integration of the ASAR6-141 7kb region into autosomes or the inactive X-chromosome also resulted in delayed chromosome replication. They then use RNA FISH experiments to show that knockdown of these hnRNP proteins disrupts ASAR6-141 localization to chromatin and in turn replication timing.

Strengths:

Given prior publications showing HNRNPU to be important for chromatin retention of XIST and Firre, this work expands upon our understanding on the role of hnRNP proteins in lncRNA function.

Weaknesses:

The work presented is mechanistically interesting, however, one must be careful with the over interpretation that hnRNP proteins can regular chromosome replication directly.

Reviewer #2 (Public Review):

Summary:

This paper reports a role for a substantial number of RNA binding proteins (RBPs), in particular hnRNPs, in the function of ASAR "genes". ASARs are (very) long, non-coding RNAs (lncRNAs) that control allelic expression imbalance (e.g.: mono-allelic expression) and replication timing of their resident chromosomes. These relatively novel "genes" have recently been identified on all human autosomes and are of broad significance given their critical importance for basic chromosomal functions and stability. However, the mechanism(s) of ASAR function remain unclear. ASARs exhibit some functional relatedness to Xist RNA, including persistent association of the expressed RNA with its resident chromosome, and similarities in the composition of RNA sequences associated with ASARs, in particular Line1 RNAs. Recent findings that certain hnRNPs control the chromosome territory retention of Cot1-bearing RNAs (which includes Line1) led the authors to test hypothesis that hnRNPs might regulate ASARs.

Specific new findings in this paper:

-Analysis of eCLIP (RNA-protein interaction) ENCODE data shows numerous interactions of the ASAR6-141 RNA with RBPs, including hnRNPs (e.g.: HNRNPU) that have been implicated in the retention of RNAs within local chromosome territories.<br /> -most of these interactions can be mapped to a 7kb region of the 185kb ASAR6-141 RNA<br /> -deletion of this 7kb region is sufficient to induce the DMC/DRT phenotype associated with deletion of the entire ASAR region<br /> -ectopic integration into mouse autosomes of the 7kb region is sufficient to cause DMC/DRT of the targeted autosome, and a similar effect upon ectopic integration into inactive X. This raises the question about integration into the active X, which was not mentioned. Is integration into the active X observed? Is it possible that integration might alter Xist expression confounding this interpretation?<br /> -Knockdown of RBPs that bind the 7kb region causes dissociation of ASAR6-141 RNA from its chromosome territory, and, remarkably, dissociation of Xist RNA from inactive X, and mis-colocalization of the ASAR6-141 and Xist RNAs. Depletion of these RBPs causes DMC/DRT on all autosomes.

Strengths:

These are compelling results suggesting shared mechanism(s) in the regulation of ASARs and Xist RNAs by RBPs that bind Cot1 sequences in these lncRNAs. The identification of these RBPs as shared effectors of ASARs and Xist that are required for RNA territory localization mechanistically links previously independent phenomena.

The data are convincing and support the conclusions. The replication timing method is low resolution and is only a relative measure but seems adequate for the task at hand. The FISH experiments are convincing. The quality of the images is impressive.

Links to other subfields like X-inactivation and RNA association with chromosome territories provide novel context and protein players, new phenotypes to examine

Weaknesses:

The exact effects of knockdown experiments are unclear and may be indirect, which is acknowledged.

The mechanism is not much clearer than before.

Author response:

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

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Major recommendations

(1) In lines 42-44 (abstract), the authors state that "ASARs function as essential RNA scaffolds for the assembly of hnRNP complexes that help maintain the structural integrity of each mammalian chromosome". Similar conclusions are restated in lines 138-140. Based on the data presented, it is evident that ASARs localization on chromatin is dependent on hnRNPs. However, there is insufficient evidence to conclude that ASARs cause the assembly of hnRNP complexes or that these hnRNP complexes are directly responsible for the regulation of chromosome replication. Please revise your claims.

We have modified the text as follows: “Our results further demonstrate the role that ASARs play during the temporal order of genome-wide replication, and we propose that ASARs function as essential RNA scaffolds for the assembly of hnRNP complexes that help maintain the structural integrity of each mammalian chromosome.”

(2) In the analysis in Figure 1C- F, it is unclear why XIST is used as a comparison to ASAR6-141. A more meaningful control would be to show that hnRNPs preferentially bind ASAR6-141 relative to all expressed transcripts. Also, some panels are missing the y-axis label.

We have genetically validated 8 different ASAR genes for their role in controlling chromosome-wide replication timing. The only other gene known to control chromosome-wide replication timing is XIST, which also encodes a chromosome-associated lncRNA. Our analysis of publicly available eCLIP data (and previous literature on XIST-binding proteins) showed substantial overlap between RBPs that associate with ASARs and XIST. Hence, we anticipated that at least some RBP knockdowns would affect both lncRNAs, despite their contrasting functions. In addition, we routinely use XIST RNA as a positive control in RNA FISH assays, as the XIST RNA FISH protocol represents a robust and well validated chromosomal RNA FISH procedure.

y-axis labels have been added to Figure 1.

(3) In Figure 2K&L, it would be beneficial to quantify and normalize the BrdU incorporation, as ectopic integration of the sense 7kb region appears to result in overall higher BrdU incorporation in all chromosomes, not just chromosome 5.

There are two main aspects of the BrdU incorporation assay that we use: 1) The BrdU incorporation banding pattern on each chromosome is unique to that chromosome, and the banding pattern is also representative of the time during S phase when the BrdU incorporation occurred, i.e. we detect a different banding pattern if BrdU is incorporated in early S phase versus late S phase. 2) The amount of BrdU incorporation can be used to measure the synchrony between chromosome homologs, but only within the same cell. Thus, we generate a ratio of BrdU incorporation in chromosome homologs in individual cells, then compare the ratio of incorporation into each chromosome pair in multiple cells (see Figure 2B-E). The overall BrdU incorporation into the chromosomes of different cells is quite variable; however, the banding pattern and ratio of BrdU incorporation in chromosome homologs in individual cells is comparable, unless we have disrupted or ectopically integrated an ASAR. Given the variability in overall BrdU incorporation detected between different cells in the population this is not a useful readout for measuring synchronous versus asynchronous replication between chromosome homologs.

(4) hnRNP protein can regulate multiple aspects of RNA processing other than chromatin retention. Hence, it would be beneficial to rule out an alternative hypothesis as to what the hnRNP knockdowns do to ASAR6-131? For example, assessing changes in RNA levels or splicing upon knockdown of hnRNPs using qPCR?

We agree that direct roles for any of the hnRNP/RBPs that are critical for ASAR RNA localization and replication timing have not been established. However, our findings combined with the observation that cells depleted of HNRNPU show reduced origin licensing in G1, and show reduced origin activation frequency during S phase (PMID: 34888666), supports a role for HNRNPU, either directly or indirectly, in DNA replication. Furthermore, we also found that depletion of the DNA replication fork remodeler HLTF or the deubiquitinase UCHL5 also results in mis-localization of ASAR RNAs, and results in asynchronous replication of every autosome pair, indicating that ASAR RNA mis-localization and asynchronous replication are not simply a phenotype associated with hnRNP depletions. A full mechanistic understanding of the role that ASAR RNAs play in combination with this relatively large and diverse set of hnRNP/RBPs will require a better understanding of the direct roles that each protein, and any higher order complexes that contain these proteins, play in regulating DNA synthesis, splicing, transcription, chromatin structure and/or ASAR RNA localization.

(5) Both the disruption and ectopic expression of the 7kb region result in delayed chromosome replication. Would one not expect there to be opposing effects on replication timing? Please discuss.

One puzzling set of observations is that loss of function mutations and gain of function mutations of ASAR genes result in a similar delayed replication timing and delayed mitotic condensation phenotype. We have detected delayed replication timing in human cells following genetic knockouts (loss of function) of eight different ASAR genes located on 5 different autosomes. We have also detected delayed replication timing on mouse chromosomes expressing transgenes (gain of function) from three different ASAR genes (ASAR6, ASAR6-141, and ASAR15). The ASAR transgenes ranged in size from an ~180kb BAC, to an ~3kb PCR product. One possible explanation for these observations is that ectopic integration of ASAR transgenes function in a dominant negative manner by interfering with the endogenous “ASARs” on the integrated chromosomes. Consistent with this possibility is that we recently identified ASAR candidate genes on every human autosome (PMC9588035). Our favored model is that expression of ASAR transgenes integrated into mouse chromosomes disrupts the function of endogenous ASARs by "out-competing" them for shared RBPs. We also point out that a similar ectopic integration assay, using Xist transgenes, has been an informative assay for characterization of Xist functions, including the ability to delay replication timing and induce gene silencing on autosomes (reviewed in PMID:19898525). One intriguing observation (yet largely ignored by the X inactivation field) is that deletion of the Xist gene on either the active or inactive X chromosomes in somatic cells results in delayed replication timing of the X chromosomes (PMC1667074; PMC1456779). Thus, both loss of function and gain of function mutations of Xist result in a similar delayed replication timing phenotype. Given these parallels between Xist and ASAR gene mutation phenotypes we were curious to test the consequences of ASAR gain of function on the inactive X chromosome. In this manuscript, we integrated the ~7kb ASAR6-141 transgene into the inactive X chromosome, and detected a delayed replication timing phenotype on the integrated X chromosome. We also detected an association between Xist and ASAR RNAs using RNA FISH in interphase cells (Figure 4A and 4B), which supports the observations that ASAR RNAs and XIST RNA are bound by a partially overlapping set of hnRNP/RBPs (Figure 1D-F), and is consistent with the model that ASAR transgenes disrupt function by competition for shared RBPs. Dissecting the roles that the hnRNP/RBPs that interact with both ASAR and XIST RNAs will undoubtably give important insights into both XIST and ASAR function, and how these poorly understood chromosomal phenotypes are generated.

Minor recommendations

(1) In Figure 1G, it would be informative to show where the LINE-1 element within ASAR6-141 is located to get a sense of what hnRNP proteins bind to it.

There are numerous LINE-1 elements within the ASAR6-141 gene. The ~7kb RBPD does not contain LINE-1 sequences. Therefore, we did not detect significant hnRNP/RBP eCLIP peaks within LINE-1 sequences.

(2) The rationale for ectopic integration of the 7kb region into the inactive X-chromosome is unclear. Is there something unique about the replication of the inactive X or were you interested in seeing whether the 7kb region could escape X-inactivation?

Given the parallels between Xist and ASAR gene mutation phenotypes, i.e. loss of function and gain of function result in delayed replication timing (see above), we were curious to test the consequences of ASAR gene gain of function on the inactive X chromosome. One possibility was reversal of X inactivation and a shift to earlier replication timing. However, we detected delayed replication timing on the inactive X, and an enhanced XIST RNA FISH signal that overlapped with the ASAR RNA. This speaks to the comment of Reviewer 2 questioning: "Is it possible that integration might alter Xist expression confounding this interpretation? ". The enhanced XIST RNA FISH signal suggests that the delayed replication of the inactive X is not due to reduced expression of XIST RNA.

Joint Public Review:

Xie et al. propose that the asymmetric segregation of the NuRD complex is regulated in a V-ATPase-dependent manner, and plays a crucial role in determining the differential expression of the apoptosis activator egl-1 and thus critical for the life/death fate decision.

Remaining concerns are the following:

The authors should provide the point-by-point response to the following issues. In particular, authors should provide clear reasoning as to why they did not address some of the following comments in the previous revisions. The next response should be directly answering to the following concerns.

(1) Discussion should be added regarding the criticism that NuRD asymmetric segregation is simply a result of daughter cell size asymmetry. It is perfectly fine that the NuRD asymmetry is due to the daughter cell size difference (still the nucleus within the bigger daughter would have more NuRD, which can determine the fate of daughter cells). Once the authors add this clarification, some criticisms about 'control' may become irrelevant.

(2) ZEN-4 is a kinesin that predominantly associates with the midzone microtubules and a midbody during mitosis. Given that midbodies can be asymmetrically inherited during cell division, ZEN-4 is not a good control for monitoring the inheritance of cytoplasmic proteins during asymmetric cell division. Other control proteins, such as a transcriptional factor that predominantly localizes in the cytoplasm during mitosis and enters into nucleus during interphase, are needed to clarify the concern.

As for pHluorin experiments, symmetric inheritance of GFP and mCherry is not an appropriate evidence to estimate the level of pHluorin during asymmmetric Q cell division. This issue remains unsolved.

(3) Q-Q plot (quantile-quantile plot) in Figure S10 can be used for visually checking normality of the data, but it does not guarantee that the distribution of each sample is normal and has the standard deviation compared with the other samples. I recommend the authors to show the actual statistical comparison P-values for each case. The authors also need to show the number of replicate experiments for each figure panel.

The authors left inappropriate graphs in the revised manuscript. In Figure 3E, some error bars are disconnected and the other are stuck in the bars. In Figure S4C, LIN-53 in QR.a/p graph shows lines disconnected from error bars.

I am bit confused with the error bars in Figure 2B. Each dot represents a fluorescent intensity ratio of either HDA-1 or LIN-53 between the two daughter cells in a single animal. Plots are shown with mean and SEM, but several samples (for example, the left end) exhibit the SEM error bar very close to a range of min and max. I might misunderstand this graph but am concerned that Figure 2B may contain some errors in representing these data sets. I would like to ask the authors to provide all values in a table format so that the reviewers could verify the statistical tests and graph representation.

(4) The authors still do not provide evidence that the increase in sAnxV::GFP and Pegl-1gfp or the increase in H3K27ac at the egl-1 gene in hda-1(RNAi) and lin-53(RNAi) animals is not a consequence of global effects on development. Indeed, the images provided in Figure S7B demonstrate that there are global effects in these animals. no causal interactions have been demonstrated.

(5) Figure 4: Due to the lack of appropriate controls for the co-IP experiment (Fig. 4), I remain unconvinced of the claim that the NuRD complex and V-ATPase specifically interact. Concerning the co-IP, the authors now mention that the co-IP was performed three times: "Assay was performed using three biological replicates. Three independent biological replicates of the experiment were conducted with similar results." However, the authors did not use ACT-4::GFP or GFP alone as controls for their co-IP as previously suggested. This is critical considering that the evidence for a specific HDA-1::GFP - V-ATPase interaction is rather weak (compare interactions between HDA-1::GFP and V-ATPase subunits in Fig 4B with those of HDA-1::GFP and subunits of NuRD in Fig S8B).

(6) Based on Fig 5E, it appears that Bafilomycin treatment causes pleiotropic effects on animals (see differences in HDA-1::GFP signal in the three rows). The authors now state: "Although BafA1-mediated disruption of lysosomal pH homeostasis is recognized to elicit a wide array of intracellular abnormalities, we found no evidence of such pleiotropic effects at the organismal level with the dosage and duration of treatment employed in this study". However, the 'evidence' mentioned is not shown. It is critical that the authors provide this evidence.

eLife assessment

The author use an approach that is in principle useful, comparative meta-analysis, to contribute to our understanding of life history evolution. The advance remains limited, as both the meta-analysis and the theoretical model are incomplete, and proper statistical and mechanistic descriptions of the simulations are lacking. A major concern is that the interpretation does not properly take into account the effect of well-characterised complexities in the relationship between clutch size and fitness in birds.

Reviewer #2 (Public Review):

I have read the re-submission of the manuscript "The optimal clutch size revisited: separating individual quality from the parental survival costs of reproduction" by LA Winder and colleagues.

I have to say that I am quite disappointed not to see any formalisation of the mechanism that the authors have in mind to explain the results they have and to draw general conclusions from it. In my original review, I strongly recommended "improving the theoretical component of the analysis by providing a solid theoretical framework before, from it, drawing conclusions. This, at a minimum, requires [...] most importantly a mechanistic model describing the assumed relationships."

Without it, it is impossible to follow, agree or disagree with the authors and learn something from the meta-analysis other than: the clutch size-annual survival relationship has opposite slopes for manipulated and natural populations. Such a set of equations (would replace pages of verbose and) is not only necessary for the readers to be able to understand the authors' points and to clearly understand the simplifying assumptions, but also for the authors to ensure they conclusions are sound. For these reasons this is a central part of such studies, see, e.g. (Walker et al., 2008). This is supposedly replaced here by a figure (figure 5), which top-left part reads: "Parental survival costs of reproduction constrain intra-specific reproduction" - "no the effect size on fig 4 is too small". Figure 4 is the output of simulations where the authors have incorporated the mean effect on survival rate per egg from the manipulated populations into a model where they compute R0 for various increases in the annual fertility rate, and related decreases in annual survival rates, showing that along the slow-fast gradient, for balanced survival-reproduction (certainly not far from R0=1), R0 is not affected (or very little) by change in fertility-survival along the trade-off. Nowhere on this figure, do we have any information inferring that survival costs of reproduction do not constrain intra-specific reproduction. It is actually possible to build a simple mechanistic model with a trade-off mechanism that strongly affects the LRS and its variance between individuals and to would produce the exact same figure.

This is compounded in this manuscript by the constant verbose, imprecisions, outright mistakes, with a general confusion between magnitudes and variation of magnitudes, which makes it very hard to read. Let us just look at two examples illustrating my points. In the abstract, I read: " ... revealed that reproduction presented negligible costs, except when reproductive effort was forced beyond the level observed within species, to that seen between species" means nothing: what is the level of reproductive effort seen between species? I suppose the authors mean "forced beyond the maximum level observed within species, to that seen between species" or something like that. Caption figure 4:" Selection differentials (i.e., the difference in lifetime reproductive output between hypothetical control and brood-manipulated populations)" It cannot be how this was calculated however: the difference between equal things is 0, not 1. These errors and all the other imprecisions, lengthy definitions that are for some almost impossible to fathom are the direct result of trying at all costs not to use a single equation, the most important tool in the study of ecology and trade-offs in particular, in a paper on costs of reproduction.

Author response:

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

eLife assessment

In this potentially useful study, the authors attempt to use comparative meta-analysis to advance our understanding of life history evolution. Unfortunately, both the meta-analysis and the theoretical model is inadequate and proper statistical and mechanistic descriptions of the simulations are lacking. Specifically, the interpretation overlooks the effect of well-characterised complexities in the relationship between clutch size and fitness in birds.

Public Reviews:

We would like to thank the reviewers for their helpful comments, which have been considered carefully and have been valuable in progressing our manuscript. The following bullet points summarise the key points and our responses, though our detailed responses to specific comments can be found below:<br /> - Two reviewers commented that our data was not made available. Our data was provided upon submission and during the review process, however was not made accessible to the reviewers. Our data and code are available at https://doi.org/10.5061/dryad.q83bk3jnk.

- The reviewers have highlighted that some of our methodology was unclear and we have added all the requested detail to ensure our methods can be easily understood.

- The reviewers highlight the importance of our conclusions, but also suggest some interpretations might be missing and/or are incomplete. To make clear how we objectively interpreted our data and the wider consequences for life-history theory we provide a decision tree (Figure 5). This figure makes clear where we think the boundaries are in our interpretation and how multiple lines of evidence converge to the same conclusions.

Reviewer #1 (Public Review):

This paper falls in a long tradition of studies on the costs of reproduction in birds and its contribution to understanding individual variation in life histories. Unfortunately, the meta-analyses only confirm what we know already, and the simulations based on the outcome of the meta-analysis have shortcomings that prevent the inferences on optimal clutch size, in contrast to the claims made in the paper.

There was no information that I could find on the effect sizes used in the meta-analyses other than a figure listing the species included. In fact, there is more information on studies that were not included. This made it impossible to evaluate the data-set. This is a serious omission, because it is not uncommon for there to be serious errors in meta-analysis data sets. Moreover, in the long run the main contribution of a meta-analysis is to build a data set that can be included in further studies.

It is disappointing that two referees comment on data availability, as we supplied a link to our full dataset and the code we used in Dryad with our submitted manuscript. We were also asked to supply our data during the review process and we again supplied a link to our dataset and code, along with a folder containing the data and code itself. We received confirmation that the reviewers had been given our data and code. We support open science and it was our intention that our dataset should be fully available to reviewers and readers. Our data and code are at https://doi.org/10.5061/dryad.q83bk3jnk.

The main finding of the meta-analysis of the brood size manipulation studies is that the survival costs of enlarging brood size are modest, as previously reported by Santos & Nakagawa on what I suspect to be mostly the same data set.

We disagree that the main finding of our paper is the small survival cost of manipulated brood size. The major finding of the paper, in our opinion, is that the effect sizes for experimental and observational studies are in opposite directions, therefore providing the first quantitative evidence to support the influential theoretical framework put forward by van Noordwijk and de Jong (1986), that individuals differ in their optimal clutch size and are constrained to reproducing at this level due to a trade-off with survival. We further show that while the manipulation experiments have been widely accepted to be informative, they are not in fact an effective test of whether within-species variation in clutch size is the result of a trade-off between reproduction and survival.

The comment that we are reporting the same finding as Santos & Nakagawa (2012) is a misrepresentation of both that study and our own. Santos & Nakagawa found an effect of parental effort on survival only in males who had their clutch size increased – but no effect for males who had their clutch size reduced and no survival effect on females for either increasing or reducing parental effort. However, we found an overall reduction in survival for birds who had brood sizes manipulated to be larger than their original brood (for both sexes and mixed sex studies combined). In our supplementary information, we demonstrate that the overall survival effect of a change in reproductive effort is close to zero for males, negative (though non-significant) for females and significantly negative for mixed sexes (which are not included in the Santos & Nakagawa study). Please also note that the Santos & Nakagawa study was conducted over 10 years ago. This means we added additional data (L364-365). Furthermore, meta-analyses are an evolving practice and we also corrected and improved on the overall analysis approach (e.g. L358-359 and L 393-397, and see detailed SI).

The paper does a very poor job of critically discussing whether we should take this at face value or whether instead there may be short-comings in the general experimental approach. A major reason why survival cost estimates are barely significantly different from zero may well be that parents do not fully adjust their parental effort to the manipulated brood size, either because of time/energy constraints, because it is too costly and therefore not optimal, or because parents do not register increased offspring needs. Whatever the reason, as a consequence, there is usually a strong effect of brood size manipulation on offspring growth and thereby presumably their fitness prospects. In the simulations (Fig.4), the consequences of the survival costs of reproduction for optimal clutch size were investigated without considering brood size manipulation effects on the offspring. Effects on offspring are briefly acknowledged in the discussion, but otherwise ignored. Assuming that the survival costs of reproduction are indeed difficult to discern because the offspring bear the brunt of the increase in brood size, a simulation that ignores the latter effect is unlikely to yield any insight in optimal clutch size. It is not clear therefore what we learn from these calculations.

The reviewer’s comment is somewhat of a paradox. We take the best studied example of the trade-off between reproductive effort and parental survival – a key theme in life history and the biology of ageing – and subject this to a meta-analysis. The reviewer suggests we should interpret our finding as if there must be something wrong with the method or studies we included, rather than considering that the original hypothesis could be false or inflated in importance. We do not consider questioning the premise of the data over questioning a favoured hypothesis to necessarily be the best scientific approach here. In many places in our manuscript, we question and address, at length, the underlying data and their interpretation (L116-117, L165-167, 202-204 and L277-282). Moreover, we make it clear that we focus on the trade-off between current reproductive effort and subsequent parental survival, while being aware that other trade-offs could counter-balance or explain our findings (discussed on L208-210 & L301-316). Note that it is also problematic, when you do not find the expected response, to search for an alternative that has not been measured. In the case here, of potential trade-offs, there are endless possibilities of where a trade-off might operate between traits. We purposefully focus on the one well-studied and most commonly invoked trade-off. We clearly acknowledge, though, that when all possible trade-offs are taken into account a trade-off on the fitness level can occur and cite two famous studies (Daan et al., 1990 and Verhulst & Tinbergen 1991) that have shown just that (L314-316).

So whilst we agree with the reviewer that the offspring may incur costs themselves, rather than costs being incurred by the parents, the aim of our study was to test for a general trend across species in the survival costs of reproductive effort. It is unrealistic to suggest that incorporating offspring growth into our simulations would add insight, as a change in offspring number rarely affects all offspring in the nest equally and there can even be quite stark differences; for example, this will be most evident in species that produce sacrificial offspring. This effect will be further confounded by catch-up growth, for example, and so it is likely that increased sibling competition from added chicks alters offspring growth trajectories, rather than absolute growth as the reviewer suggests. There are mixed results in the literature on the effect of altering clutch size on offspring survival, with an increased clutch size through manipulation often increasing the number of recruits from a nest.

What we do appreciate from the reviewer’s comment is that the interpretation of our findings is complex. Even though our in-text explanation includes the caveats the reviewer refers to, and are discussed at length, their inter-relationships are hard to appreciate from a text format. To improve this presentation and for ease of the reader, we have added a decision tree (Figure 5) which represents the logical flow from the hypothesis being tested through to what overall conclusion can be drawn from our results. We believe this clarifies what conclusions can be drawn from our results. We emphasise again that the theory that trade-offs between reproductive effort and parental survival being the major driver of variation in offspring production was not supported though is the one that practitioners in the field would be most likely to invoke, and our result is important for this reason.

There are other reasons why brood size manipulations may not reveal the costs of reproduction animals would incur when opting for a larger brood size than they produced spontaneously themselves. Firstly, the manipulations do not affect the effort incurred in laying eggs (which also biases your comparison with natural variation in clutch size). Secondly, the studies by Boonekamp et al on Jackdaws found that while there was no effect of brood size manipulation on parental survival after one year of manipulation, there was a strong effect when the same individuals were manipulated in the same direction in multiple years. This could be taken to mean that costs are not immediate but delayed, explaining why single year manipulations generally show little effect on survival. It would also mean that most estimates of the fitness costs of manipulated brood size are not fit for purpose, because typically restricted to survival over a single year.

First, our results did show a survival cost of reproduction for brood manipulations (L107-123, Figure 1, Table 1). Note, however, that much theory is built on the immediate costs of reproduction and, as such, these costs are likely overinterpreted, meaning that our overall interpretation still holds, i.e. “parental survival trade-off is not the major determinative trade-off in life history within-species” (Figure 5).

We agree with the reviewer that lifetime manipulations could be even more informative than single-year manipulations. Unfortunately, there are currently too few studies available to be able to draw generalisable conclusions across species for lifetime manipulations. This is, however, the reason we used lifetime change in clutch size in our fitness projections, which the reviewer seems to have missed – please see methods line 466-468, where we explicitly state that this is lifetime enlargement. Of course, such interpretations do not include an accumulation of costs that is greater than the annual cost, but currently there is no clear evidence that such an assumption is valid. Such a conclusion can also not be drawn from the study on jackdaws by Boonekamp et al (2014) as the treatments were life-long and, therefore, cannot separate annual from accrued (multiplicative) costs that are more than the sum of the annual costs incurred. Note that we have now included specific discussion of this study in response to the reviewer (L265-269).

Details of how the analyses were carried out were opaque in places, but as I understood the analysis of the brood size manipulation studies, manipulation was coded as a covariate, with negative values for brood size reductions and positive values for brood size enlargements (and then variably scaled or not to control brood or clutch size). This approach implicitly assumes that the trade-off between current brood size (manipulation) and parental survival is linear, which contrasts with the general expectation that this trade-off is not linear. This assumption reduces the value of the analysis, and contrasts with the approach of Santos & Nakagawa.

We thank the reviewer for highlighting a lack of clarity in places in our methods. We have added additional detail to the methodology section (see “Study sourcing & inclusion criteria” and “Extracting effect sizes”) in our revised manuscript. Note, that our data and code was not shared with the reviewers despite us supplying this upon submission and again during the review process, which would have explained a lot more of the detail required.

For clarity in our response, each effect size was extracted by performing a logistic regression with survival as a binary response variable and clutch size was the absolute value of offspring in the nest (i.e., for a bird that laid a clutch size of 5 but was manipulated to have -1 egg, we used a clutch size value of 4). The clutch size was also standardised and, separately, expressed as a proportion of the species’ mean.

We disagree that our approach reduces the value of our analysis. First, our approach allows a direct comparison between experimental and observational studies, which is the novelty of our study. Our approach does differ from Santos & Nakagawa but we disagree that it contrasts. Our approach allows us to take into consideration the severity of the change in clutch size, which Santos & Nakagawa do not. Therefore, we do not agree that our approach is worse at accounting for non-linearity of trade-offs than the approach used by Santos & Nakagawa. Arguably, the approach by Santos & Nakagawa is worse, as they dichotomise effort as increased or decreased, factorise their output and thereby inflate their number of outcomes, of which only 1 cell of 4 categories is significant (for males and females, increased and decreased brood size). The proof is in the pudding as well, as our results clearly demonstrate that the magnitude of the manipulation is a key factor driving the results, i.e. one offspring for a seabird is a larger proportion of care (and fitness) than one offspring for a passerine. Such insights were not achieved by Santos & Nakagawa’s method and, again, did not allow a direct quantitative comparison between quality (correlational) and experimental (brood size manipulation, i.e. “trade-off”) effects, which forms a central part of our argumentation (Figure 5). 

Our analysis, alongside a plethora of other ecological studies, does assume that the response to our predictor variable is linear. However, it is common knowledge that there are very few (if any) truly linear relationships. We use linear relationships because they serve a good approximation of the trend and provide a more rigorous test for an underlying relationship than would fitting nonlinear models. For many datasets the range of added chicks required to estimate a non-linear relationship was not available. The question also remains of what the shape of such a non-linear relationship should be and is hard to determine a priori. There is also a real risk when fitting non-linear terms that they are spurious and overinterpreted, as they often present a better fit (denoting one df is not sufficient especially when slopes vary). We have added this detail to our discussion.

The observational study selection is not complete and apparently no attempt was made to make it complete. This is a missed opportunity - it would be interesting to learn more about interspecific variation in the association between natural variation in clutch size and parental survival.

We clearly state in our manuscript that we deliberately tailored the selection of studies to match the manipulation studies (L367-369). We paired species extracted for observational studies with those extracted in experimental studies to facilitate a direct comparison between observational and experimental studies, and to ensure that the respective datasets were comparable. The reviewer’s focus in this review seems to be solely on the experimental dataset. This comment dismisses the equally important observational component of our analysis and thereby fails to acknowledge one of the key questions being addressed in this study. Note that in our revised version we have edited the phylogenetic tree to indicate for which species we have both types of information, which highlights our approach to selecting observational data (Figure 3).

Reviewer #2 (Public Review):

I have read with great interest the manuscript entitled "The optimal clutch size revisited: separating individual quality from the costs of reproduction" by LA Winder and colleagues. The paper consists in a meta-analysis comparing survival rates from studies providing clutch sizes of species that are unmanipulated and from studies where the clutch sizes are manipulated, in order to better understand the effects of differences in individual quality and of the costs of reproduction. I find the idea of the manuscript very interesting. However, I am not sure the methodology used allows to reach the conclusions provided by the authors (mainly that there is no cost of reproduction, and that the entire variation in clutch size among individuals of a population is driven by "individual quality").

We would like to highlight that we do not conclude that there is no cost of reproduction. Please see lines 336–339, where we state that our lack of evidence for trade-offs driving within-species variation in clutch size does not necessarily mean the costs of reproduction are non-existent. We conclude that individuals are constrained to their optima by the survival cost of reproduction. It is also an over-statement of our conclusion to say that we believe that variation in clutch size is only driven by quality. Our results show that unmanipulated birds that have larger clutch sizes also lived longer, and we suggest that this is evidence that some individuals are “better” than others, but we do not say, nor imply, that no other factors affect variation in clutch size. We have added Figure 5 to our manuscript to help the reader better understand what questions we can answer with our study and what conclusions we can draw from our results.

I write that I am not sure, because in its current form, the manuscript does not contain a single equation, making it impossible to assess. It would need at least a set of mathematical descriptions for the statistical analysis and for the mechanistic model that the authors infer from it.

We appreciate this comment, and have explained our methods in terms that are accessible to a wider audience. Note, however, that our meta-analysis is standard and based on logistic regression and standard meta-analytic practices. We have added the model formula to the model output tables.

For the simulation, we simply simulated the resulting effects. We of course supplied our code for this along with our manuscript (https://doi.org/10.5061/dryad.q83bk3jnk), though as we mentioned above, we believe this was not shared with the reviewers despite us making this available for the review process. We therefore understand why the reviewer feels the simulations were not explained thoroughly. We have revised our methods section and added details which we believe make our methodology more clear without needing to consult the supplemental material. However, we have also added the equations used in the process of calculating our simulated data to the Supplementary Information for readers who wish to have this information in equation form.

The texts mixes concepts of individual vs population statistics, of within individual vs among-individuals measures, of allocation trade-offs and fitness trade-offs, etc ....which means it would also require a glossary of the definitions the authors use for these various terms, in order to be evaluated.

We would like to thank the reviewer for highlighting this lack of clarity in our text. Throughout the manuscript we have refined our terminology and indicated where we are referring to the individual level or the population level. The inclusion of our new Figure 5 (decision tree) should also help in this context, as it is clear on which level we base our interpretation and conclusions on.

This problem is emphasised by the following sentence to be found in the discussion "The effect of birds having naturally larger clutches was significantly opposite to the result of increasing clutch size through brood manipulation". The "effect" is defined as the survival rate (see Fig 1). While it is relatively easy to intuitively understand what the "effect" is for the unmanipulated studies: the sensitivity of survival to clutch size at the population level, this should be mentioned and detailed in a formula. Moreover, the concept of effect size is not at all obvious for the manipulated ones (effect of the manipulation? or survival rate whatever the manipulation (then how could it measure a trade-off ?)? at the population level? at the individual level ?) despite a whole appendix dedicated to it. This absolutely needs to be described properly in the manuscript.

Thank you for identifying this sentence for which the writing was ambiguous, our apologies. We have now rewritten this and included additional explanation. L282-290: ‘The effect on parental annual survival of having naturally larger clutches was significantly opposite to the result of increasing clutch size through brood manipulation, and quantitatively similar. Parents with naturally larger clutches are thus expected to live longer and this counterbalances the “cost of reproduction” when their brood size is experimentally manipulated. It is, therefore, possible that quality effects mask trade-offs. Furthermore, it could be possible that individuals that lay larger clutches have smaller costs of reproduction, i.e. would respond less in terms of annual survival to a brood size manipulation, but with our current dataset we cannot address this hypothesis (Figure 5).’

We would also like to thank the reviewer for bringing to our attention the lack of clarity about the details of our methodology. We have added details to our methodology (see “Extracting effect sizes” section) to address this (see highlighted sections). For clarity, the effect size for both manipulated and unmanipulated nests was survival, given the brood size raised. We performed a logistic regression with survival as a binary response variable (i.e., number of individuals that survived and number of individuals that died after each breeding season), and clutch size was the absolute value of offspring in the nest (i.e., for a bird that laid a clutch size of 5 but was manipulated to have -1 egg, we used a clutch size value of 4). This allows for direct comparison of the effect size (survival given clutch size raised) between manipulated and unmanipulated birds.

Despite the lack of information about the underlying mechanistic model tested and the statistical model used, my impression is still that the interpretation in the introduction and discussion is not granted by the outputs of the figures and tables. Let's use a model similar to that of (van Noordwijk and de Jong, 1986): imagine that the mechanism at the population level is

a.c_(i,q)+b.s_(i,q)=E_q

Where c_(i,q) are s_(i,q) are respectively the clutch size for individual i which is of quality q, and E_q is the level of "energy" that an individual of quality q has available during the given time-step (and a and b are constants turning the clutch size and survival rate into energy cost of reproduction and energy cost of survival, and there are both quite "high" so that an extra egg (c_(i,q) is increased by 1) at the current time-step, decreases s_(i,q) markedly (E_q is independent of the number of eggs produced), that is, we have strong individual costs of reproduction). Imagine now that the variance of c_(i,q) (when the population is not manipulated) among individuals of the same quality group, is very small (and therefore the variance of s_(i,q) is very small also) and that the expectation of both are proportional to E_q. Then, in the unmanipulated population, the variance in clutch size is mainly due to the variance in quality. And therefore, the larger the clutch size c_(i,q) the higher E_q, and the higher the survival s_(i,q).

In the manipulated populations however, because of the large a and b, an artificial increase in clutch size, for a given E_q, will lead to a lower survival s_(i,q). And the "effect size" at the population level may vary according to a,b and the variances mentioned above. In other words, the costs of reproduction may be strong, but be hidden by the data, when there is variance in quality; however there are actually strong costs of reproduction (so strong actually that they are deterministic and that the probability to survive is a direct function of the number of eggs produced)

We would like to thank the reviewer for these comments. We have added detail to our methodology section so our models and rationale are more clear. Please note that our simulations only take the experimental effect of brood size on parental survival into account. Our model does not incorporate quality effects. The reviewer is right that the relationship between quality and the effects exposed by manipulating brood size can take many forms and this is a very interesting topic, but not one we aimed to tackle in our manuscript. In terms of quality we make two points: (1) overall quality effects connecting reproduction and parental survival are present, (2) these effects are opposite in direction to the effects when reproduction is manipulated and similar in magnitude. We do not go further than that in interpreting our results. The reviewer is correct, however, that we do suggest and repeat suggestions by others that quality can also mask the trade-off in some individuals or circumstances (L74-76, L95-98 & L286-289), but we do not quantify this, as it is dependent on the unknown relationship between quality and the response to the manipulation. A focussed set of experiments in that context would be interesting and there are some data that could get at this, i.e. the relationship between produced clutch size and the relative effect of the manipulation (now included L287-290). Such information is, however, not available for all studies and, although we explored the possibility of analysing this, currently this is not possible with adequate confidence and there is the possible complexity of non-linear effects. We have added this rationale in our revision (L259-265).

Moreover, it seems to me that the costs of reproduction are a concept closely related to generation time. Looking beyond the individual allocative (and other individual components of the trade-off) cost of reproduction and towards a populational negative relationship between survival and reproduction, we have to consider the intra-population slow fast continuum (some types of individuals survive more and reproduce less (are slower) than other (which are faster)). This continuum is associated with a metric: the generation time. Some individuals will produce more eggs and survive less in a given time-period because this time-period corresponds to a higher ratio of their generation time (Gaillard and Yoccoz, 2003; Gaillard et al., 2005). It seems therefore important to me, to control for generation time and in general to account for the time-step used for each population studied when analysing costs of reproduction. The data used in this manuscript is not just clutch size and survival rates, but clutch size per year (or another time step) and annual (or other) survival rates.

The reviewer is right that this is interesting. There is a longstanding unexplained difference in temperate (seasonal) and tropical reproductive strategies. Most of our data come from seasonal breeders, however. Although there is some variation in second brooding and such, these species mostly only produce one brood. We do agree that a wider consideration here is relevant, but we are not trying to explain all of life history in our paper. It is clearly the case that other factors will operate and the opportunity for trade-offs will vary among species according to their respective life histories. However, our study focuses on the two most fundamental components of fitness – longevity and reproduction – to test a major hypothesis in the field, and we uncover new relationships that contrast with previous influential studies and cast doubt on previous conclusions. We question the assumed trade-off between reproduction and annual survival. We show that quality is important and that the effect we find in experimental studies is so small that it can only explain between-species patterns but is unlikely to be the selective force that constrains reproduction within species. We do agree that there is a lot more work that can be done in this area. We hope we are contributing to the field, by questioning this central trade-off. We have incorporated some of the reviewers suggestions in the revision (L309-315). We have added Figure 5 to make clear where we are able to reach solid conclusions and the evidence on which these are based as clearly as possible in an easily accessible format.

Finally, it is important to relate any study of the costs of reproduction in a context of individual heterogeneity (in quality for instance), to the general problem of the detection of effects of individual differences on survival (see, e.g., Fay et al., 2021). Without an understanding of the very particular statistical behaviour of survival, associated to an event that by definition occurs only once per life history trajectory (by contrast to many other traits, even demographic, where the corresponding event (production of eggs for reproduction, for example) can be measured several times for a given individual during its life history trajectory).

Thank you for raising this point. The reviewer is right that heterogeneity can dampen or augment selection. Note that by estimating the effect of quality here we give an example of how heterogeneity can possibly do exactly this. We thank the reviewer for raising that we should possibly link this to wider effects of heterogeneity and we have added to our discussion of how our results play into the importance of accounting for among-individual heterogeneity (L252-256).

References:

Fay, R. et al. (2021) 'Quantifying fixed individual heterogeneity in demographic parameters: Performance of correlated random effects for Bernoulli variables', Methods in Ecology and Evolution, 2021(August), pp. 1-14. doi: 10.1111/2041-210x.13728.

Gaillard, J.-M. et al. (2005) 'Generation time: a reliable metric to measure life-history variation among mammalian populations.', The American naturalist, 166(1), pp. 119-123; discussion 124-128. doi: 10.1086/430330.

Gaillard, J.-M. and Yoccoz, N. G. (2003) 'Temporal Variation in Survival of Mammals: a Case of Environmental Canalization?', Ecology, 84(12), pp. 3294-3306. doi: 10.1890/02-0409.

van Noordwijk, A. J. and de Jong, G. (1986) 'Acquisition and Allocation of Resources: Their Influence on Variation in Life History Tactics', American Naturalist, p. 137. doi: 10.1086/284547.

Reviewer #3 (Public Review):

The authors present here a comparative meta-analysis analysis designed to detect evidence for a reproduction/ survival trade-off, central to expectations from life history theory. They present variation in clutch size within species as an observation in conflict with expectations of optimisation of clutch size and suggest that this may be accounted for from weak selection on clutch size. The results of their analyses support this explanation - they found little evidence of a reproduction - survival trade-off across birds. They extrapolated from this result to show in a mathematical model that the fitness consequences of enlarged clutch sizes would only be expected to have a significant effect on fitness in extreme cases, outside of normal species' clutch size ranges. Given the centrality of the reproduction-survival trade-off, the authors suggest that this result should encourage us to take a more cautious approach to applying concepts the trade-off in life history theory and optimisation in behavioural ecology more generally. While many of the findings are interesting, I don't think the argument for a major re-think of life history theory and the role of trade-offs in fitness maximisation is justified.

The interest of the paper, for me, comes from highlighting the complexities of the link between clutch size and fitness, and the challenges facing biologists who want to detect evidence for life history trade-offs. Their results highlight apparently contradictory results from observational and experimental studies on the reproduction-survival trade-off and show that species with smaller clutch sizes are under stronger selection to limit clutch size.

Unfortunately, the authors interpret the failure to detect a life history trade-off as evidence that there isn't one. The construction of a mathematical model based on this interpretation serves to give this possible conclusion perhaps more weight than is merited on the basis of the results, of this necessarily quite simple, meta-analysis. There are several potential complicating factors that could explain the lack of detection of a trade-off in these studies, which are mentioned and dismissed as unimportant (lines 248-250) without any helpful, rigorous discussion. I list below just a selection of complexities which perhaps deserve more careful consideration by the authors to help readers understand the implications of their results:

We would like to thank the reviewer for their thoughtful response and summary of the findings that we also agree are central to our study. The reviewer also highlights areas where our manuscript could benefit from a deeper consideration and we have added detail accordingly to our revised discussion.

We would like to highlight that we do not interpret the failure to detect a trade-off as evidence that there is not one. First, and importantly, we do find a trade-off but show this is only incurred when individuals produce a clutch beyond their optimal level. Second, we also state on lines 322-326 that the lack of evidence to support trade-offs being strong enough to drive variation in clutch size does not necessarily mean there are no costs of reproduction.

The statement that we have constructed a mathematical model based on the interpretation that we have not found a trade-off is, again, factually incorrect. We ran these simulations because the opposite is true – we did find a trade-off. There is a significant effect of clutch size when manipulated on annual parental survival. We benefit from our unique analysis allowing for a quantitative fitness estimate from the effect size on annual survival (as this is expressed on a per-egg basis). This allowed us to ask whether this quantitative effect size can alone explain why reproduction is constrained, and we evaluate this using simulations. From these simulations we find that this effect size is too small to explain the constraint, so something else must be going on, and we do spend a considerable amount of text discussing the possible explanations (L202-215). Note that the possibly most parsimonious conclusion here is that costs of reproduction are not there, or simply small, so we also give that explanation some thought (L221-224 and L315-331).

We are disappointed by the suggestion that we have dismissed complicating factors that could prevent detection of a trade-off, as this was not our intention. We were aiming to highlight that what we have demonstrated to be an apparent trade-off can be explained through other mechanisms, and that the trade-off between clutch size and survival is not as strong in driving within-species variation in clutch size as previously assumed. We have added further discussion to our revised manuscript to make this clear and give readers a better understanding of the complexity of factors associated with life-history theory, including the addition of a decision tree (Figure 5).

• Reproductive output is optimised for lifetime reproductive success and so the consequences of being pushed off the optimum for one breeding attempt are not necessarily detectable in survival but in future reproductive success (and, therefore, lifetime reproductive success).

We agree this is a valid point, which is mentioned in our manuscript in terms of alternative stages where the costs of reproduction might be manifested (L316-320). We would also like to highlight that , in our simulations, the change in clutch size (and subsequent survival cost) was assumed for the lifetime of the individual, for this very reason.

• The analyses include some species that hatch broods simultaneously and some that hatch sequentially (although this information is not explicitly provided (see below)). This is potentially relevant because species which have been favoured by selection to set up a size asymmetry among their broods often don't even try to raise their whole broods but only feed the biggest chicks until they are sated; any added chicks face a high probability of starvation. The first point this observation raises is that the expectation of more chicks= more cost, doesn't hold for all species. The second more general point is that the very existence of the sequential hatching strategy to produce size asymmetry in a brood is very difficult to explain if you reject the notion of a trade-off.

We agree with the reviewer that the costs of reproduction can be absorbed by the offspring themselves, and may not be equal across offspring (we also highlight this at L317-318 in the manuscript). However, we disagree that for some species the addition of more chicks does not equate to an increase in cost, though we do accept this might be less for some species. This is, however, difficult to incorporate into a sensible model as the impacts will vary among species and some species do also exhibit catch-up growth. So, without a priori knowledge on this, we kept our model simple to test whether the effect on parental survival (often assumed to be a strong cost) can explain the constraint on reproductive effort, and we conclude that it does not.

We would also like to make clear that we are not rejecting the notion of a trade-off. Our study shows evidence that a trade-off between survival and reproductive effort probably does not drive within-species variation in clutch size. We do explicitly say this throughout our manuscript, and also provide suggestions of other areas where a trade-off may exist (L317-320). The point of our study is not whether trade-offs exist or not, it is whether there is a generalisable across-species trend for a trade-off between reproductive effort and survival – the most fundamental trade-off in our field but for which there is a lack of conclusive evidence within species. We believe the addition of Figure 5 to our reviewed manuscript also makes this more evident.

• For your standard, pair-breeding passerine, there is an expectation that costs of raising chicks will increase linearly with clutch size. Each chick requires X feeding visits to reach the required fledge weight. But this is not the case for species which lay precocious chicks which are relatively independent and able to feed themselves straight after hatching - so again the relationship of care and survival is unlikely to be detectable by looking at the effect of clutch size but again, it doesn't mean there isn't a trade-off between breeding and survival.

Precocial birds still provide a level of parental care, such as protection from predators. Though we agree that the level of parental care in provisioning food (and in some cases in all parental care given) is lower in precocial than altricial birds, this would only make our reported effect size for manipulated birds to be an underestimate. Again, we would like to draw the reviewer’s attention to the fact we did detect a trade-off in manipulated birds and we do not suggest that trade-offs do not exist. The argument the reviewer suggests here does not hold for unmanipulated birds, as we found that birds that naturally lay larger clutch sizes have higher survival.

• The costs of raising a brood to adulthood for your standard pair-breeding passerine is bound to be extreme, simply by dint of the energy expenditure required. In fact, it was shown that the basal metabolic rate of breeding passerines was at the very edge of what is physiologically possible, the human equivalent being cycling the Tour de France (Nagy et al. 1990). If birds are at the very edge of what is physiologically possible, is it likely that clutch size is under weak selection?

If birds are at the very edge of what is physiologically possible, then indeed it would necessarily follow that if they increase the resource allocated in one area then expenditure in another area must be reduced. In many studies, however, the overall brood mass is increased when chicks are added and cared for in an experimental setting, suggesting that birds are not operating at their limit all the time. Our simulations show that if individuals increase their clutch size, the survival cost of reproduction counterbalances the fitness gained by increasing clutch size and so there is no overall fitness gain to producing more offspring. Therefore, selection on clutch size is constrained to the within-species level. We do not say in our manuscript that clutch size is under weak selection – we only ask why variation in clutch size is maintained if selection always favours high-producing birds.

• Variation in clutch size is presented by the authors as inconsistent with the assumption that birds are under selection to lay the Lack clutch. Of course, this is absurd and makes me think that I have misunderstood the authors' intended point here. At any rate, the paper would benefit from more clarity about how variable clutch size has to be before it becomes a problem for optimality in the authors' view (lines 84-85; line 246). See Perrins (1965) for an exquisite example of how beautifully great tits optimise clutch size on average, despite laying between 5-12 eggs.

We thank the reviewer for highlighting that our manuscript may be misleading in places, however, we are unsure which part of our conclusions the author is referring to here. The question we pose is “Why don’t all birds produce a clutch size at the population optimum?”, and is central to the decades-long field of life-history theory. Why is variation maintained? As the reviewer outlines, there is extensive variability, with some birds laying half of what other birds lay.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) Title: while the costs of reproduction are possibly important in shaping optimal clutch size, it is not clear what you can about it given that you do not consider clutch / brood size effects on fitness prospects of the offspring.

We have expanded on our discussion of how some costs may be absorbed by the offspring themselves. However, a change in offspring number rarely affects all offspring in the nest equally and there can even be quite stark differences; for example this will be most evident in species that produce sacrificial offspring. This effect will be further confounded by catch-up growth. There are mixed results in the literature on the effect of altering clutch size on offspring survival, with an increased clutch size through manipulation often increasing the number of recruits from a nest. We have focussed on the relationship between reproductive effort and survival because it is given the most weight in the field in terms of driving intra-specific variation in clutch size. We have altered our title to show we focus on the survival costs specifically: “The optimal clutch size revisited: separating individual quality from the parental survival costs of reproduction”.

(2) L.11-12: I agree that this is true for birds, but this is phrased more generally here. Are you sure that that is justified?

The trade-off between survival and reproductive effort has largely been tested experimentally through brood manipulations in birds as this provides a good system in which to test the costs and benefits of increasing parental effort. The work in this area has provided theory beyond just passerine birds, which are the most commonly manipulated group, to across-taxa theories. We are unaware of any study/studies that provide evidence that the reproduction/survival trade-off is generalisable across multiple species in any taxa. As such, we do believe this sentence is justified. An example is the lack of a consistent negative genetic correlation in populations of fruitflies, for example, that has also been hailed as a lack-of-cost paradigm. Furthermore, some mutants that live longer do so without a cost on reproduction.

(3) L.13-14: Not sure what you mean with this sentence - too much info lacking.

We have added some detail to this sentence.

(4) L.14: it is slightly awkward to say 'parental investment and survival' because it is the survival effect that is usually referred to as the 'investment'. Perhaps what you want to say is 'parental effort and survival'?

We have replaced “parental investment” with “reproductive effort”

(5) L.15: you can omit 'caused'. Compared to control treatment or to reduced broods? Why not mention effects or lack thereof of brood reduction? And it would be good to also mention here whether effects were similar in the sexes.

Please see our methodology where we state that we use clutch size as a continuous variable (we do not compare to control or reduced but include the absolute value of offspring in a logistic regression). The effects of a brood reduction are drawn from the same regression and so are opposite. Though we appreciate the detail here is lacking to fully comprehend our study, we would like to highlight this is the abstract and details are provided in the main text.

(6) L. 15: I am not sure why you write 'however', as the finding that experimental and natural variation have opposite effects is in complete agreement with what is generally reported in the literature and will therefore surprise no one that is aware of the literature.

We use “however” to highlight the change in direction of the effect size from the results in the previous sentence. We also believe that ours ise the first study that provides a quantitative estimate of this effect and that previous work is largely theoretical. The reviewer states that this is what is generally reported but it is not reported in all cases, as some relationships between reproductive effort and survival are negative (for the quality measurement, in correlational space, see Figure 1).

(7) L.16: saying 'opposite to the effect of phenotypic quality' seems difficult to justify, as clutch size cannot be equated with phenotypic quality. Perhaps simply say 'natural variation in clutch size'? If that is what you are referring to.

Please note we are referring to effect sizes here –- that is, the survival effect of a change in clutch size. By phenotypic quality we are referring to the fact that we find higher parental survival when natural clutch sizes are higher. It is not the case that we refer to quality only as having a higher clutch size. This is explicitly stated in the sentence you refer to. We have changed “effect” to “effect size” to highlight this further.

(8) L.18: why do you refer to 'parental care' here? Brood size is not equivalent to parental care.

Brood size manipulations are used to manipulate parental care. The effect on parental survival is expected to be incurred because of the increase in parental care. We have changed “parental care” to “reproductive effort” to reduce the number of terms we use in our manuscript.

(9) L.18-19: suggest to tone down this claim, as this is no more than a meta-analytic confirmation of a view that is (in my view) generally accepted in the field. That does not mean it is not useful, just that it does not constitute any new insight.

We are unaware of any other study which provides generalisable across-species evidence for opposite effects of quality and costs of reproduction. The work in this area is also largely theoretical and is yet to be supported experimemtally, especially in a quantitative fashion. It is surprising to us that the reviewer considers there to be general acceptance in a field, rather than being influenced by rigorous testing of hypotheses, made possible by meta-analysis, the current gold standard in our field.

(10) L.21: what does 'parental effort' mean here? You seem to use brood size, parental care, parental effort, and parental investment interchangeably but these are different concepts. Daan et al (1990, Behaviour), which you already cite, provide a useful graph separating these concepts. Please adjust this throughout the manuscript, i.e. replace 'reproductive effort' with wording that reflect the actual variable you use.

We have not used the phrase “parental effort” in this sentence. We agree these are different concepts but in this context are intertwined. For example, brood size is used to manipulate parental care as a result of increased parental effort. We do agree the manuscript would benefit from keeping terminology consistent throughout the manuscript and have adjusted this throughout.

(11) L.23: perhaps add 'in birds' somewhere in this sentence? Some reference to the assumptions underlying this inference would also be useful. Two major assumptions being that birds adjusted their effort to the manipulation as they would have done had they opted for a larger brood size themselves, and that the costs of laying and incubating extra eggs can be ignored. And then there is the effect that laying extra eggs will usually delay the hatch date, which in many species reduces reproductive success.

Though our study does exclusively use birds, birds have been used to test the survival/reproduction trade-off because they present a convenient system in which to experimentally test this. The conclusions from these studies have a broader application than in birds alone. We believe that although these details are important, they are not appropriate in the abstract of our paper.

(12) L.26: how is this an explanation? It just repeats the finding.

We intend to refer to all interpretations from all results presented in our manuscript. We have made this more clear by adjusting our writing.

(13) L.27: I do not see this point. And 'reproductive output' is yet another concept, that can be linked to the other concepts in the abstract in different ways, making it rather opaque.

We have changed “reproductive output” to “reproductive effort”.

(14) L.33: here you are jumping from 'resources' to 'energetically' - it is not clear that energy is the only or main limiting resource, so why narrow this down to energy?

We do not say energy is the only or main limiting resource. We simply highlight that reproduction is energetically demanding and so, intuitively, a trade-off with a highly energetically demanding process would be the focal place to observe a trade off. We have, though, replaced “energetically” with “resource”.

(15) L.35-36: this is new to me - I am not aware of any such claims, and effects on the residual reproductive value could also arise through effects on future reproduction. The authors you cite did not work on birds, or (in their own study systems) presented results that as far as I remember warrant such a general statement.

The trade-off between reproduction and survival is seminal to the disposable soma theory, proposed by Kirkwood. Though Kirkwood’s work was largely not focussed on birds, it had fundamental implications for the field of evolutionary ecology because of the generalisable nature of his proposed framework. In particular, it has had wide-reaching influence on how the biology of aging is interpreted. The readership of the journal here is broad, and our results have implications for that field too. The work of Kirkwood (many of the papers on this topic have over 2000 citations each) has been perhaps overly influential in many areas, so a link to how that work should be interpreted is highly relevant. If the reviewer is interested in this topic the following papers by one of the co-authors and others could be of interest, some of which we could not cite in the main manuscript due to space considerations:

https://www.science.org/doi/pdf/10.1126/sciadv.aay3047

https://agingcelljournal.org/Archive/Volume3/stochasticity_explains_non_genetic_inheritance_of_lifespan/

https://pubmed.ncbi.nlm.nih.gov/21558242/

https://besjournals.onlinelibrary.wiley.com/doi/full/10.1111/1365-2435.13444

https://www.nature.com/articles/362305a0

https://www.cell.com/trends/ecology-evolution/fulltext/S0169-5347(12)00147-4

https://www.cell.com/cell/pdf/S0092-8674(15)01488-9.pdf

https://bmcbiol.biomedcentral.com/articles/10.1186/s12915-018-0562-z

(16) L.42: this could be preceded with mentioning the limitations of observational data.

We have added detail as to why brood manipulations are a good test for trade-offs and so this is now inherently implied.

(17) L.42-43: why?

We have added detail to this sentence.

(18) L.45: do any of the references cited here really support this statement? I am certain that several do not - in these this statement is an assumption rather than something that is demonstrated. It may be useful to look at Kate Lessell's review on this that appeared in Etologia, I think in the 1990's. Mind however that 'reproductive effort' is operationally poorly defined for reproducing birds - provisioning rate is not necessarily a good measure of effort in so far as there are fitness costs.

We have updated the references to support the sentence.

(19) L.47: Given that you make this statement with respect to brood size manipulations in birds, it seems to me that the paper by Santos & Nakagawa is the only paper you should cite here. Given that you go on to analyze the same data it deserves to be discussed in more detail, for example to clarify what you aim to add to their analysis. What warrants repeating their analysis?

Please first note that our dataset includes Santos & Nakagawa and additional studies, so it is not accurate to say we analyse the same data. Furthermore, we believe our study has implications beyond birds alone and so believe it is appropriate to cite the papers that do support our statement. We have added details to the methods to explicitly state what data is gathered from Santos & Nakagawa (it is only used to find the appropriate literature and data was re-extracted and re-analysed in a more appropriate way) and, separately, how we gathered the observational studies (see L352-381).

(20) L.48: There are more possible explanations to this, which deserve to be discussed. For example, brood size manipulations may not have been that effective in manipulating reproductive effort - for example, effects on energy expenditure tend to be not terribly convincing. Secondly, the manipulations do not affect the effort incurred in laying eggs (which also biases your comparison with natural variation in clutch size). Thirdly, the studies by Boonekamp et al on Jackdaws found that while there was no effect of brood size manipulation on parental survival after one year of manipulation, there was a strong effect when the same individuals were manipulated in the same direction in multiple years. This could be taken to mean that costs are not immediate but delayed, explaining why single year manipulations generally show little effect on survival. It would also mean that most estimates of the fitness costs of manipulated brood size are not fit for purpose, because typically restricted to survival over a single year.

Please see our response to this comment in the public reviews.

Out of interest and because the reviewer mentioned “energy expenditure” specifically: There are studies that show convincing effects of brood size manipulation on parental energy expenditure. We do agree that there are also studies that show ceilings in expenditure. We therefore disagree that they “tend to be not terribly convincing”. Just a few examples:

https://academic.oup.com/beheco/article/10/5/598/222025 (Figure 2)

https://besjournals.onlinelibrary.wiley.com/doi/full/10.1111/1365-2435.12321 (Figure 1)

https://besjournals.onlinelibrary.wiley.com/doi/full/10.1046/j.1365-2656.2000.00395.x (but ceiling at enlarged brood).

(21) L.48, "or, alternatively, that individuals may differ in quality": how do you see that happening when brood size is manipulated, and hence 'quality' of different experimental categories can be assumed to be approximately equal? This point does apply to observational studies, so I assume that that is what you had in mind, but that distinction should be clear (also on line 54).

We have made it more clear that we determine if there are quality effects separate to the costs of reproduction found using brood manipulation studies.

(22) L.50: Drent & Daan, in their seminal paper on "The prudent parent" (1980, Ardea) were among the earliest to make this point and deserve to be cited here.

We have added this citation

(23) L.51, "relative importance": relative to what? Please be more specific.

We have adjusted this sentence.

(24) L.54: Vedder & Bouwhuis (2018, Oikos) go some way towards this point and should be explicitly mentioned with reference to the role of 'quality' effects on the association between reproductive output and survival.

We have added this reference.

(25) L.55: can you be more specific on what you want to do exactly? What you write here could be interpreted differently.

We have added an explicit aim after this sentence to be more clear.

(26) L.57: Here also a more specific wording would be useful. What does it mean exactly when you say you will distinguish between 'quality' and 'costs'?

We have added detail to this sentence.

(27) L.62: it should be clearer from the introduction that this is already well known, which will indirectly emphasize what you are adding to what we know already.

We would argue this is not well known and has only been theorised but not shown empirically, as we do here.

(28) L.62: you equate clutch size with 'quality' here - that needs to be spelled out.

We refer to quality as the positive effect size of survival for a given clutch size, not clutch size alone. We appreciate this is not clear in this sentence and have reworded.

(29) L.64: this looks like a serious misunderstanding to me, but in any case, these inferences should perhaps be left to the discussion (this also applies to later parts of this paragraph), when you have hopefully convinced readers of the claims you make on lines 62-63.

We are unsure of what the reviewer is referring to as a misunderstanding. We have chosen this format for the introduction to highlight our results. If this is a problem for the editors we will change as required.

(30) L.66: quantitative comparison of what?

Comparison of species. We have changed the wording of this sentence

(31) L.67-69: this should be in the methods.

We have used a modern format which highlights our result. We are happy to change the format should the editors wish us to.

(32) L.74-88: suggest to (re)move this entire paragraph, presenting inferences in such an uncritical manner before presenting the evidence is inappropriate in my view. I have therefore refrained from commenting on this paragraph.

We have chosen a modern format which highlights our result. We are happy to change the format should the editors wish us to.

(33) L.271, "must detail variation in the number of raised young": it is not sufficiently clear what this means - what does 'detail' mean in this context? And what does 'number of raised young' mean? The number hatched or raised to fledging?

We have now made this clear.

(34) L271, "must detail variation in the number of raised young": looking at table S4, it seems that on the basis of this criterion also brood size manipulation studies where details on the number of young manipulated were missing are excluded. I see little justification for this - surely these manipulations can for example be coded as for example having the average manipulation size in the meta-analysis data set, thereby contributing to tests of manipulation effects, but not to variation within the manipulation groups?

We have done in part what the reviewer describes. We are specifically interested in the manipulation size, so we required this to compare effect sizes across species and categories, a key advance of our study and outlined in many places in our manuscript. Note, however, that we only need comparative differences, and have used clutch size metrics more generally to obtain a mean clutch size for a species, as well as SD where required. Please also note that our supplement details exactly why studies were excluded from our analysis, as is the preferred practice in a meta-analysis.

(35) L.271, "referred to as clutch size": the point of this simplification is not clear to me why it is clearly confusing - why not refer to 'brood size' instead?

Brood size and clutch size can be used interchangeably here because, in the observational studies, the individuals vary in the number of eggs produced, whereas for brood manipulations this obviously happens after hatching and brood is perhaps a more appropriate term, but we wanted to simplify the terminology used. However, we use clutch size throughout as the aim of our study is to determine why individuals differ in the number of offspring they produce, and so clutch size is the most appropriate term for that.

(36) L.280: according to the specified inclusion criteria (lines 271/272) these studies should already be in the data set, so what does this mean exactly?

Selection criteria refers to whether a given study should be kept for analysis or not. It does not refer to how studies were found. Please see lines 361-378 for details on how we found studies (additional details are also in the Supplementary Methods).

(37) L.281: the use of 'quality' here is misleading - natural variation in clutch or brood size will have multiple causes, variation in phenotypic quality of the individuals and their environment (territories) is only one of the causes. Why not simply refer to what you are actually investigating: natural and experimental variation in brood size.

We disagree, our study aims to separate quality effects from the costs of reproduction and we use observational studies to test for quality differences, though we make no inference about the mechanisms. We do not imply that the environment causes differences in quality, but that to directly compare observation and experimental groups, they should contain similar species. So, to be clear again, quality refers to the positive covariation of clutch size with survival. We feel that we explain this clearly in our study’s rationale and have also improved our writing in several sections on this to avoid any confusion (see responses to earlier comments by the three reviewers).

(38) L.283, "in most cases": please be exact and say in xx out xx cases.

We have added the number of studies for each category here.

(39) L.283-285: presumably readers can see this directly in a table with the extracted data?

Our data and code can be accessed with the following link: https://doi.org/10.5061/dryad.q83bk3jnk. We believe the data are too large to include as a table in the main text and are not essential in understanding the paper. Though we do believe all readers should have access to this information if they wish and so is publicly available.

(40) L.293: there does not seem to be a table that lists the included studies and effect sizes. It is not uncommon to find major errors in such tables when one is familiar with the literature, and absence of this information impedes a complete assessment of the manuscript.

We supplied a link to our full dataset and the code we used in Dryad with our submitted manuscript. We were also asked to supply our data during the review process and we again supplied a link to our dataset and code, along with a folder containing the data and code itself. We received confirmation that the reviewers had been given our data and code. We support open science and it was our intention that our dataset should be fully available to reviewers and readers. We believe the data are too large to include as a table in the main text and are not essential in understanding the paper. Our data and code are at https://doi.org/10.5061/dryad.q83bk3jnk.

(41) L.293: from how many species?

We have added this detail.

(42) L.296, "longevity": this is a tricky concept, not usually reported in the studies you used, so please describe in detail what data you used.

We have removed longevity as we did not use this data in our current version of the manuscript.

(43) L. 298: again: where can I see this information?

Our data and code can be accessed with the following link: https://doi.org/10.5061/dryad.q83bk3jnk. We did supply this information when we submitted our manuscript and again during the review process but we believe this was not passed onto the reviewers.

(44) L. 304, "we used raw data": I assume that for the majority of papers the raw data were not available, so please explain how you dealt with this. Or perhaps this applies to a selection of the studies only? Perhaps the experimental studies?

By raw data, we mean the absolute value of offspring in the nest. We have changed the wording of this sentence and added detail about whether the absolute value of offspring was not present for brood manipulation studies (L393-397).

(45) L.304: When I remember correctly, Santos and Nakagawa examined effects of reducing and enlarging brood size separately, which is of importance because trade-off curves are unlikely to be linear and whether they are or not has major effects on the optimization process. But perhaps you tackled this in another way? I will read on.....

You are correct that Santos & Nakagawa compared brood increases and reductions to control separately. Note that this only partially accounts non-linearity and it does not take into account the severity of the change in brood size. By using a logistic regression of absolute clutch size, as we have done, we are able to directly compare brood manipulations with experimental studies. Please see Supplementary Methods lines 11-12, where we have added additional detail as to why our approach is beneficial in this analysis.

(46) L.319: what are you referring to exactly with "for each clutch size transformation"?

We refer to the raw, standardised and proportional clutch size transformations. We have added detail here to be more clear.

(47) L.319: is there a cost of survival? Perhaps you mean 'survival cost'? This would be appropriate for the experimental data, but not for the observational data, where the survival variation may be causally unrelated to the brood size variation, even if there is a correlation.

We have changed “cost of survival” to “effect of parental survival”. We only intend to imply causality for the experimental studies. For observational studies we do not suggest that increasing clutch size is causal for increasing survival, only correlative (and hence we use the phrase “quality”).

(48) L.320: please replace "parental effort" with something like 'experimental change in brood size'.

We have changed “parental effort” to “reproductive effort”

(49) L.321: due to failure of one or more eggs to hatch, and mortality very early in life, before brood sizes are manipulated, it is not likely that say an enlargement of brood size by 1 chick can be equated to the mean clutch size +1 egg / check. For example, in the Wytham great tit study, as re-analysed by Richard Pettifor, a 'brood size manipulation' of unmanipulated birds is approximately -1, being the number of eggs / chicks lost between laying and the time of brood size manipulation. Would this affect your comparisons?

Though we agree these are important factors in determining what a clutch/brood size actually is for a given individual/pair, as this can vary from egg laying to fledging. We do not believe that accounting for this (if it was possible to do so) would significantly affect our conclusions, as observational studies are comparable in the fact that these birds would also likely see early life mortality of their offspring. It is also possibly the case that parents already factor in this loss, and so a brood manipulation still changes the parental care effort an individual has to incur.

(50) L.332: instead of "adjusted" perhaps say 'mean centred'?

We have implemented this suggestion.

(51) L.345: this statement surprised me, but is difficult to verify because I could not locate a list of the included studies. However, to my best knowledge, most studies reporting brood size manipulation effects on parental survival had this as their main focus, in contrast to your statement.

Our data and code can be accessed with the following link: https://doi.org/10.5061/dryad.q83bk3jnk. We did supply this information when we submitted our manuscript and again during the review process but we believe this was not passed onto the reviewers by the journal, although supplied by us on several occasions. We regret that the reviewer was impeded by this unfortunate communication failure, but we did our best to make the data available to the reviewers during the initial review process.

(52) L.361-362: this seems a realistic approach from an evolutionary perspective, but we know from the jackdaw study by Boonekamp that the survival effect of brood size manipulation in a single year is very different from the survival effect of manipulating as in your model, i.e. every year of an individual's life the same manipulation. For very short-lived species this possibly does not make much difference, but for somewhat longer-lived species this could perhaps strongly affect your results. This should be discussed, and perhaps also explored in your simulations?

Note that the Boonekamp study does not separate whether the survival effects are additive or

multiplicative. As such, we do not know whether the survival effects for a single year manipulation are just small and hard to detect, or whether the survival effects are multiplicative. Our simulations assumed that the brood enlargement occurred every year throughout their lives. We have added some text to the discussion on the point you raise.

(53) L.360: what is "lifetime reproductive fitness"? Is this different from just "fitness"?

We have changed “lifetime reproductive fitness” to “lifetime reproductive output”.

(54) L.363: when you are interested in optimal clutch size, why not also explore effects of reducing clutch size?

As we find that a reduction in clutch size leads to a reduction in survival (for experimental studies), we already know that these individuals would have a reduced fitness return compared to reproducing at their normal level, and so we would not learn anything from adding this into our simulations. The interest in using clutch size enlargements is to find out why an individual does not produce more offspring than it does, and the answer is that it would not have a fitness benefit (unless its clutch size and survival rate combination is out of the bounds of that observable in the wild).

(55) Fig.1 - using 'parental effort' in the y-axis label is misleading, suggest to replace with e.g. "clutch or brood size". Using "clutch size" in the title is another issue, as the experimental studies typically changed the number of young rather than the number of eggs.

We have updated the figure axes to say “clutch size” rather than “parental effort”. Please see response to comment 35 where we explain our use of the term “clutch size” throughout this manuscript.

(56) L.93 - 108: I appreciate the analysis in Table 1, in particular the fact that you present different ways of expressing the manipulation. However, in addition, I would like to see the results of an analysis treating the manipulations as factor, i.e. without considering the scale of the manipulation. This serves two purposes. Firstly, I believe it is in the interest of the field that you include a detailed comparison with the results of Santos & Nakagawa's analysis of what I expect to be largely the same data (manipulation studies only - for this purpose I would also like to see a comparison of effect size between the sexes). Secondly, there are (at least) two levels of meta-analysis, namely quantifying an overall effect size, and testing variables that potentially explain variation in effect size. You are here sort of combining the two levels of analysis, but including the first level also would give much more insight in the data set.

Our main intention here was to improve on how the same hypothesis was approached by Santos & Nakagawa. We did this by improving our analysis (on a by “egg” basis) and by adding additional studies (i.e. more data). In this process mistakes are corrected (as we re-extracted all data, and did not copy anything across from their dataset – which was used simply to ensure we found the same papers); more recent data were also added, including studies missed by Santos & Nakagawa. This means that the comparison with Santos & Nakagawa becomes somewhat irrelevant, apart from maybe technical reasons, i.e. pointing out mistakes or limitations in certain approaches. We would not be able to pinpoint these problems clearly without considering the whole dataset, yet Santos & Nakagawa only had a small subset of the data that were available to us. In short, meta-analysis is an iterative process and similar questions are inevitably analysed multiple times and updated. This follows basic meta-analytic concepts and Cochrane principles. Except where there is a huge flaw in a prior dataset or approach (like we sometimes found and highlighted in our own work, e.g. Simons, Koch, Verhulst 2013, Aging Cell), in itself a comparison of the kind the reviewer suggests distracts from the biology. With the dataset being made available others can make these comparisons, if required. On the sex difference, we provide a comparison of effect sizes separated between both sexes and mixed sex in Table S2 and Figure S1.

(57) L.93 - 108: a thing that does not become clear from this section is whether experimentally reducing brood size affects parental survival similarly (in absolute terms) as enlarging brood size. Whether these effects are symmetric is biologically important, for example because of its effect on clutch size optimization. In the text you are specific about the effects of increasing brood size, but the effect you find could in theory be due entirely to brood size reduction.

We have added detail to make it clear that a brood reduction is simply the opposite trend. We use linear relationships because they serve a good approximation of the trend and provide a more rigorous test for an underlying relationship than would fitting nonlinear models. For many datasets there is not a range of chicks added for which a non-linear relationship could be estimated. The question also remains of what the shape of this non-linear relationship should be and is hard to determine a priori.

We have added some discussion on this to our manuscript (L278-282), in response to an earlier comment.

(58) L.103-107: this is perhaps better deferred to the discussion, because other potential explanations should also be considered. For example, there have been studies suggesting that small birds were provisioning their brood full time already, and hence had no scope to increase provisioning effort when brood size was experimentally increased.

We agree this is a discussion point but we believe it also provides an important context for why we ran our simulations, and so we believe this is best kept brief but in place. We agree the example you give is relevant but believe this argument is already contained in this section. See line 121-123 “...suggesting that costs to survival were only observed when a species was pushed beyond its natural limits”.

(59) L.103-107: this discussion sort of assumes that the results in Table 1 differ between the different ways that the clutch/brood size variation is expressed. Is there any statistical support for this assumption?

We are unsure of what the reviewer means here exactly. Note that in each of the clutch size transformations, experimental and observational effect sizes are significantly opposite. For the proportional clutch size transformation, experimental and observation studies are both separately significantly different from 0.

(60) L.104: at this point, I would like to have better insight into the data set. Specifically, a scatter plot showing the manipulation magnitude (raw) plotted against control brood size would be useful.

Our data and code can be accessed with the following link: https://doi.org/10.5061/dryad.q83bk3jnk. We did supply this information when we submitted our manuscript and again during the review process but we believe this was not passed onto the reviewers by the journal.

Thank you for this suggestion: this is a useful suggestion also to illustrate how manipulations are relatively stronger for species with smaller clutches, in line with our interpretation of the result presented in Figure 2. We have added Figure S1 which shows the strength of manipulation compared to the species average.

(61) L. 107: this seems a bold statement - surely you can test directly whether effect size becomes disproportionally stronger when manipulations are outside the natural range, for example by including this characterization as a factor in the models in Table 1.

It is hard to define exactly what the natural range is here, so it is not easy to factorise objectively, which is why we chose not to do this. However, it is clear that for species with small clutches the manipulation itself is often outside the natural range. Thank you for your suggestion to include a figure for this as it is clear manipulations are stronger in species with smaller clutches. We attribute this to species being forced outside their natural range. We consider our wording makes it clear that this is our interpretation of our findings and we therefore do not think this is a bold statement, especially as it fits with how we interpret our later simulations.

(62) Fig.3, legend: the term 'node support' does not mean much to me, please explain.

Node support is a value given in phylogenetic trees to dictate the confidence of a branch. In this case, values are given as a percentage and so can translate to how many times out of 100 the estimate of the phylogeny gives the same branching. Our values are low, as we have relatively few species in our meta-analysis.

(63) Fig.3: it would be informative when you indicate in this figure whether the species contributed to the experimental or the observational data set or both.

We have added into Fig 3 whether the species was observational, experimental or both.

(64) L.139: the p-value refers to the interaction between species clutch size and treatment (observational vs. experimental), but it appears that no evidence is presented for the correlation being significant in either observational or experimental studies.

We agree that our reporting of the effect size could be misinterpreted and have added detail here. The statistic provided describes the slopes are significantly different between observational and experimental, implying there are differences between the slopes of small and large clutch-laying species.

(65) L.140: I am wondering to what extent these correlations, which are potentially interesting, are driven by the fact that species average clutch size was also used when expressing the manipulation effect. In other words, to what extent is the estimate on the Y-axis independent from the clutch size on the X-axis? Showing that the result is the same when using survival effect sizes per manipulation category would considerably improve confidence in this finding.

We are unsure what the reviewer means by “per manipulation category”. Please also note that we have used a logistic regression to calculate our effect sizes of survival, given a unit increase in reproductive effort. So, for example, if a population contained birds that lay 2,3 or 4 eggs, provided that the number of birds which survived and died in each category did not change, if we changed the number of eggs raised to 10,11 or 12, respectively, then our effect size would be the same. In this way, our effect sizes are independent of the species’ average clutch size.

(66) L.145: when I remember correctly, Santos & Nakagawa considered brood size reduction and enlargement separately. Can this explain the contrasting result? Please discuss.

You are correct, in that Santos & Nakagawa compared reductions and enlargements to controls separately. However, we found some mistakes in the data extracted by Santos & Nakagawa that we believe explain the differences in our results for sex-specific effect sizes. We do not feel that highlighting these mistakes in the main text is fair, useful or scientifically relevant, as our approach is to improve the test of the hypothesis.

(67) L.158-159: looking at table S2 it seems to me you have a whole range of estimates. In any case, there is something to be said for taking the estimates for females because it is my impression (and experience) that clutch size variation in most species is a sex-linked trait, in that clutch size tends to be repeatable among females but not among males.

We agree that, in many cases, the female is the one that ultimately decides on the number of chicks produced. We did also consider using female effect sizes only, however, we decided against this for the following reasons: (1) many of the species used in our meta-analysis exhibit biparental care, as is the case for many seabirds, and so using females only would bias our results towards species with lower male investment; in our case this would bias the results towards passerine species. (2) it has also been shown that, as females in some species are operating at their maximum of parental care investment, it is the males who are able to adjust their workload to care for extra offspring. (3) we are ultimately looking at how many offspring the breeding adults should produce, given the effort it costs to raise them, and so even if the female chooses a clutch size completely independently of the male, it is still the effort of both parents combined that determines whether the parents gain an overall fitness benefit from laying extra eggs. (4) some studies did not clearly specify male or female parental survival and we would not want to reduce our dataset further.

(68) L.158-168: please explain how you incorporated brood size effects on the fitness prospects of offspring, given that it is a very robust finding of brood size manipulation studies that this affects offspring growth and survival.

We would argue this is near-on impossible to incorporate into our simulations. It is unrealistic to suggest that incorporating offspring growth into our simulations would add insight, as a change in offspring number rarely affects all offspring in the nest equally and there can even be quite stark differences; for example, this will be most evident in species that produce sacrificial offspring. This effect will be further confounded by catch-up growth, for example, and so it is likely that increased sibling competition from added chicks alters offspring growth trajectories, rather than absolute growth as the reviewer suggests. There are mixed results in the literature on the effect of altering clutch size on offspring survival, with an increased clutch size through manipulation often increasing the number of recruits from a nest. It would be interesting, however, to explore this further using estimates from the literature, but this is beyond our current scope, and would in our initial intuition not be very accurate. It would be interesting to explore how big the effect on offspring should be to constrain effect size strongly. Such work would be more theoretical. The point of our simple fitness projections here is to aid interpretation of the quantitative effect size we estimated.

(69) L.163: while I can understand that you select the estimate of -0.05 for computational reasons, it has enormous confidence intervals that also include zero. This seems problematic to me. However, in the simulations, you also examined the results of selecting -0.15, which is close to the lower end of the 95% C.I., which seems worth mentioning here already.

Thank you for this suggestion. Yes, indeed, our range was chosen based on the CI, and we have now made this explicit in the manuscript.

(70) L.210: defined in this way, in my world this is not what is generally taken to be a selection differential. Is what you show not simply scaled lifetime reproductive success?

As far as we are aware, a selection differential is the relative change between a given group and the population mean, which is what we have done here. We appreciate this is a slightly unusual context in which to place this, but it is more logical to consider the individuals who produce more offspring as carrying a potential mutation for higher productivity. However, we believe that “selection differential” is the best terminology for the statistic we present. We also detail in our methodology how we calculate this. We have adjusted this sentence to be more explicit about what we mean by selection differential.

(71) L.177-180: is this not so because these parameter values are closest to the data you based your estimates on, which yielded a low estimate and hence you see that here also?

We are unsure of what exactly the reviewer means here. The effect sizes for our exemplar species were predicted from each combination of clutch size and survival rate. Note that we used a range of effect sizes, higher than that estimated in our meta-analysis, to explore a large parameter space and that these same conclusions still hold.

(72) L.191-194: these statements are problematic, because based on the assumption that an increase in brood size does not impact the fitness prospects of the offspring, and we know this assumption to be false.

Though we appreciate that some cost is often absorbed by the offspring themselves, we are unaware of any evidence that these costs are substantial and large enough to drive within-species variation in reproductive effort, though for some specific species this may be the case. However, in terms of explaining a generalisable, across-species trend, the fitness costs incurred by a reduction in offspring quality are unlikely to be significantly larger than the survival costs to reproduce. We also find it highly unlikely the cost to fitness incurred by a reduction in offspring quality is large enough to counter-balance the effect of parental quality that we find in our observational studies. We do also discuss other costs in our discussion.

(73) L.205: here and in other places it would be useful to be more explicit on whether in your discussion you are referring to observational or experimental variation.

We have added this detail to our manuscript. Do note that many of our conclusions are drawn by the combination of results of experimental and observational studies. We believe the addition of Figure 5 makes this more clear to the reader.

(74) L.225: this may be true (at least, when we overlook the misuse of the word 'quality' here), but I would expect some nuance here to reflect that there is no surprise at all in this result as this pattern is generally recognized in the literature and has been the (empirical) basis for the often-repeated explanation of why experiments are required to demonstrate trade-offs. On a more quantitative level, it is worth mentioning the paper of Vedder & Bouwhuis (2017, Oikos) that essentially shows the same thing, i.e. a positive association between reproductive output and parental survival.

We have added some discussion on this point, including adding the citation mentioned. However, we would like to highlight that our results demonstrate that brood manipulations are not necessarily a good test of trade-offs, as they fail to recognise that individuals differ in their underlying quality. Though we agree that this result should not necessarily be a surprising one, we have also not found it to be the case that differences in individual quality are accepted as the reason that intra-specific clutch size is maintained – in fact, we find that it is most commonly argued that when costs of reproduction are not identifiedit is concluded that the costs must be elsewhere – yet we cannot find conclusive evidence that the costs of reproduction (wherever they lie) are driving intra-specific variation in reproductive effort. Furthermore, some studies in our dataset have reported negative correlations between reproductive effort and survival (see observational studies, Figure 1).

(75) L.225-226: perhaps present this definition when you first use the term.

We have added more detail to where we first use and define this term to improve clarity (L57-58).

(76) L.227-228, "currently unknown": this statement surprised me, given that there is a plethora of studies showing within-population variation in clutch size to depend on environmental conditions, in particular the rate at which food can be gathered.

We mean to question that if an individual is “high quality”, why is it not selected for? We have rephrased, to improve clarity.

(77) L.231: this seems no more than a special case of the environmental effect you mention above.

We think this is a relevant special case, as it constitutes within-individual variation in reproduction that is mistaken for between-individual variation. This is a common problem in our field, that we feel needs adressing. We only have between-individual variation here in our study on quality, and by highlighting this we show that there might not be any variation between individuals, but this could come about fully (doubtful) or partly (perhaps likely) due to terminal effects.

(78) L235-236: but apparently depending on how experimental and natural variation was expressed? Please specify here.

We are not sure what results the reviewer is referring to here, as we found the same effect (smaller clutch laying species are more severely affected by a change in clutch size) for both clutch size expressed as raw clutch size and standardised clutch size.

(79) L.237: the concept of 'limits' is not very productive here, and it conflicts with the optimality approach you apply elsewhere. What you are saying here can also be interpreted as there being a non-linear relationship between brood size manipulation and parental survival, but you do not actually test for that. A way to do this would be to treat brood size reduction and enlargement separately. Trade-off curves are not generally expected to be linear, so this would also make more sense biologically than your current approach.

We have replaced “limits” with “optima”. We believe our current approach of treating clutch size as a continuous variable, regardless of manipulation direction, is the best approach, as it allows us to directly compare with observational studies and between species that use different manipulations (now nicely illustrated by the reviewer’s suggested Figure S1). Also note that transforming clutch size to a proportion of the mean allows us to account for the severity in change in clutch size. We also do not believe that treating reductions and enlargements separately accounts for non-linearity, as either we are separating this into two linear relationships (one for enlargements and one for reductions) or we compare all enlargements/reductions to the control, as in Santos & Nakagawa 2012, which does not take into account the severity of the increase, which we would argue is worse for accounting for non-linearity. Furthermore, in the cases where the manipulation involved one offspring only, we also cannot account for non-linearity.

(80) L.239: assuming birds are on average able to optimize their clutch size, one could argue that any manipulation, large or small, on average forces birds to raise a number of offspring that deviates from their natural optimum. At this point, it would be interesting to discuss in some detail studies with manipulation designs that included different levels of brood size reduction/enlargement.

We agree with the reviewer that any manipulation is changing an individual’sclutch size away from its own individual optima, which we have argued also means brood manipulations are not necessarily a good test of whether a trade-off occurs in the wild (naturally), as there could be interactions with quality – we have now edited to explicitly state this (L299-300).

(81) L.242-244: when you choose to maintain this statement, please add something along the lines of "assuming there is no trade-off between number and quality of offspring".

As explained above, though we agree that the offspring may incur some of the cost themselves, we are not aware of any evidence suggesting this trade-off is also large enough to drive intra-specific variation in clutch size across species. Furthermore, in the context here, the trade-off between number and quality of offspring would not change our conclusion – that the fitness benefit of raising more offspring is offset by the cost on survival. We have added detail on the costs incurred by offspring earlier in our discussion (L309-315). The addition of Figure 5 should help interpret these data.

(82) L.253: instead of reference 30 the paper by Tinbergen et al in Behaviour (1990) seems more appropriate.

We believe our current citation is relevant here but we have also added the Tinbergen et al (1990) citation.

(83) L.253-254: such trade-offs may perfectly explain variation in reproductive effort within species if we were able to estimate cost-benefit relations for individuals. In fact, reference 29 goes some way to achieve this, by explaining seasonal variation in reproductive effort.

We are unaware of any quantitative evidence that any combination of trade-offs explains intra-specific variation in reproductive effort, especially as a general across-species trend.

(84) L.255: how does one demonstrate "between species life-history trade-offs"? The 'trade-off' between reproductive rate and survival we observe between species is not necessarily causal, and hence may not really be a trade-off but due to other factors - demonstrating causality requires some form of experimental manipulation.

Between-species trade-offs are well established in the field, stemming from GC Williams’ seminal paper in 1966, and for example in r/K selection theory. It is possible to move from these correlations to testing for causation, and this is happening currently by introducing transgenes (genes from other species) that promote longevity into shorter-lived species (e.g., naked-mole rat genes into mice). As yet it is unclear what the effects on reproduction are.

(85) L.256: it is quite a big claim that this is a novel suggestion. In fact, it is a general finding in evolutionary theory that fitness landscapes tend to be rather flat at equilibrium.

It is important to note here that we simulate the effect size found, and hence this is the novel suggestion, that because the resulting fitness landscape is relatively flat there is no directional selection observed. We did not intend to suggest our interpretation of flat fitness landscapes is novel. We have changed the phrasing of this sentence to avoid misinterpretation.

(86) L.259: why bring up physiological 'costs' here, given that you focus on fitness costs? Do you perhaps mean fitness costs instead of physiological costs? Furthermore, here and in the remainder of this paragraph it would be useful to be more specific on whether you are considering natural or experimental variation.

The cost of survival is a physiological cost incurred by the reduction of self-maintenance as a result of lower resource allocation. This is one arm of fitness; we feel it would be confusing here to talk about costs to fitness, as we do not assess costs to future reproduction (which formed the large part of the critique offered by the reviewer). We would like to highlight that the aim of this manuscript was to separate costs of reproduction from the effects of quality, and this is why we have observational and experimental studies in one analysis, rather than separately. Our conclusion that we have found no evidence that the survival cost to reproduce drives within-species variation in clutch size comes both from the positive correlation found in the observational studies and our negligible fitness return estimates in our simulations. We therefore, do not believe it is helpful to separate observational and experimental conclusions throughout our manuscript, as the point is that they are inherently linked. We hope that with the addition of Figure 5 that this is more clear.

(87) L.262: The finding that naturally more productive individuals tend to also survive better one could say is by definition explained by variation in 'quality', how else would you define quality?

We agree, and hence we believe quality is a good term to describe individuals who perform highly in two different traits. Note that we also say the lack of evidence that trade-offs drive intra-specific variation in clutch size also potentially suggests an alternative theory, including intra-specific variation driven by differences in individual quality.

Supplementary information

(88) Table S1: please provide details on how the treatment was coded - this information is needed to derive the estimates of the clutch size effect for the treatments separately.

We have added this detail.

(89) Table S2: please report the number of effect sizes included in each of these models.

We have added this detail.

(90) Table S4: references are not given. Mentioning species here would be useful. For example, Ashcroft (1979) studied puffins, which lay a single egg, making me wonder what is meant when mentioning "No clutch or brood size given" as the reason for exclusion. A few more words to explain why specific studies were excluded would be useful. For example, what does "Clutch size groups too large" mean? It surprises me that studies are excluded because "No standard deviation reported for survival" - as the exact distribution is known when sample size and proportion of survivors is known.

We have updated this table for more clarity.

(91) Fig.S1: please plot different panels with the same scale (separately for observational and experimental studies). You could add the individual data points to these plots - or at least indicate the sample size for the different categories (female, male, mixed).

We have scaled all panels to have the same y axis and added sample sizes to the figure legend.

(92) Fig.S3: please provide separate plots for experimental and observational studies, as it seems entirely plausible that the risk of publication bias is larger for observational studies - in particular those that did not also include a brood size manipulation. At the same time, one can wonder what a potential publication bias among observational studies would represent, given that apparently you did not attempt to collect all studies that reported the relevant information.

We have coloured the points for experimental and observational studies. Note that a study is an independent effect size and, therefore, does not indicate whether multiple data (i.e., both experimental and observational studies) came from the same paper. As we detail in the paper and above in our reviewer responses, we searched for observational studies from species used in the experimental studies to allow direct comparison between observational and experimental datasets.

Reviewer #2 (Recommendations For The Authors):

I strongly recommend improving the theoretical component of the analysis by providing a solid theoretical framework before, from it, drawing conclusions.

This, at a minimum, requires a statistical model and most importantly a mechanistic model describing the assumed relationships.

We thank the reviewer for highlighting that our aims and methodology are unclear in places. We have added detail to our model and simulation descriptions and have improved the description of our rationale. We also feel the failure of the journal to provide code and data to the reviewers has not helped their appreciation of our methodology and use of data.

Because the field uses the same wording for different concepts and different wording for the same concept, a glossary is also necessary.

We thank the reviewer for raising this issue. During the revision of this manuscript, we have simplified our terminology or given a definition, and we believe this is sufficient for readers to understand our terminology.

Reviewer #3 (Recommendations For The Authors):

• The files containing information of data extracted from each study were not available so it has not been possible to check how any of the points raised above apply to the species included in the study. The ms should include this file on the Supp. Info as is standard good practice for a comparative analysis.

We supplied a link to our full dataset and the code we used in Dryad with our submitted manuscript. We were also asked to supply our data during the review process and we again supplied a link to our dataset and code, along with a folder containing the data and code itself. We received confirmation that the reviewers had been given our data and code. We support open science and it was our intention that our dataset should be fully available to reviewers and readers. We believe the data is too large to include as a table in the main text and is not essential in understanding the paper. Our data and code are at https://doi.org/10.5061/dryad.q83bk3jnk.

• For clarity, refer to 'the effect size of clutch size on survival" rather than simply "effect size". Figures 1 and 2 require cross-referencing with the main text to understand the y-axis.

We have added detail to the figure legend to increase the interpretability of the figures.

• Silhouettes in Figure 3 (or photos) would help readers without ornithological expertise to understand the taxonomic range of the species included in the analyses.

We have added silhouettes into Figure 3.

• Throughout the discussion: superscripts shouldn't be treated as words in a sentence so please add authors' names where appropriate.

We have added author names and dates where required.

eLife assessment

This valuable paper presents a new protocol for quantifying tRNA aminoacylation levels by deep sequencing. The improved methods for discrimination of aminoacyl-tRNAs from non-acylated tRNAs, more efficient splint-assisted ligation to modify the tRNAs' ends for the following RT-PCR reaction, along with the use of an error-tolerating mapping algorithm to map the tRNA sequencing reads provide new tools for anyone interested in tRNA concentrations and functional states in different cells and organisms. The results and conclusions are solid, with well-designed tests to optimize the protocol under different conditions.

Reviewer #1 (Public Review):

The manuscript of Davidsen and Sullivan describes an improved tRNA-seq protocol to determine aminoacyl-tRNA levels. The improvements include: (i) optimizing the Whitfeld or oxidation reaction to select aminoacyl-tRNAs from oxidation-sensitive non-acylated tRNAs; (ii) using a splint-assisted ligation to modify the tRNAs' ends for the following RT-PCR reaction; (iii) using an error-tolerating mapping algorithm to map the tRNA sequencing reads that contain mismatches at modified nucleotides.

The revised manuscript of Davidsen and Sullivan has addressed my concerns in the previous review. The authors performed a end-to-end comparison, which I requested - Fig. 2 and Fig S2. This is exactly what I meant, albeit the differences in each method to perform the comparison of the detectability. The manuscript is a strong methodological improvement of the tRNA quantification protocols!

Reviewer #2 (Public Review):

Davidsen and Sullivan present an improved method for quantifying tRNA aminoacylation levels by deep sequencing. By combining recent advances in tRNA sequencing with lysine-based chemistry that is more gentle on RNA, splint oligo-based adapter ligation, and full alignment of tRNA reads, they generate an interesting new protocol. The lab protocol is complemented by a software tool that is openly available on Github. Many of the points highlighted in this protocol are not new, but have been used in recent protocols such as Behrens et al. (2021) or McGlincy and Ingolia (2017). Nevertheless, a strength of this study is that the authors carefully test different conditions to optimize their protocol using a set of well-designed controls.

The conclusions of the manuscript appear to be well supported by the data presented. However, the lack of benchmarking relative to other methods remains as a key criticism also after this revision.

(1) The manuscript reports a different method to measure aminoacylation of tRNA. The main point that remains unsatisfactory is a better benchmarking of such aminoacylation measurements against the state of the art. In the current form of the revised manuscript it is not possible to estimate how much the results of this new protocol differ from alternative methods and in particular from Behrens et al. (2021). Here it will be helpful to perform experiments with samples similar to those (like HEK cells or yeast cells) used in the mim-tRNAseq study and not with H1299 cells.

The claim that a comparison to every published protocol is not feasible is not a good argument for not performing any benchmarking experiments. Such benchmarking experiments are not meant to define the ground truth but are needed to estimate the difference in the outcome of different protocols. I agree with the authors that precision/reproducibility is essential when developing a new protocol. But the analysis and comparison should not stop there.

(2) The reported protocol can not only be used for quantification of tRNA aminoacylation but it can also be used for tRNA quantification and analysis of tRNA modifications. It will increase the impact of this study if the authors benchmark the outcomes of their protocol with other tRNA sequencing protocols with samples similar to these papers, which will be important for certain research teams that are unlikely to implement two different tRNA sequencing methods.

The authors decided not to perform further experiments in cell lines or mutants that allow a comparison to other published methods. In my opinion this limits the impact of the work. But as a reviewer I can only make recommendations. It is the authors decision to take those or not.

Author response:

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

eLife assessment

This valuable paper presents a new protocol for quantifying tRNA aminoacylation levels by deep sequencing. The improved methods for discrimination of aminoacyl-tRNAs from non-acylated tRNAs, more efficient splint-assisted ligation to modify the tRNAs' ends for the following RT-PCR reaction, and the use of an error-tolerating mapping algorithm to map the tRNA sequencing reads provide new tools for anyone interested in tRNA concentrations and functional states in different cells and organisms. The results and conclusions are solid with well-designed tests to optimize the protocol under different conditions.

Public Reviews:

We thank both reviewers for suggestions, feedback and improvements. We address these pointwise below.

Reviewer #1 (Public Review):

Summary:

The manuscript of Davidsen and Sullivan describes an improved tRNA-seq protocol to determine aminoacyl-tRNA levels. The improvements include: (i) optimizing the Whitfeld or oxidation reaction to select aminoacyl-tRNAs from oxidation-sensitive non-acylated tRNAs; (ii) using a splint-assisted ligation to modify the tRNAs' ends for the following RT-PCR reaction; (iii) using an error-tolerating mapping algorithm to map the tRNA sequencing reads that contain mismatches at modified nucleotides.

Strengths:

The two steps, the oxidation, and the splint-assisted ligation are yield-diminishing steps, thus the protocol of Davidsen and Sullivan is an important improvement of the current protocols to enhance the quantification of aminocyl-tRNAs.

Weaknesses:

The oxidation and the selection of aminoacyl-tRNA is the first step in all protocols. Thereafter they differ on whether blunt ligation, hairpin (DM-tRNA-seq, YAMAT-seq, QuantM-seq, mim tRNA-seq, LOTTE tRNA-seq), or splint ligation is used and finally what detection method is applied (i-tRAP, tRNA microarrays). What is the correlation to those alternative approaches (e.g. i-tRAP (PMID 36283829), tRNA microarrays (PMID: 31263264) etc.)? What is the correlation with other approaches with which this improved protocol shares some steps (DM-tRNA-seq, mim-tRNA-seq)?

We appreciate the fair assessment and fully agree that our work would benefit from a large comparison between all known tRNA-seq methods. We did directly compare many elements of our method to those of other methods (e.g. ligation efficiency and barcode bias); however, as noted by the reviewer we did not perform a direct end-to-end comparison with all other methods. An ideal comparison would require running several different sample conditions and technical replicates through our protocol and repeating the process across a half dozen or so other methods as they are described. Unfortunately, this approach is unlikely to be feasible since each method uses different oligos, reagents and kits, and all would have to be acquired at substantial cost. Some methods also rely on other detection methods such as microarrays, qPCR, or Illumina sequencing, which would also make this goal all the more onerous. There are also different pipelines for data processing that, in some instances, make the final results hard to compare. In short, this would be a monumental and expensive task to do comprehensively. We also worry that, even if these experiments were conducted such that some variables were concluded to be superior, they could still be challengeable based on perceived or actual protocol differences from the prior art. In summary, we think that an overall comparison with each method would be ideal, but practical concerns limit us to optimizing and comparing the variables that we found to be most prone to introducing bias in the results.

For methods that measure tRNA expression levels (DM-tRNA-seq, YAMAT-seq, QuantM-seq, mim-tRNA-seq, LOTTE tRNA-seq etc.) there are some fundamental problems regarding absolute quantification using NGS that preclude simple comparisons. These problems are well known in the field of microRNA (Fuchs et al. (2012) [PMID: 25942392]) and arise due to several factors introduced during processing steps such as purification, ligation, reverse transcription and amplification. With the lack a “true” quantitation benchmark it would be difficult to make quantitative claims from each.  Therefore, in our own work we benchmark tRNA expression levels for sample-to-sample reproducibility (i.e. precision) as further explained in the response to reviewer #2.

For comparison to methods that measure tRNA charge we did have an opportunity to compare our results with those of another study. To this end, we have added a figure comparing the baseline charge found using our method and the one used in Evans et al. (Revised manuscript Figure 2—figure supplement 9). This comparison finds broadly similar results for tRNA charge, including similar trends for a subset of Glu, Ser and Pro codons that are notable for their lowered basal tRNA charge.

Reviewer #2 (Public Review):

Davidsen and Sullivan present an improved method for quantifying tRNA aminoacylation levels by deep sequencing. By combining recent advances in tRNA sequencing with lysine-based chemistry that is more gentle on RNA, splint oligo-based adapter ligation, and full alignment of tRNA reads, they generate an interesting new protocol. The lab protocol is complemented by a software tool that is openly available on Github. Many of the points highlighted in this protocol are not new but have been used in recent protocols such as Behrens et al. (2021) or McGlincy and Ingolia (2017). Nevertheless, a strength of this study is that the authors carefully test different conditions to optimize their protocol using a set of well-designed controls.

The conclusions of the manuscript appear to be well supported by the data presented. However, there are a few points that need to be clarified.

We appreciate the acknowledgement of the strength of our aminoacylation controls and agree that our method is relying on many aspects of the mentioned prior work.  

(1) One point that remains unsatisfactory is a better benchmarking against the state of the art. It is currently impossible to estimate how much the results of this new protocol differ from alternative methods and in particular from Behrens et al. (2021). Here it will be helpful to perform experiments with samples similar to those used in the mim-tRNAseq study and not with H1299 cells.

We fully agree that more rigorous benchmarking would be desirable. As also noted in the response to reviewer #1, a full end-to-end comparison of methods would be ideal but would be onerous and expensive in practice, so we focused on optimizing the steps we found to be most prone to introducing bias in the data.

We agree that Behrens et al., (2021) has substantial methodological overlap with our work and was instrumental in our efforts; however, the focus of their manuscript was largely on quantification of tRNA abundance and modifications, rather than the tRNA charge. In fact, tRNA charge was only determined for yeast in that study. Quantifying the abundance of short RNAs using NGS is very difficult (Fuchs et al. (2012) [PMID: 25942392]) and will likely require the use of a mixture of tRNAs as spike-in references for normalization (Bissels et al. (2009) [PMID: 19861428]). In the case of Behrens et al. (2021), they did not use a spike-in tRNA reference, but instead correlated gene copy number with their measured tRNA abundance. They also compare to Northern blotting for two tRNA transcripts, showing a directionally similar result; however, no quantitative claims can be made measurement accuracy. Until a good method of normalizing tRNA quantification is found, we believe that sample-to-sample reproducibility (i.e. precision) is the most useful objective to optimize because this will allow detection of differential expression. Towards that end, we quantified the precision of our method (Figure 4 and its two supplementary figures) with associated statistics, which can be used to estimate the number of samples required to detect significance during differential expression analysis. For tRNA charge, quantification is easier, which is why we present statistics on both accuracy and precision. In this case we can better compare results across methods, and so we have added a comparison of our results to the charge quantification from Evans et al. (2017) (Figure 2—figure supplement 9).

(2) While the protocol aims to implement an improved method for quantification of tRNA aminoacylation, it can also be used for tRNA quantification and analysis of tRNA modifications. It will increase the impact of this study if the authors benchmark the outcomes of their protocol with other tRNA sequencing protocols with samples similar to these papers, which will be important for certain research teams that are unlikely to implement two different tRNA sequencing methods. Are there any possible adaptations that would allow the analysis of tRNA fragments?

The first part of this comment regarding comparison of methods is addressed in response to in the prior reviewer comment and in the response to reviewer 1. In the specific case of tRNA modifications, the issue is similar to abundance quantification in that a “true” reference of modified tRNA is likely necessary for proper quantification, alongside testing of each method simultaneously.

Regarding tRNA fragments, our method is not suitable for this use case. This is because our adapter ligation step depends on an intact tRNA structure with either CCA or CC overhang on the 3’-end and thus we almost exclusively get reads with CCA/CC ends and no reads from fragments. This specificity is good for increasing charge quantification accuracy but not good for the methods versatility. For a more versatile method we recommend Watkins et al. (2022) [PMID: 35513407].

(3) Like Behrens et al. (2021), Davidsen and Sullivan use TGIRT-III RT for their analyses. The enzyme is not currently available in a form suitable for tRNA-seq. It would be very helpful to test different new RT enzymes that are commercially available. The example of Maxima RT - Figure 2 Supp 6 - shows significantly lower performance than the presented TGIRT-III RT data. In lines 296-298, the authors mention improvements to the protocol by using ornithine. Why are these improvements not included?

We share similar concerns that the TGIRT-III enzyme is no longer commercially available. It became unavailable while we were preparing this manuscript, reflected by the fact that almost all our figures are made using this enzyme. Others have discovered this too and Lucas et al. (2023) [PMID: 37024678] tested several RT polymerases using TapeStation as a readout for readthrough. As they reported that Maxima has good performance, we decided to test it on a full run with replicates. The results are outlined in Figure 2—figure supplement 6 and for resubmission we have added a table to the appendix that compares the alignment statistics. Unfortunately, the readthrough of the Maxima polymerase on cytoplasmic tRNAs is not as high as for TGIRT-III; however, interestingly it seems to have better performance for mitochondrial tRNAs (Figure 2 – Figure Supplement 6). Regardless, in the initial paper submission we failed to evaluate whether this readthrough difference affected charge measurements. We have now fixed this by adding Figure 2—figure supplement 7, which shows that there are no differences in charge measurements TGIRT-III vs. Maxima. Not surprisingly, there are substantial differences between polymerases when looking at relative tRNA abundance (which affirms the discussion above related to the difficulty of tRNA abundance quantification); however, the high sample-to-sample reproducibility remains intact with either polymerase. An exhaustive search for better polymerases is warranted but falls outside the scope of our work.

Regarding the improvements suggested by us, using ornithine as a cleavage catalyst instead of lysine, we first learned about this possibility later and thus only want to make readers aware that other options exist. We have clarified the paragraph to make this clearer.

(4) A technical concern: The samples are purified multiple times using a specific RNA purification kit. Did the authors test different methods to purify the RNA and does this influence the result of the method?

In the past, we have relied exclusively on alcohol precipitation but during the development of this protocol we found it easier and more reproducible to use column-based purification when possible. However, as we have not made a direct comparison this remains anecdotal evidence. Nonetheless, to minimize any possible bias of column-based purification you will notice that we use columns with binding capacity 5x higher than the highest amount of RNA/DNA added to the column.

(5) The study would benefit from an explicit step-by-step protocol, including the choice of adapters that are shown to work best in the protocol.

This is a great point! We have included tables with all the oligos used (Supplementary file 1), a detailed step-by-step protocol with pictures of anticipated gel results (Supplementary file 2) and an overview of the RNA/DNA manipulations to make it clear where adapter sequences are located (Supplementary file 3). For the data processing we provide a comprehensive example in the Github repository. All this was included in our first submission of this manuscript (as well as on bioRxiv), but we suspect this was not readily accessible to the reviewers. We will make sure that these documents are going to be available through eLife and have emphasized their existence in the main text of the manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

To stratify this improvement a comparison to the most common methods should be made. For example, how do the results with the improved protocol with i-tRAP (PMID 36283829), tRNA microarrays (PMID: 31263264), or with the approaches the improved protocol shares with some other tRNA-seq approaches (DM-tRNA-seq, mim-tRNA-seq)?

Once again, we thank the reviewer for the good recommendations. The points about direct comparisons were discussed above.

Reviewer #2 (Recommendations For The Authors):

These are all great points; we address them below.

Minor points:

- Please use chemical conventions, e.g. for mcm5s2U and NaIO4 with superscript or subscript.

Fixed.

- Figure 2F: Glu GAA is only 82% charged; can this be due to mcm5s2U (Figure 3 supp 2) leading to a misalignment? What happens to Ser-NNN? Why is mitochondrial tRNA so much less charged?

Regarding the Glu-GAA charge at baseline, we do not think this is an artifact of the mcm5s2U modification as it would then also be expected for Gln-CAA and Lys-AAA. The same occurs in the charge data in Evans et al. (2017) and they use a very different alignment strategy. Lastly, the charge titration and half-life experiments show no evidence of inaccuracy/bias for Glu-GAA.

But the question remains – why is the charge of Glu-GAA so low? At this point our best guess is speculative. It may have something to do with the strong enrichment of Glu-GAA codons in the A site found by ribosome profiling on mouse embryonic stem cells (Ingolia et al. (2011) [PMID: 22056041]).

- Spell out "clvg" or "dphs" in the figure legend of Figure 2 and others. Similar for other abbreviations in figures. They are not always explained in the legends.

Fixed.

- Figure 3 supp 2: Please use U instead of T in the anticodons. The labels are a bit confusing. Please clearly align to the tick (also for Figure 3C).

Fixed.

- Line 220-223. Which RT enzyme was used for Figure 3 supp 2? Does it make a difference?

TGIRT-III was used. Only Figure 2—figure supplement 6 and Figure 2—figure supplement 7 (added for resubmission) show data with the Maxima polymerase. To address the second part of the question we have added a comparison between TGIRT-III and Maxima for mcm5s2U modification detection (Figure 3—figure supplement 3). Interestingly, there is a polymerase specific signature for mcm5s2U modifications; however, more work would be required to determine which polymerase is best suited for detection of this and other modifications.

- Figure 4 supp 1 and Figure 4 supp 2 change order.

Fixed.

Typos:

- Figure 1 and Figure 1-figure supplement 1: In the periodate the "-" is in a small box (at least in my PDF viewer). Can this box be removed?

- Line 175: duplicated verb.

- Line 348: "moved".

Thanks for catching these. They have now been fixed.

eLife assessment

This useful studying implicates TRPV4 as a mediator of sweat, potentially based on TRPV4's expression and function on sweat glands. The data and methods are solid, with some limitations in terms of the approach. Overall, the work lends new insight into the physiologic basis of sweating using data from mice and humans.

Joint Public Review:

In this study, Kashio et al examined the role of TRPV4 in regulating perspiration in mice. They find coexpression of TRPV4 with the chloride channel ANO1 and aquaporin 5, which implies possible coupling of heat sensing through TRPV4 to ion and water excretion through the latter channels. Calcium imaging of eccrine gland cells revealed that the TRPV4 agonist GSK101 activates these cells in WT mice, but not in TRPV4 KO. This effect is reduced with cold-stimulating menthol treatment. Temperature-dependent perspiration in mouse skin, either with passive heating or with ACh stimulation, was reduced in TRPV4 KO mice. Functional studies in mice - correlating the ability to climb a slippery slope to properly regulate skin moisture levels - reveal potential dysregulation of foot pad perspiration in TRPV4 KO mice, which had fewer successful climbing attempts. Lastly, a correlation of TRPV4 to hypohydrosis in humans was shown, as anhidrotic skin showed reduced levels of TRPV4 expression compared to normohidrotic or control skin.

Overall this is an interesting study on how TRPV4 regulates perspiration.

(1) The functional relationship between TRPV3 and ANO1 remains correlative.

(2) Littermate controls were not used, but TRPV4ko were backcrossed onto the WT strain.

(3) In general, the results support the authors' claims that TRPV4 activity is a necessary component of sweat gland secretion, which may have important implications for controlling perspiration; secretion from other glands where TRPV4 may be expressed remains a possibility given the lack of us of exocrine-specific knockouts.

Author response:

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

Reviewer #1 (Public Review):

(1) Measurement of secreted amylase could be seen as direct evidence of sweating, however, how to determine the causal relationship between climbing behavior and sweating? Friction force may also be reduced when there is too much fingertip moisture.

As the reviewer notes, measurement of secreted amylase can provide direct evidence of sweating, and we performed an iodine and starch reaction. Upon observing the involvement of TRPV4 in mouse foot pad perspiration, we then considered which type of behavioral analysis would be suitable to evaluate this perspiration. We agree with the reviewer’s point that friction force in the climbing test may be reduced by excessive sweating. However, we did not observe severe sweating in the absence of acetylcholine treatment. Accordingly, we interpreted that the increase in the climbing test failure rate for TRPV4KO mice could reflect the reduced friction force associated with the lack of TRPV4 activity.

(2) For the human skin immunostaining, did the author use the same TRPV4 antibody as used in the mouse staining? Did they validate the specificity of the antibody for the human TRPV4 channel? 

We used different antibodies for human and mouse samples. Since commercially available anti-TRPV4 antibodies do not work well with mouse samples, we generated our own anti-TRPV4 antibody and validated its specificity.

(3) In lines 116-117, the authors tried to determine "the functional interaction of TRPV4 and ANO1 is involved in temperature-dependent sweating", however, they only used the TRPV4 ko mice and did not show any evidence supporting the relationship between TRPV4 and ANO1. 

As the reviewer pointed out, based on the data presented in the original submission we cannot conclude that an interaction between TRPV4 and ANO1 is involved in perspiration. However, we think that the data for TRPV4KO mice presented in Figure 3 of the original version does indicate that TRPV4 is involved in perspiration. The finding that menthol and its related compounds, which inhibit the function of both TRPV4 and ANO1 (see our publication in Scientific Reports 7: 43132, 2017), blocked perspiration in both wild-type and TRPV4KO mice (original Figure 3C, D) indicates involvement of either TRPV4 or ANO1 in perspiration. In the revised version, we present results for additional iodine and starch reaction experiments using Ani9, a potent and specific ANO1 inhibitor. Ani9 drastically inhibited perspiration from mouse food pads both at 25 °C and 35 °C. Based on these collective results, we concluded that both TRPV4 and ANO1, likely acting as a complex, are involved in perspiration. We present the new data with Ani9 in the revised Figure 3E, F.

(4) Figure 3-4 is quite confusing. At 25˚C, no sweating difference was observed between TRPV4 and wt mice (Fig 3A-3D), suggesting both Ach-induced sweating and basal sweating are TRPV4-independent at 25˚C, however, the climbing test was done at 26-27 ˚C and the data showed a climbing deficit in TRPV4 ko mice. How to interpret the data is unclear. 

Thank you for raising this point. In the iodine and starch reaction experiment, we observed no significant reduction in perspiration in the absence of acetylcholine at 25 °C, which is the same condition as in the climbing test, whereas we detected less perspiration for TRPV4KO mice. In a trial using additional mice, we detected significantly less perspiration under control conditions without acetylcholine at 25 °C, which is consistent with the results of the climbing test. We have added this new data to the revised Figure 3A, B.

(5) Were there any gender differences associated with sweating in mice? In Figure 3, the mouse number for behavior tests should be at least 5. 

The TRPV4KO mice reproduced poorly and we were unable to obtain sufficient numbers of male and female mice to determine whether there were gender differences in sweating. However, according to the reviewer’s suggestion, and as mentioned above, we increased the number of experiments to obtain the results shown in the revised Figure 3. We did not a observe a significant difference in sweating with the larger sample size, which supports our conclusions.

(6) 8- to 21-week-old mice were used in the immunostaining, the time span is too long. 

Given the difficulty in obtaining sufficient numbers of TRPV4KO mice, we used a somewhat wider age distribution to obtain samples for immunostaining. However, we did not observe age-dependent differences in immunostaining. We reference this point in the revised manuscript.

(7) The authors used homozygous TRPV4 ko mice for all experiments. What are control mice? Are they littermates of the TRPV4 ko mice? 

We did not use littermates for our in vivo experiments because the TRPV4KO mice reproduced poorly and the litter sizes were small. However, we did backcross the KO mice to the commercially available wild-type mice more than ten times. As such, we expect that the wild-type and TRPV4KO mice will have similar genetic backgrounds. In addition, we have published multiple studies that have successfully used this method, which we think supports the reliability of our results for experiments involving mice.

Reviewer #2 (Public Review):

(1) The coexpression data needs additional controls. In the TRPV4 KO mice, there appears to be staining with the TRPV4 Ab in TRPV4 KO mice below the epidermis. This pattern appears similar to that of the location of the secretory coils of the sweat glands (Fig 1A). Is the co-staining the authors note later in Figure 1 also seen in TRPV4 KOs? This control should be shown, since the KO staining is not convincing that the Ab doesn't have off-target binding. 

We thank the reviewer for raising these concerns about immunostaining. As the reviewer notes, in the low power image the signals appeared to be weak and punctate signals were present in the basal region of glandular cells. Although we did not identify immunohistochemical conditions that produced no signal, tissue sections from WT mice stained with anti-TRPV4 antibody showed conspicuous apical signals for the glandular cells facing lumen. Meanwhile, TRPV4KO tissues showed no signals at the apical region of the glandular cells, where the TRPV4-ANO1 interaction is expected to occur. We confirmed no trace signals in the TRPV4KO tissues in the immunoblotting.

(2) Are there any other markers besides CGRP for dark cells in mice to support the conclusion that mouse secretory cells have clear cell and dark cell properties? 

We did not stain with other dark cell markers. Based on previous studies describing the differences between clear and dark cells in mouse eccrine glands, we think that dark and clear cells cannot be clearly discriminated, as we described in lines 93-96 of the Results. We identified secretory cells using CK8 and dark cells with CGRP, a marker of dark cells in human eccrine glands (Zancanaro et al. 1999 J Anat). Our result showed that CGRP immunostaining could not discriminate between clear and dark cells, which is consistent with a previous report showing that mouse secretory cells were assumed to be undifferentiated and primitive based on electron microscopic observation (Kurosumi et al. 1970 Arch Histol Jap).

(3) The authors utilize menthol (as a cooling stimulus) in several experiments. In the discussion, they interpret the effect of menthol as potentially disrupting TRPV4-ANO1 interactions independent of TRPM8. Yet, the role of TRPM8, such as in TRPM8 KO mice, is not evaluated in this study.

We performed the iodine and starch reaction experiments with TRPM8KO mice. In the TRPM8KO mice, the sweat spots did not differ from those seen for WT mice (p=0.63, t-test), and there was also a significant reduction in sweating with menthol treatment following acetylcholine stimulation that was similar to that seen for WT mice. These results would rule out the involvement of TRPM8 in a menthol-induced reduction in sweating. We have included this data in the revised Figure 3D.

(4) Along those lines, the authors suggest that menthol inhibits eccrine function, which might lead to a cooling sensation. But isn't the cooling sensation of sweating from evaporative cooling? In which case, inhibiting eccrine function may actually impair cooling sensations.

Menthol has a non-specific effect that activates TRPM8, TRPV3 and TRPA1, and inhibits TRPV1, TRPV4 and ANO1. Therefore, we did not carry out a climbing test with menthol in part because menthol-dependent TRPA1 activation decreased the propensity of the mice to climb. As the reviewer notes, TRPM8 activation following topical application of menthol may cause a cooling sensation elicited in sensory neurons beneath the skin. However, the comfortable cooling sensation could also be caused in part by decreased sweating. The relationship between a comfortable cooling sensation and less perspiration following menthol application may be difficult to determine, and we have mentioned this in the updated Discussion.

(5) The climbing assay is interesting and compelling. The authors note performing this under certain temperature and humidity conditions. Presumably, there is an optimal level of skin moisture, where skin that is too dry has less traction, but skin that is too wet may also have less traction. It would bolster this section of the study to perform this assay under hot conditions (perhaps TRPV4 KO mice, with impaired perspiration, would outperform WT mice with too much sweating?), or with pharmacologic intervention using TRPV4 agonists or antagonists to more rigorously evaluate whether this model correlates to TRPV4 function in the setting of different levels of perspiration.

We thank the reviewer for this suggestion. Upon detecting the involvement of TRPV4/ANO1 interaction in perspiration, we considered different behavioral analyses that can be performed to demonstrate whether the TRPV4/ANO1 interactions are involved in perspiration. As the reviewer suggested, there should be an optimal level of sweating. Therefore, we first set the room temperature at 26-27 ˚C and humidity at 35-50%. To our knowledge, this is the first demonstration of temperature-dependent sweating of mouse foot pads. In humans, palm sweating is often referred to as psychotic sweating that is known to be regulated by sympathetic nerve activity. Here we tested whether foot pad sweating might be related to friction force wherein sufficient amounts of sweating could increase the friction force and in turn increase the success rate for the climbing test using a vinyl-covered slippery slope that was selected based on several trials to determine the optimal surface material and slope angles. As the reviewer suggests, the success rates could be affected by multiple factors, and hot temperatures likely induce more sweating that could increase the success rates in the climbing test. We will need to carry out additional experiments that are beyond the scope of this study to examine these temperature-dependent effects. Generally, sweating is regulated by sympathetic nerve activity that occurs in response to increased brain neuron excitation. However, here we raise for the first time the possibility that sweating might be regulated by local temperature sensation mediated through TRPV4 that may be effective for fine-tuning of perspiration activity. We have updated the Discussion to reference this possibility.

(6) There are other studies (PMID 33085914, PMID 31216445) that have examined the role of TRPV4 in regulating perspiration. The presence of TRPV4 in eccrine glands is not a novel finding. Moreover, these studies noted that TRPV4 was not critical in regulating sweating in human subjects. These prior studies are in contradiction to the mouse data and the correlation to human anhidrotic skin in the present study. Neither of these studies is cited or discussed by the authors, but they should be. 

We thank the reviewer for referencing these other studies concerning the possible involvement of TRPV4 in perspiration in humans. These studies focused on the vasodilating effects of TRPV4 and drew the conclusion that TRPV4 is not involved in sweating in humans, which is in contrast to our data for mice and humans. Multiple factors could explain the apparent difference between the two studies. For example, the parameters they examined differed from ours in that we assessed patients with AIGA, whereas the previous studies involved healthy volunteers. We have updated the Discussion to note the difference in the results of our and previous studies.   

Reviewer #3 (Public Review):

(1) Figure 2: The calcium imaging-based approach shows average traces from 6 cells per genotype, but it was unclear if all acinar cells tested with this technique demonstrated TRPV4-mediated calcium influx, or if only a subset was presented.

“n = 6” does not indicate the number of cells, but rather 6 independent experiments that each had over 20 ROIs of sweat glands. We have clarified this point in the updated figure legend.

(2) Figure 4: The climbing behavioral test shows a significant reduction in climbing success rate in TRPV4-deficient mice. The authors ascribe this to a lack of hind paw 'traction' due to deficiencies in hind paw perspiration, but important controls and evidence that could rule out other potential confounds were not provided or cited. 

As noted in our response to Comment 5 made by Reviewer #2, we spent considerable time identifying optimal conditions that would delineate success rates in the climbing experiments. We are confident that TRPV4KO mice had significantly lower success rates than WT mice, but there are various factors that could affect the experimental outcomes. We reference these factors in the updated Discussion.

(3) In general, the results support the authors' claims that TRPV4 activity is a necessary component of sweat gland secretion, which may have important implications for controlling perspiration as well as secretion from other glands where TRPV4 may be expressed. 

As described above, the results we obtained in the climbing test can be affected by various factors. However, based on the consistency of the results obtained for the climbing test and the iodine and starch reaction assay, we think that our interpretation is correct. In terms of the involvement of TRPV4/ANO1 interactions in fluid secretion, we previously reported that the TRPV4/ANO1 complex is involved in cerebrospinal fluid secretion in the mouse choroid plexus (FASEB J. 2014) and in saliva and tear secretion in mouse salivary and lacrimal glands (FASEB J. 2018). Together, these findings suggest that this mechanism is common to water efflux from exocrine glands.

Reviewer #1 (Recommendations For The Authors):

(1) An exocrine gland-specific trpv4 knockout mouse should be used, as TRPV4 is also expressed by muscles, global knockout TRPV4 may affect the TRPV4-dependent muscle strength and reduce the climbing ability in mice. 

As the reviewer suggests, use of mice with TRPV4 knockout specific to exocrine glands would be preferable to mice having global TRPV4 knockout given that TRPV4 is expressed in multiple tissues. We agree with this suggestion, but we do not currently have such mice in hand. However, as mentioned above, we have reported the involvement of theTRPV4/ANO1 interaction in cerebrospinal fluid secretion from the choroid plexus in mice (FASEB J. 28: 2238-2248, 2014), as well as saliva and tear secretion in mouse salivary and lacrimal glands (FASEB J. 32: 1841-1854, 2018.), suggesting that the TRPV4/ANO1 interaction could be widely involved in exocrine gland functions that involve water movement. We have updated the Discussion to reference this point.  

(2) The authors showed Calcium imaging data that Menthol inhibits TRPV4-dependent calcium influx. However, it is well known that menthol induces the sensation of cooling by activating TRPM8. More evidence, including patch clamp recordings, should be done to verify the inhibition effects of menthol on TRPV4 and ANO1. Moreover, Fig 3E-3F could only suggest that menthol-induced cooling sensation may affect sweating but not the inhibition effect of menthol on TRPV4 and ANO1 channels. 

We agree that more evidence including patch-clamp recordings can verify the inhibitory effects of menthol on TRPV4 and ANO1. We did not include such experiments here since we previously showed that menthol and related agents indeed inhibit TRPV4- and ANO1-mediated currents (Sci. Rep. 7: 43132, 2017). We now cite this paper in the revised version.

(3) Excepting the climbing test, are there any other better models to asses the sweating-related behaviors? 

When we detected the involvement of TRPV4/ANO1 interactions in perspiration, we considered different types of behavioral analyses that could be used to demonstrate TRPV4/ANO1-dependent perspiration. We think that the climbing experiment is the best test, particularly since foot pads are one of the few regions on mice that is not covered by fur and thus amenable to evaluation of perspiration using an iodine and starch test.

Reviewer #2 (Recommendations For The Authors):

(1) I was confused by a section in the introduction on lines 59-60: How does Cl- efflux lead to the formation of a physical complex in cells with high intracellular Cl-? What is the physical complex? This seems like several disparate concepts combined together, which need to be clarified.

We apologize for the incomplete descriptions of several of our previous works. We have amended the Introduction section in the revised manuscript.

Reviewer #3 (Recommendations For The Authors):

(1) TRPV4 is expressed by multiple other cell types in the skin (keratinocytes, macrophages etc.) which may have an impact on peripheral sensory function. Is there evidence that TRPV4-deficient animals have relatively normal sensory acuity and/or proprioception? Such evidence would lend more credibility to the reported findings in the climbing test. 

As the reviewer points out, TRPV4 is expressed by multiple other cell types in the skin. To date we have found that TRPV4KO mice show no differences in sensory functions compared to WT mice. Whether TRPV4 is involved in proprioception is unclear, based on both our own observation and those that appear in the literature, although TRPV4 is clearly activated by mechanical stimuli. We previously compared the mechanical sensitivity of TRPV4 and Piezo1 in bladder epithelial cells, and found that Piezo 1 shows much higher sensitivity relative to TRPV4 (J. Biol. Chem. 289: 16565-16575, 2014), which is consistent with the involvement of Piezo1, rather than TRPV4, in proprioception. Although TRPV4 is reported to be expressed in sensory neurons, we did not detect TRPV4-mediated responses in isolated rat and mouse DRG neurons, suggesting that TRPV4-positive sensory neurons are relatively rare.

(2) The methods section refers to loading entire sweat glands with Fura-2 dye for calcium imaging, but the figure legend refers to sweat gland acinar cells. Resolving this ambiguity would help readers to interpret the data. 

We apologize for this error and have made an appropriate correction in the revised manuscript.

(3) Alternatively, could acute intraplantar injection of a TRPV4 antagonist (e.g. GSK205) in wild-type mice phenocopy the TRPV4-knockout mouse deficits, or could normal climbing behavior be restored in the TRPV4 knockout by adding artificial perspiration to their hindpaws?

We thank the reviewer for raising this interesting possibility and suggesting use of TRPV4 agonists or antagonists in the climbing tests. We agree that results of such an experiment would support the involvement of TRPV4 in sweating. We tried to do such experiments using injection of TRPV4 regulators into mouse hindpaws. However, the injections themselves appeared to impact climbing ability, perhaps in part due to painful sensations associated with the injection. Similarly, menthol injection appeared to reduce climbing activity, likely through pain sensations associated with TRPA1 activation. As such, we did not pursue these experiments.

Author Response

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

Reviewer #2 (Recommendations For The Authors):

We sincerely appreciate the time and efforts of the Reviewer.

In light of your data showing that the IgG response is similar with and without CIN, it would be good to drop "and induce abroad, vaccination-like anti-tumor IgG response". This suggests a direct connection between CIN and the IgG response.In my opinion, the shorter title is equally strong and more correct.

We edited this phrase in the originally submitted title for accuracy:

Chromosomal instability induced in cancer can enhance macrophage-initiated immune responses that include anti-tumor IgG

I agree that inducing CIN through other means can be left for a different study but in that case the abstract should moredirectly mention MSP1 inhibition since that is how CIN is always induced. Perhaps line 18: CIN is induced by MSP-1inhibition in poorly immunogenic....

Done as requested:

“…Here, CIN is induced in poorly immunogenic B16F10 mouse melanoma cells using spindle assembly checkpoint MPS1 inhibitors…”

---

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

eLife assessment

This study highlights a valuable finding that chromosomal instability can change immunes responses, in particular macrophages behaviours. The convincing results showing that the use of CD47 targeting and anti-Tyrp1 IgG can overcome changes in immune landscape in tumors and prolong survival of tumor-bearing mice. These findings reveal a new exciting dimension on how chromosomal instability can influence immune responses against tumor.

We thank the Editors for their enthusiasm and appreciation for this work. We also want to highlight our thanks for their careful reading, support, and patience while handling this manuscript. While this work provides useful insight into potential therapeutic implications of chromosomal instability in the macrophage immunotherapy field, we also hope it elucidates some novel basic science to further explore how chromosomal instability has such interesting effects on the immune system.

Public Reviews:

Reviewer #1 (Public Review):

The manuscript by Hayes et al. explored the potential of combining chromosomal instability with macrophage phagocytosis to enhance tumor clearance of B16-F10 melanoma. However, the manuscript suffers from substandard experimental design, some contradictory conclusions, and a lack of viable therapeutic effects.

The authors suggest that early-stage chromosomal instability (CIN) is a vulnerability for tumorigenesis, CD47-SIRPa interactions prevent effective phagocytosis, and opsonization combined with inhibition of the CD47-SIRPa axis can amplify tumor clearance. While these interactions are important, the experimental methodology used to address them is lacking.

Reviewer #1 (Recommendations For The Authors):

First, early stages of the tumor are essentially being defined as before implantation. In all cases, the tumor cells were pre-treated with MPS1i or had a genetic knockout of CD47. This makes it difficult to see how this would translate clinically.

We greatly appreciate the Reviewer’s interest in the topic and its potential, but our manuscript makes no claims of immediate clinical translation. Chromosomal instability (CIN) studies have to date not yet discovered or described whether and how CIN can affect macrophage function. To our knowledge, this is the first study to begin such characterizations with various MPS1i drugs to induce CIN. Many variations of the approach can be envisioned for future studies.

Our Results include some key studies of cancer cells with wildtype levels of CD47- including in vivo tumor elimination (Fig.3E). Nonetheless, we do conduct some of our studies in a CD47 knockout context to remove this “brake” that generally impedes phagocytosis, with our goal being to better understand how CIN affects phagocytosis. As cited to some extent in our Introduction, there are many efforts in clinical trials to disrupt this macrophage checkpoint and others focused on macrophage immunotherapy. Whether CIN can be induced by clinically translatable drugs and specifically in cancer cells is beyond the scope of our studies.

I would like to see the amount of CIN that occurs in WT B16F10 over the course of tumorigenesis (ie longer than 5 days). This is because I would assume that CIN would eventually occur in the WT B16F10 regardless of whether MPS1i is being given. And if that's the case, then the initiation of CIN at day 10 after implantation (for example) would still be considered "early stage" CIN. If the therapy is then initiated at this point, does the effect remain? Or put differently, how would the authors propose to induce the appropriate level of CIN in an established tumor? Why is pretreatment necessary?

Untreated B16F10 cells fail to produce micronuclei over 12 days compared to MPS1i treated cells – as shown in a newly added panel in Fig. S1:

Author response image 1.

This helps support our decision to pre-treat cells with MPS1i to stimulate genomic instability and is described in the first section of Results:

“…we saw >10-fold increases of micronuclei over the cell line’s low basal level (~1% of cells), and two other MPS1i inhibitors AZ3146 and BAY12-17389 confirm such effects (Fig. S1A). Micronuclei-positive cells can persist up to 12 days after treatment (Fig. S1B), while control cells maintain the low basal levels. The results suggest pre-treatment with MPS1i can simulate CIN in an experimental context even for 1-2 weeks, which may not typically occur at the same frequency during early tumor growth.

It is known that PD-1 expression inhibits tumor-associated macrophage phagocytosis (Nature, 2017). Does MSP1i (sic) treatment affect the population of PD-1+ tumor macrophages in vivo?

We thank the Reviewer for bringing up an interesting point.

Using the same tumor RNA-seq data that was used for Fig.1E, a heatmap of expression of PD-1 (gene Pdcd1) shows no consistent trend with MPS1i:

Author response image 2.

We also examined whether the secretome from CIN-afflicted cancer cells affect PD-1 expression in cultured macrophages, but we did not register any reads from our single-cell RNA-sequencing experiment for Pdcd1 in any of the macrophage clusters from Fig. 1H.

Author response image 3.

The Discussion section now includes a statement on this topic:

“…B16F10 tumors are poorly immunogenic, do not respond to either anti-CD47 or anti-PD-1/PDL1 monotherapies, and show modest and variable cure rates (~20-40%; Dooling et al., 2023; Hayes et al., 2023) even when macrophages have been made maximally phagocytic according to notions above. We should note here that our whole-tumor RNA-seq data (Fig.1E) shows expression of PD-1 (gene Pdcd1) follows no consistent trend upon MPS1i treatment, and that Pdcd1 was not detected in our scRNA-seq data for macrophage cultures (Fig.1G) – motivating further study.”

The authors must explain how the proposed therapy works since MPS1i increases tumor (cell) size, making it difficult for macrophages to phagocytose the tumor cells. It also reduces or suppresses Tyrp1 expression on the cancer cells, making it harder to opsonize. Since these were two main points for the rationale of this study, the authors need to reconcile them.

We appreciate this comment and have re-organized this Results section to try to minimize confusion:

CIN-afflicted, CD47-knockout tumoroids are eliminated by Macrophages

To assess functional effects of macrophage polarization, we focused on a 3D “immuno-tumoroid” model in which macrophage activity can work (or not) over many days against a solid proliferating mass of cancer cells in non-adherent roundbottom wells (Fig. 2A) (Dooling et al., 2023). We used CD47 knockout (KO) B16F10 cells, which removes the inhibitory effect of CD47 on phagocytosis, noting that KO does not perturb surface levels of Tyrp1, which is targetable for opsonization with anti-Tyrp1 (Fig. S2A). BMDMs were added to pre-assembled tumoroids at a 3:1 ratio, and we first assessed surface protein expression of macrophage polarization markers. Consistent with our whole-tumor bulk RNA-sequencing and also single-cell RNA-sequencing of BMDM monocultures (Fig. 1E, 1I-J), BMDMs from immunotumoroids of MPS1i-treated B16F10 showed increased surface expression of M1-like markers MHCII and CD86 while showing decreased expression of M2-like markers CD163 and CD206 (Fig. 2B-C). Although these macrophages seemed poised for anticancer activity, the cancer cells showed decreased binding of anti-Tyrp1 (Fig. S2B) and ~20% larger size in flow cytometry (Fig. S2C). The latter likely reflects cytokinesis defects and poly-ploidy as acute effects of CIN induction (Chunduri & Storchová, 2019; Mallin et al., 2022). Such cancer cell changes might explain why standard 2D phagocytosis assays show BMDMs attached to rigid plastic engulf relatively few anti-Tyrp1 opsonized cancer cells pretreated with MPS1i versus DMSO (Fig. S2D). In such cultures, BMDMs use their cytoskeleton to attach and spread, competing with engulfment of large and poorly opsonized targets. Noting that tumors in vivo are not as rigid as plastic, our 3D immunotumoroids eliminate attachment to plastic, and large numbers of macrophages can cluster and cooperate in engulfing cancer cells in a cohesive mass (Dooling et al., 2023). We indeed find CIN-afflicted tumoroids are eliminated by BMDMs regardless of anti-Tyrp1 opsonization (Fig. 2D-E), whereas anti-Tyrp1 is required for clearance of DMSO control tumoroids (Fig. 2D, S3B). Imaging also suggests that cancer CIN stimulates macrophages to cluster (compare Day-4 in Fig. 2D), which favors cooperative phagocytosis of tumoroids (Dooling et al., 2023), and occurs despite the lack of cancer cell opsonization and their larger cell size. The 3D immunotumoroid results with induced CIN are thus consistent with a more pro-phagocytic M1-type polarization (Fig.1J and 2B,C).

The authors used varying numbers of tumor cells for the in vivo portions of the study; the first half of the manuscript uses 500,000 cells, while the latter half uses 200,000 cells. Why?

The reasons for the difference in numbers is now clarified in the Methods:

For assessing immune infiltrates in early stages of tumor engraftment, when tumors are still small, we used a relatively high number of tumor cells (500,000 cells in Fig. 1D and Fig. 2F-G) to achieve sufficient cell numbers after dissociating the tumors, particularly for the slow-growing MPS1i-treated tumors. More specifically, with dissection, collagenase treatment, passage through a filter to remove clumps, we would lose many cells, and yet needed 100,000 viable cells or more for bulk RNA-seq suspensions and for flow cytometry measurements. For all other studies, 200,000 cancer cells were injected,

The authors need to report the tumor volumes and the total number of cells isolated from the day five tumors to avoid grossly inflating the effect (i.e. Fig 2G and 4G).

We have added relevant numbers in the Methods:

For day 5 post-challenge measurements, 100,000 to 200,000 live cells were collected. For in vivo tumor infiltrate studies in re-challenged mice, 10 million live cells were collected.

Also, regarding tumor sizes and cell numbers, we have previously published relevant measurements in assessments of tumor growth. Please see:

Brandon H Hayes, Hui Zhu, Jason C Andrechak, Lawrence J Dooling, Dennis E Discher, Titrating CD47 by mismatch CRISPR-interference reveals incomplete repression can eliminate IgG-opsonized tumors but limits induction of antitumor IgG, PNAS Nexus, Volume 2, Issue 8, August 2023, pgad243, https://doi.org/10.1093/pnasnexus/pgad243

Dooling, L.J., Andrechak, J.C., Hayes, B.H. et al. Cooperative phagocytosis of solid tumours by macrophages triggers durable anti-tumour responses. Nat. Biomed. Eng 7, 1081–1096 (2023). https://doi.org/10.1038/s41551-023-01031-3

In the present study, similar tumor growth curves are provided for transparency, but the Kaplan-Meier curves as the key pieces of data in Fig. 3-4. Lastly, regarding reporting total cell number harvested, we based our experiments on previously accepted measurements that also reported numbers out of total harvested cells. See:

Cerezo-Wallis, D., Contreras-Alcalde, M., … Soengas, M.S., 2020. Midkine rewires the melanoma microenvironment toward a tolerogenic and immune-resistant state. Nat Med 26, 1865–1877. https://doi.org/10.1038/s41591-020-1073-3

The figure titles need to be revised. For example, the title of Figure 1 claims that "MPS1i-induced chromosomal instability causes proliferation deficits in B16F10 tumors." However, the evidence provided is weak. The authors only present GSEA analysis of proliferation and no functional evidence of impairment. The authors need to characterize this proliferation deficit using in vitro studies and functional studies of macrophage polarization. I would suggest proliferation assays (crystal violet, MTT, Incucyte, etc) to measure the B16 growth over time with MPS1i treatment.

We thank the Reviewer for pointing this out. In Fig.1 we have minimized information regarding proliferation because it is later quantified in Figs.2D,E, S3, and 3D-i:

Fig.1F legend: Top downregulated hallmark gene sets in tumors comprised of MPS1i-treated B16F10 cells, showing downregulated DNA repair, cell cycle, and growth-related pathways, consistent with observations of slowed growth in culture and in vivo – as subsequently quantified.

Then the authors could collect the tumor supernatant to culture with macrophages and determine polarization in vitro. I would also like to see functional studies of macrophage polarization (suppression assays, cytokine production, etc). Currently, the authors provide no functional studies.

Fig.2B,C provides functional surface marker measurements of in vitro polarization toward anti-cancer M1 macrophages by MPS1i-pretreated tumor cells, consistent with gene expression in Fig.1G-J. Function is further shown as ant-cancer activity in Fig.2D,E, as now stated explicitly in the text:

“…In our 3D tumoroid in vitro assays, we found that macrophages can suppress the growth of chromosomally unstable tumoroids and clear them, surprisingly both with and without anti-Tyrp1 (Fig. 2D-E), regardless of MPS1i concentration used for treatment. Such a result is consistent with M1-type polarization (Fig.1J and 2B,C), which tends to be more pro-phagocytic. Such a result is consistent with M1-type polarization (Fig.1J and 2B,C), which tends to be more prophagocytic.”

The authors claim that macrophages are the key effector cells, but they need to provide evidence for this claim.

Other immune cells clearly contribute to the presented results because the IgG must eventually come from B cells. The text has been edited to indicate 'macrophages are key initiating-effector cells', and some evidence for this is the maximal survival of (WT B16 + Rev tumors) in Fig.3E upon treatment with Marrow Macrophages plus Macrophage-relevant SIRPa blockade and Macrophage-relevant IgG (via FcR). T cells do not have SIRPa or FcR.

They can deplete macrophages and T and B cells to determine whether the effect remains or is ablated. This is the only definitive way to make this claim.

To determine whether T and B cells might also be key initiating-effector cells, new experiments were done with mice depleted of T and B cells (per Fig.S9, below). We compared the growth of MPS1i vs DMSO treatments in these mice to results in mice with T and B cells (which should replicate our previous results in Fig.3D-i). We found that slower growth with Rev relative to DMSO was similar in mice without T and B cells compared to mice with T and B cells. We have added to the text our conclusion that: T and B cells are not key initiating-effector cells. Whereas B cells are effector cells at least in terms of eventually making anti-tumor IgG, our results show that macrophages are key initiating-effector cells because macrophages certainly affect the growth of (WT B16 + Rev tumors) when more are added (Fig.3E).

Author response image 4.

Growth of CIN-afflicted wild-type (WT) tumors in T- and B-cell deficient mice and T- and B-cell replete mice. Similar growth delays for MPS1i-pretreated B16F10 cells in T- and B-cell deficient NSG mice and immunocompetent C57BL/6 mice. Both types of mice have functional macrophages. Parallel studies in vivo were done with WT B16F10 ctrl cells cultured 24 h in 2.5 μM MPS1i (reversine or DMSO, then washed 3x in growth media for 5 min each and allowed to recover in growth media for 48 h. 200,000 cells in 100 uL PBS were injected subcutaneously into right flanks, and the standard size limit was used to determine survival curves. The C57BL/6 experiments were done independently here (by co-author L.J.D.) from the similar results (by B.H.H.) shown in Fig.3D-i, which provides evidence of reproducibility.

The Results section final paragraph describes all of this:

Macrophages seem to be the key initiating-effector cells, based in part on the following findings. First, macrophages with both SIRPα blockade and FcR-engaging, tumor-targeting IgG maximize survival of mice with WT B16 + Rev tumors (Fig. 3E) – noting that macrophages but not T cells express SIRPα and FcR’s. Despite the clear benefits of adding macrophages, to further assess whether T and B cells are key initiating-effector cells, new experiments were done with mice depleted of T and B cells. We compared the growth delay of MPS1i versus DMSO treatments in these mice to the delay in fully immunocompetent mice with T and B cells – with all studies done at the same time. We found that slower growth with Rev relative to DMSO was similar in mice without T and B cells when compared to immunocompetent C57 mice (Fig.S9). We conclude therefore that T and B cells are not key initiating-effector cells. At later times, B cells are likely effector cells at least in terms of making anti-tumor IgG, and T cells in tumor re-challenges are also increased in number (Fig. 4G-ii). We further note that in our earlier collaborative study (Harding et al., 2017) WT B16 cells were pre-treated by genome-damaging irradiation before engraftment in C57 mice, and these cells grew minimally – similar to MPS1i treatment – while untreated WT B16 cells grew normally at a contralateral site in the same mouse. Such results indicate that T and B cells in C57BL/6 mice are not sufficiently stimulated by genome-damaged B16 cells to generically impact the growth of undamaged B16 cells.

Reviewer #2 (Public Review):

Harnessing macrophages to attack cancer is an immunotherapy strategy that has been steadily gaining interest. Whether macrophages alone can be powerful enough to permanently eliminate a tumor is a high-priority question. In addition, the factors making different tumors more vulnerable to macrophage attack have not been completely defined. In this paper, the authors find that chromosomal instability (CIN) in cancer cells improves the effect of macrophage targeted immunotherapies. They demonstrate that CIN tumors secrete factors that polarize macrophages to a more tumoricidal fate through several methods. The most compelling experiment is transferring conditioned media from MSP1 inhibited and control cancer cells, then using RNAseq to demonstrate that the MSP1-inhibited conditioned media causes a shift towards a more tumoricidal macrophage phenotype. In mice with MSP1 inhibited (CIN) B16 melanoma tumors, a combination of CD47 knockdown and anti-Tyrp1 IgG is sufficient for long term survival in nearly all mice. This combination is a striking improvement from conditions without CIN.

Like any interesting paper, this study leaves several unanswered questions. First, how do CIN tumors repolarize macrophages? The authors demonstrate that conditioned media is sufficient for this repolarization, implicating secreted factors, but the specific mechanism is unclear. In addition, the connection between the broad, vaccination-like IgG response and CIN is not completely delineated. The authors demonstrate that mice who successfully clear CIN tumors have a broad anti-tumor IgG response. This broad IgG response has previously been demonstrated for tumors that do not have CIN. It is not clear if CIN specifically enhances the anti-tumor IgG response or if the broad IgG response is similar to other tumors. Finally, CIN is always induced with MSP1 inhibition. To specifically attribute this phenotype to CIN it would be most compelling to demonstrate that tumors with CIN unrelated to MSP1 inhibition are also able to repolarize macrophages.

Overall, this is a thought-provoking study that will be of broad interest to many different fields including cancer biology, immunology and cell biology.

We thank the Reviewer for their enthusiastic and positive comments toward the manuscript.

Our main purpose with this study has been discovery science oriented and mechanistic, with implications for improving macrophage immunotherapies. More experimentation needs to be done to further understand how this positive immune response emerges. However, we could address whether CIN enhances or not the anti-tumor IgG response by quantitative comparisons to our two other recent studies, and we conclude that it does not per new edits in the Abstract and the Results. See attached PPT for full details and comparison.

Abstract:

“CIN does not greatly affect the level of the induced response but does significantly increase survival.”

“…these results demonstrate induction of a generally potent anti-cancer antibody response to CIN-afflicted B16F10 in a CD47 KO context. Importantly, comparing these sera results for CINafflicted tumors to our recent studies of the same tumor model without CIN (Dooling et al., 2022; Hayes et al., 2022), we find similar levels of IgG induction (e.g. ~100-fold above naive on average for IgG2a/c), similar increases in phagocytosis by sera opsonization (e.g. equivalent to antiTyrp1), and similar levels of suppressed tumoroid growth – including the variability.

…

However, median survival increased (21 days) compared to their naïve counterparts (14 days), supporting the initial hypothesis of prolonged survival and consistent not only with past results indicating major benefits of a prime-&-boost approach with anti-Tyrp1 (Dooling et al., 2022) but also with the noted similarities in induced IgG levels.”

Future studies could certainly focus on trying to identify what secreted factors might be inducing the M1-like polarization (using ELISA assays for cytokine detection, for example). This could be important because a main finding here is that we achieve nearly a 100% success rate in clearing tumors when we combine CD47 ablation and IgG opsonization with cancer cell CIN. Previous studies were only able to achieve about 40% cures in mice when working with CD47 disription and IgG opsonization alone, suggesting CIN in this experimental context does improve macrophage response.

Lastly, we agree with the Reviewer that future studies should also address how CIN in general (not MPS1i-induced) affects tumor growth. The final paragraph of our Discussion at least cites support for consistent effects of M1-like polarization:

“The effects of CIN and aneuploidy in macrophages certainly requires further investigation. We did publish recently that M1-like polarization of BMDMs with IFNg priming is sufficient to suppress growth of B16 tumoroids with anti-Tyrp1 opsonization more rapidly than unpolarized/unprimed macrophages and much more rapidly than M2-like polarization of BMDMs with IL4 (Extended Data Fig.5a in Dooling et al., 2023); hence, anti-cancer polarization contributes in this assay.

While the secretome from MPS1i-treated cancer cells has been found to trigger…”

Nonetheless, we can only speculate that there is a threshold of CIN reached by a certain timepoint in tumor engraftment and growth. Natural CIN might not be enough, so we pursued a pharmacological approach consistent with ongoing pre-clinical studies (https://doi.org/10.1158/1535-7163.MCT-15-0500). Future studies should consider trying knockdown models to gradually accrue CIN in tumors or using more relevant pharmacological drugs that are known to induce CIN not associated with the spindle. We believe, however, that these are larger questions on their own and are beyond the scope of the foundational discoveries in this manuscript.

Reviewer #2 (Recommendations For The Authors):

None

We again thank the Reviewer for their support and enthusiasm for the manuscript. We made some additional changes and more data to address questions posed by the other Reviewer that we hope you find to help the manuscript further.

eLife assessment

The authors provide compelling evidence that MSP1 inhibition (leading to chromosomal instability or CIN in the cancer cells) increases phagocytosis and that tumors with CIN respond better to macrophage therapeutics. In this important study, they demonstrate particularly impressive survival rates for mouse models of CIN B16 tumors treated with adoptively transferred macrophages, CD47-SIRPα blockade, and anti-Tyrp1 IgG.

eLife assessment

This study provides a useful set of experiments showing the relative contribution of the Neurodrenergic system in reversing the sedation induced by midazolam. The evidence supporting the claims of the authors is solid, although specificity issues in the pharmacology and neural-circuit investigations narrow down the strengths of the conclusions. After dealing with these limitations, the paper will be of interest to medical biologists working on the neurobiology of anesthesia.

Reviewer #1 (Public Review):

In this study, Gu at al., investigated the role of the central noradrenaline system from LC to VLPO in the recovery of consciousness induced by midazolam. Combining pharmacology, optogenetics/chemogenetics, they found that the LC to VLPO NE circuits are essential for consciousness rebooting after midazolam, activation of this circuit strongly speeded up the recovery process, dependent on alpha1 adrenergic receptors in the VLPO neurons. The topic is important and their findings are of some interest.<br /> However, substantial improvements are needed in the language, for grammar, clarity, and layout. There are significant experimental errors (see below 1-2). Further experiments are required to support their main conclusions.

(1) One major issue arises in Figure 4, the recording of VLPO Ca2+ activity. In Lines 211-215, they stated that they injected AAV2/9-DBH-GCaMP6m into the VLPO, while activating LC NE neurons. As they claimed in line 157, DBH is a specific promoter for NE neurons. This implies an attempt to label NE neurons in the VLPO, which is problematic because NE neurons are not present in the VLPO. This raises concerns about their viral infection strategy since Ca activity was observed in their photometry recording. This means that DBH promoter could randomly label some non-NE neurons. Is DBH promoter widely used? The authors should list references. Additionally, they should quantify the labeling efficiency of both DBH and TH-cre throughout the paper.<br /> (2) A similar issue arises with chemogenetic activation in Fig. 5 L-R, the authors used TH-cre and DIO-Gq virus to label VLPO neurons. Were they labelling VLPO NE or DA neurons for recording? The authors have to clarify this.<br /> (3) Another related question pertains to the specificity of LC NE downstream neurons in the VLPO. For example, do they preferentially modulate GABAergic or glutamatergic neurons?<br /> (4) In Figure 1A-D, in the measurement of the dosage-dependent effect of Mida in LORR, were they only performed one batch of testing? If more than one batch of mice were used, error bar should be presented in 1B. Also, the rationale of testing TH expression levels after Mid is not clear. Is TH expression level change related to NE activation specifically? If so, they should cite references.<br /> (5) Regarding the photometry recording of LC NE neurons during the entire process of midazolam injection in Fig. 2 and Fig. 4, it is unclear what time=0 stands for. If I understand correctly, the authors were comparing spontaneous activity during the four phases. Additionally, they only show traces lasting for 20s in Fig. 2F and Fig. 4L. How did the authors select data for analysis, and what criteria were used? The authors should also quantify the average Ca2+ activity and Ca2+ transient frequency during each stage instead of only quantifying Ca2+ peaks. In line 919, the legend for Figure 2D, they stated that it is the signal at the BLA; were they also recorded from the BLA?

Reviewer #2 (Public Review):

Summary:

This article mainly explores the neural circuit mechanism of recovery of consciousness after midazolam administration and proves that the LC-VLPO NEergic neural circuit helps to promote the recovery of midazolam, and this effect is mainly caused by α1 adrenergic receptors. (α1-R) mediated.

Strengths:

This article uses innovative methods such as optogenetics and fiber optic photometry in the experimental methods section to make the stimulation of neuronal cells more precise and the stimulation intensity more accurate in experimental research. In addition, fiber optic photometry adds confidence to the results of calcium detection in mouse neuronal cells.

This article explains the results from the entire system down to cells, and then cells gradually unfold to explain the entire mechanism. The entire explanation process is logical and orderly. At the same time, this article conducted a large number of rescue experiments, which greatly increased the credibility of the experimental conclusions.

Throughout the full text and all conclusions, this article has elucidated the neural circuit mechanism of recovery of consciousness after midazolam administration and successfully verified that the LC-VLPO NEergic neural circuit helps promote the recovery of midazolam.

The conclusions of this article are crucial to ameliorate the complications of its abuse. It will pinpoint relevant regions involved in midazolam response and provide a perspective to help elucidate the dynamic changes in neural circuits in the brain during altered consciousness and suggest a promising approach towards the goal of timely recovery from midazolam. New research avenues.

At the same time, this article also has important clinical translation significance. The application of clinical drug midazolam and animal experiments have certain guiding significance for subsequent related clinical research.

Author Response:

We sincerely value the insightful and constructive feedback provided by the reviewers, which has been instrumental in identifying areas of our manuscript that required further clarification or amendment. Below are our responses detailing each comment.

Reviewer 1:

(1) One major issue arises in Figure 4, the recording of VLPO Ca2+ activity. In Lines 211-215, they stated that they injected AAV2/9-DBH-GCaMP6m into the VLPO, while activating LC NE neurons. As they claimed in line 157, DBH is a specific promoter for NE neurons. This implies an attempt to label NE neurons in the VLPO, which is problematic because NE neurons are not present in the VLPO. This raises concerns about their viral infection strategy since Ca activity was observed in their photometry recording. This means that DBH promoter could randomly label some non-NE neurons. Is DBH promoter widely used? The authors should list references. Additionally, they should quantify the labeling efficiency of both DBH and TH-cre throughout the paper.

(1) In Figure 5, we found that the VLPO received the noradrenergic projection from LC, indicating the recorded Ca2+ activity may come from the axon fibers corresponding to the projection. Similarly, Gunaydin et al. (2014) demonstrated that fiber photometry can be used to selectively record from neuronal projection.

(2) Located in the inner membrane of noradrenergic and adrenergic neurons, DBH (Dopamine-beta-hydroxylase) is an enzyme that catalyzes the conversion of dopamine to norepinephrine, and therefore plays an important role in noradrenergic neurotransmission. DBH is a marker of noradrenergic neurons. Zhou et al. (2020) clarified the probe specifically labeled noradrenergic neurons by immunolabeling for DBH. Recently, DBH promoter have been used in several studies (e.g., Han et al., 2024; Lian et al., 2023). The DBH-Cre mice are widely used to specifically labeled noradrenergic neurons (e.g., Li et al., 2023; Breton-Provencher et al., 2022; Liu et al., 2024). As reviewer said, it is difficult to distinguish the role of NE or DA neurons when using the TH promoter in VLPO. Therefore, we used DBH promoter with more specific labeling. LC is the main noradrenergic nucleus of the central nervous system. In our study, we injected rAAV-DBH-GCaMP6m-WPRE (Figure 2 and 8) and rAAV-DBH-EGFP-S'miR-30a-shRNA GABAA receptor)-3’-miR30a-WPRES (Figure 9) into the LC. The results showed that DBH promoter could specifically label noradrenergic neurons in the LC, while non-specific markers outside the LC were almost absent. As suggested, we will quantify the labeling efficiency of both DBH and TH-cre throughout the revised manuscript. This updated figure will provide a more rigorous analysis.

(2) A similar issue arises with chemogenetic activation in Fig. 5 L-R, the authors used TH-cre and DIO-Gq virus to label VLPO neurons. Were they labelling VLPO NE or DA neurons for recording? The authors have to clarify this.

As previously addressed in response to Comment #1, we acknowledge that it is difficult to distinguish the role of NE or DA neurons when using the TH promoter in VLPO. In the revised manuscript, we are considering conducting more restricted AAV injections into the VLPO to verify terminal expressions in the LC.

(3) Another related question pertains to the specificity of LC NE downstream neurons in the VLPO. For example, do they preferentially modulate GABAergic or glutamatergic neurons?

As suggested, we will supplement the multi-label ISH of LC NE downstream neurons in the VLPO to reveal the types of neurons they modulate.  

(4) In Figure 1A-D, in the measurement of the dosage-dependent effect of Mida in LORR, were they only performed one batch of testing? If more than one batch of mice were used, error bar should be presented in 1B. Also, the rationale of testing TH expression levels after Mid is not clear. Is TH expression level change related to NE activation specifically? If so, they should cite references.

(1) As recommended, we will supplement error bar in the revised manuscript.

(2) As reviewer suggested, the use of TH as a marker of NE activation is controversial, so in the revised manuscript, we will directly determine central norepinephrine content.

(5) Regarding the photometry recording of LC NE neurons during the entire process of midazolam injection in Fig. 2 and Fig. 4, it is unclear what time=0 stands for. If I understand correctly, the authors were comparing spontaneous activity during the four phases. Additionally, they only show traces lasting for 20s in Fig. 2F and Fig. 4L. How did the authors select data for analysis, and what criteria were used? The authors should also quantify the average Ca2+ activity and Ca2+ transient frequency during each stage instead of only quantifying Ca2+ peaks. In line 919, the legend for Figure 2D, they stated that it is the signal at the BLA; were they also recorded from the BLA?

(1) In this study, we used optical fiber calcium signal recording, which is a fluorescence imaging based on changes in calcium. The fluorescence signal is usually divided into different segments according to the behavior, and the corresponding segments are orderly according to the specific behavior event as the time=0. The mean calcium fluorescence signal in the time window 1.5s or 1s before the event behavior is taken as the baseline fluorescence intensity (F0), and the difference between the fluorescence intensity of the occurrence of the behavior and the baseline fluorescence intensity is divided by the difference between the baseline fluorescence intensity and the offset value. That is, the value ΔF/F0 represents the change of calcium fluorescence intensity when the event occurs. The results of the analysis are commonly represented by two kinds of graphs, namely heat map and event-related peri-event plot (e.g., Cheng et al., 2022; Gan-Or et al., 2023; Wei et al., 2018). In Fig. 2, the time points for awake, midazolam injection, LORR and RORR in mice were respectively selected as time=0, while in Fig. 4, RORR in mice was selected as time=0. The selected traces lasting for 20s was based on the length of a complete Ca2+ signal. We will explain the Ca2+ recording experiment more specifically in the revised manuscript.

(2) To the BLA, we sincerely apologize for our carelessness, the signal we recorded were from the LC rather than the BLA. We will carefully check and correct similar problems in the revised manuscript.

Reviewer 2:

In figure legends, abbreviations in figure should be supplemented as much as possible. For example, "LORR" in Figure 1.

As suggested, we will supplement abbreviations in figure as much as possible in the revised manuscript.

References

Gunaydin LA, Grosenick L, Finkelstein JC, et al. Natural neural projection dynamics underlying social behavior. Cell. 2014;157(7):1535-1551. doi:10.1016/j.cell.2014.05.017

Zhou N, Huo F, Yue Y, Yin C. Specific Fluorescent Probe Based on "Protect-Deprotect" To Visualize the Norepinephrine Signaling Pathway and Drug Intervention Tracers. J Am Chem Soc. 2020;142(41):17751-17755. doi:10.1021/jacs.0c08956

Han S, Jiang B, Ren J, et al. Impaired Lactate Release in Dorsal CA1 Astrocytes Contributed to Nociceptive Sensitization and Comorbid Memory Deficits in Rodents. Anesthesiology. 2024;140(3):538-557. doi:10.1097/ALN.0000000000004756

Lian X, Xu Q, Wang Y, et al. Noradrenergic pathway from the locus coeruleus to heart is implicated in modulating SUDEP. iScience. 2023;26(4):106284. Published 2023 Feb 27. doi:10.1016/j.isci.2023.106284

Li C, Sun T, Zhang Y, et al. A neural circuit for regulating a behavioral switch in response to prolonged uncontrollability in mice. Neuron. 2023;111(17):2727-2741.e7. doi:10.1016/j.neuron.2023.05.023

Breton-Provencher V, Drummond GT, Feng J, Li Y, Sur M. Spatiotemporal dynamics of noradrenaline during learned behaviour. Nature. 2022;606(7915):732-738. doi:10.1038/s41586-022-04782-2

Liu Q, Luo X, Liang Z, et al. Coordination between circadian neural circuit and intracellular molecular clock ensures rhythmic activation of adult neural stem cells. Proc Natl Acad Sci U S A. 2024;121(8):e2318030121. doi:10.1073/pnas.2318030121

Cheng J, Ma X, Li C, et al. Diet-induced inflammation in the anterior paraventricular thalamus induces compulsive sucrose-seeking. Nat Neurosci. 2022;25(8):1009-1013. doi:10.1038/s41593-022-01129-y

Gan-Or B, London M. Cortical circuits modulate mouse social vocalizations. Sci Adv. 2023;9(39):eade6992. doi:10.1126/sciadv.ade6992

Wei YC, Wang SR, Jiao ZL, et al. Medial preoptic area in mice is capable of mediating sexually dimorphic behaviors regardless of gender. Nat Commun. 2018;9(1):279. Published 2018 Jan 18. doi:10.1038/s41467-017-02648-0

eLife assessment

Münker and colleagues use an optical tweezer setup to apply oscillatory forces to endocytosed/phagocytosed glass beads over a wide frequency range (from ~1 to 1000 Hz) and probe cytoplasmic material properties at multiple time scales in six different cell types. Using statistical methods and principal component analysis, they find that the active and passive mechanical properties of cells can be described by 6 parameters (from power law fits) that allow characterizing the viscous and elastic nature of the cytoplasmic material as well as an effective active energy driven by cellular metabolism. Overall, this is very well done and important work, using convincing and state-of-the-art methods, albeit with some limitations related to the way the beads are internalized.

Reviewer #1 (Public Review):

Summary:

In this MS, Muenker and colleagues, explore the intracellular mechanics of a range of animal adherent cells. The study is based on the use of an optical tweezer set up, which allows to apply oscillatory forces on endocytosed/phagocytosed glass beads with a large frequency range (from ~1 to 1000 Hz) , allowing to probe cytoplasm material properties at multiple time scales. By switching off the laser trap, the authors also record the positional fluctuations of beads, to extract passive rheological signatures. The combination of both methods allow to fit 6 parameters (from power law fits) that allow to characterize the viscous and elastic nature of the cytoplasm material as well as an effective active energy driven by cellular metabolism. Using these methodologies, the authors first establish/confirm, using HeLa cells, that the cytoplasm is more solid like at short frequencies, and more fluid like at higher frequencies, and that these material states depend on both microtubules and actin cytoskeleton. The manuscript then go on to explore how these parameters evolve in other 6 cell types including muscles, highly migratory and epithelial cells. These results show for instance that muscle cells are much stiffer, while migratory cells are more fluid like with an increased active energy. Finally using statistical methods and principal component analysis, the authors establish some mechanical fingerprints (activity, fluidity and resistance) that allow to distinguish cell's mechanical state and relate it to their particular functions.

Strengths:

Overall this is a very well-executed work, which provides a large body of rigorous numbers and data to understand the regulation of cytoplasm mechanics and its relation to cell state/function.

Weaknesses:

A limit of the paper is that the biological mechanisms by which intracellular mechanics is modulated (e.g. among cell types) remains unexplored and only briefly discussed. Yet this limit is greatly offset by the rigor of the approach.

Reviewer #2 (Public Review):

Summary:

By analyzing cells' frequency-dependent viscoelastic properties and intracellular activity through microrheology, Münker et al simplify the complex active mechanical state into six key parameters that constitute the mechanical fingerprint. They apply this concept to cells treated with cytoskeleton-inhibiting drugs. Additionally, a comprehensive statistical analysis across various cell types shows how cells coordinate their mechanical properties within a defined phase-space marked by activity, mechanical resistance, and fluidity.

Strengths:

(1) The distribution of the six parameters: they have been well characterized based on established theories, and they can be used to understand cell-type-specific biomechanical differences. The examples of muscle cells and immune cells were profound and informative.<br /> (2) Efforts to perform dimension reduction of parameter space into activity (E), fluidity (C1) and resistance (A) are insightful and will be helpful for future characterization of cell mechanics.

Weaknesses:

(1) The most difficult part of the method is the part with actin polymerization inhibition with cytochalasin B. The data shows that viscoelastic parameters as well as active energy parameters are unaffected by cytochalasin B. It is reasonable to expect that elasticity will reduce and fluidity will increase upon application of such a drug. The stiffness-reducing effect was observed only when CB was used with nocodazole most likely because of phagocytosis of the bead, which is governed by microtubule. The use of other actin-depolymerizing drugs such as latrunculin A would be needed to test actin's role in mechanical fingerprints. If actin's role is only explained by accompanying microtubule inhibition, it is not a convenient system to directly test the mechano-adaptation process.<br /> (2) Depolymerization of MT with nocodazole did not reduce the solid-like property A. Adding discussion and comparison with other papers in the literature using nocodazole will be helpful in understanding why.<br /> (3) Overall, the usefulness of the concept of mechanical fingerprints and comparisons with other cell mechanics studies (from other groups) will make this manuscript stronger.

Reviewer #3 (Public Review):

Summary:

Cells and tissues are viscoelastic materials. However, metabolic processes that underly survival, growth and migration render the cell as an active matter at non-equilibrium. These two facts contribute to the difficulty of probing mechanical properties especially with sub-cellular resolution. However, the concept that the mechanical phenotype can be indicative of normal physiology necessitates approaches of defining the cellular phenotype. Here, Muenker et al evokes a powerful argument for mapping intracellular mechanics using optical tweezer- active microrheology. They present a suite of parameters towards a definition of a mechanical fingerprint. This is a compelling idea. There are some concerns as detailed below

Strengths:

These are technically challenging experiments and the authors provide systematic approaches to probe a system at non-equilibrium.

Weaknesses:

The importance of the mechanical fingerprint is diluted due to some missing controls needed for biological relevance.

Author response:

Reviewer 1:

A limit of the paper is that the biological mechanisms by which intracellular mechanics is modulated (e.g. among cell types) remains unexplored and only briefly discussed. Yet this limit is greatly offset by the rigor of the approach.

We thank the reviewer for the valuable feedback. The question regarding the biological mechanisms responsible for the different mechanical properties is, indeed, a highly important and interesting issue. In line with the reviewer, we consider this so important that it requires an extra, dedicated research focus, which is far beyond the scope of this article. By introducing the concept of the mechanical fingerprint, we provide in this work the framework to systematically investigate biological mechanisms but also the functional relevance of the intracellular mechanical properties in future studies. In the revised manuscript, we’ll elaborate on the discussion.

Reviewer 2:

The most difficult part of the method is the part with actin polymerization inhibition with cytochalasin B. The data shows that viscoelastic parameters as well as active energy parameters are unaffected by cytochalasin B. It is reasonable to expect that elasticity will reduce and fluidity will increase upon application of such a drug. The stiffness-reducing effect was observed only when CB was used with nocodazole most likely because of phagocytosis of the bead, which is governed by microtubule. The use of other actin-depolymerizing drugs such as latrunculin A would be needed to test actin’s role in mechanical fingerprints. If actin’s role is only explained by accompanying microtubule inhibition, it is not a convenient system to directly test the mechano-adaptation process.

We thank the reviewer for the time and the instructive feedback. Our finding that actin depolymerization has no effect on the intracellular mechanics may appear unfamiliar, as many rheological studies performed on the cell’s cortex highlight the importance of actin on the mechanical properties of the whole cell. However, as the actin network is reported to be very sparse away from the cortex it is not impossible that the mechanical properties may be dominated by other structures in the cytoplasm. Indeed, our findings are consisted with other studies that see no strong effect of actin depolymerization on the interphase intracellular mechanics (e.g. https://doi.org/10.1016/j.bpj.2023.04.011 or https://doi.org/10.1038/s41567-021-01368-z). Still, we fully agree with the reviewers that this is an important point. In a revised version we aim to investigate the effect of other actin-depolymerizing drugs and will try to perform immunostaining to visualize and further illuminate the potential compensation mechanism between actin and MT.

Depolymerization of MT with nocodazole did not reduce the solid-like property A. Adding discussion and comparison with other papers in the literature using nocodazole will be helpful in understanding why.

Again, we agree with the reviewer and propose to further study this point by performing additional immunostainings and by elaborating on the discussion, also including the results of other studies.

Reviewer 3:

The importance of the mechanical fingerprint is diluted due to some missing controls needed for biological relevance.

We thank the reviewer for his valuable time and feedback. This comment is in line with the point already raised by reviewer 1 and highlights the important question of how the intracellular mechanical properties are related to the actual cell function. We fully agree with the reviewers that at this point we can only report on differences, but cannot claim a biological function that is depending on the fingerprint. Although we think the alignment between function and the mechanical fingerprints allows the hypothesis that the biological system is tuning its mechanical properties for a specific function, we do not want to make any claim in this direction at the current state of our research. Hence, to answer these intriguing questions, carefully designed control experiments are required, as pointed out by the reviewer. However, this direction is not the scope of this manuscript. Here, we establish the tools we’ll use in future studies to address these highly relevant questions. Therefore, we propose to discuss these important future directions in a revised manuscript.

eLife assessment

This valuable manuscript sets out to identify sleep/arousal phenotypes in larval zebrafish carrying mutations in Alzheimer's disease (AD)-associated genes. The authors provide detailed phenotypic data for F0 knockouts of each of 7 AD-associated genes and then compare the resulting behavioral fingerprints to those obtained from a large-scale chemical screen to generate new hypotheses about underlying molecular mechanisms. The data presented are solid, although extensive interpretation of pharmacological screen data does not necessarily reflect the limited mechanistic data. Nonetheless, the phenotypic characterization presented is comprehensive, and the authors develop a well-designed behavioral analysis pipeline that will provide considerable value for zebrafish neuroscientists.

Reviewer #1 (Public Review):

Summary:

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

This is a highly innovative and thorough study, yet a handful of key questions remain. First, are nighttime sleep loss phenotypes observed in all knockouts for late-onset AD genes in the larval zebrafish a valid proxy for AD risk? For those mutants that cause nighttime sleep disturbances, do these phenotypes share a common underlying pathway? e.g. Do 5-HT reuptake inhibitors promote sleep across all 4 late-onset genes in addition to psen1? Can 5-HT reuptake inhibitors reverse other AD-related pathologies in zebrafish? Can compounds be identified that have a common behavioral fingerprint across all or multiple AD risk genes? Do these modify sleep phenotypes? Finally, the web-based platform presented could be expanded to facilitate comparison of other behavioral phenotypes, including stimulus-evoked behaviors. Finally, the authors propose but do not test the hypothesis that sorl1 might regulate localization/surface expression of 5-HT2 receptors. This could provide exciting / more convincing mechanistic support for the assertion that serotonin signaling is disrupted upon loss of AD-associated genes. Despite these important considerations, this study provides a valuable platform for high-throughput analysis of sleep phenotypes and correlation with small-molecule-induced sleep phenotypes.

Strengths:

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

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

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

Weaknesses:

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

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

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

Reviewer #2 (Public Review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

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

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

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

Reviewer #3 (Public Review):

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

A notable weakness is the introduction, which overly generalizes numerous concepts and fails to provide the necessary background to set the stage for the data.

Major points

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

(2) Because in the end the authors did not screen that many lines, it would increase confidence in the phenotypes to provide more validation of KO specificity. Some suggestions include:<br /> a. The authors cite a psen1 and psen2 germline mutant lines. Can these be tested in the FramebyFrame R analysis? Do they phenocopy F0 KO larvae?<br /> b. psen2KO is one of the larger centerpieces of the paper. The authors should present more compelling evidence that animals are truly functionally null. Without this, how do we interpret their phenotypes?<br /> c. Related to the above, for cd2AP and sorl1 KO, some of the effect sizes seem to be driven by one clutch and not the other. In other words, great clutch-to-clutch variability. Should the authors increase the number of clutches assayed?

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

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

(5) The conclusions for the serotonin section are overstated. Behavioural pharmacology purports to predict a signaling pathway disrupted with sorl1 KO. But is it not just possible that the drug acts in parallel to the true disrupted pathway in these fish? There is no direct evidence for serotonin dysfunction - that conclusion is based on response to the drug. Moreover, it is just 1 drug - is the same phenotype present with another SSRI? Likewise, language should be toned down in the discussion, as this hypothesis is not "confirmed" by the results (consider "supported"). The lack of measured serotonin differences further raises concern that this is not the true pathway. This is another major point that deserves further experimental evidence, because without it, the entire approach (behavioral pharm screen) seems more shaky as a way to identify mechanisms. There are any number of testable hypotheses to pursue such as a) Using transient transgenesis to visualize 5HT neuron morphology (is development perturbed: cell number, neurite morphology, synapse formation); b) Using transgenic Ca reporters to assay 5HT neuron activity.

Author response:

Public Reviews:

Reviewer #1 (Public Review):

Summary:

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

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

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

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

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

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

– Four indications are shared by 4/7 knockouts: “mydriasis” (dilated pupils, significant for psen1, apoea/apoeb, cd2ap, clu); “fragile X syndrome” (psen1, apoea/apoeb, cd2ap, sorl1), “insomnia” (psen2, apoea/apoeb, cd2ap, sorl1); “malignant essential hypertension” (appa/appb, psen1, apoea/apoeb, cd2ap).

– Two targets are shared by 5/7 knockouts: “glycogen synthase kinase−3 alpha” (psen1, apoeab, cd2ap, clu, sorl1) and “neuronal acetylcholine receptor beta−2” (appa/appb, psen1, apoeab, cd2ap, clu).

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

As reminder, we hypothesised that loss of Sorl1 affected serotonin signalling based on the following annotations being significant: indication “depression”, target “serotonin transporter”, and KEGG pathway “serotonergic synapse”. All three are also significant for psen2 knockouts, but none others. ZOLTAR therefore does not predict serotonin signalling to be a major theme common to all mutants with a night-time sleep loss phenotype.

While perhaps not surprising, we find reassuring that insomnia appears in the indications shared by the largest number of knockouts. apoea/apoeb, cd2ap, sorl1 also happen to be the knockouts with the largest loss in night-time sleep.

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

We see that literature also exists on the involvement of glycogen synthase kinase-3 in AD (Lauretti et al., 2020). We plan to explore further these predictions in a future study.

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

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

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

5-HT receptor type 4a is another candidate as it was shown to interact with sorting nexin 27, a subunit of retromer (Joubert et al., 2004). We see that antibodies against human 5-HT receptor type 2 and 4a exist; whether they would work in zebrafish remains to be tested, and in our experience, the availability of antibodies suitable for immunohistochemistry in the zebrafish is a serious experimental roadblock.

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

Strengths:

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

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

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

Weaknesses:

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

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

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

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

Reviewer #2 (Public Review):

Summary:

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

Strengths:

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

Weaknesses:

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

Thank you for this cogent criticism.

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

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

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

On the second point, we agree that testing first ZOLTAR on a mutant for which we have a fairly good understanding of the mechanism causing the behavioural phenotype could have been a productive approach. Note, however, that examples already exist in the literature. First, Hoffman et al. (2016) found that drugs generating behavioural fingerprints that positively correlate with the cntnap2a/cntnap2b double knockout fingerprint are enriched with NMDA and GABA receptor antagonists. In experiments analogous to our citalopram treatment (Fig. 5c,d), cntnap2a/cntnap2b knockout larvae were found to be overly sensitive to the NMDA receptor antagonist MK-801 and the GABAA receptor antagonist pentylenetetrazol (PTZ). Among other drugs tested, zolpidem, a GABAA receptor agonist, caused opposite effects on wild-type and cntnap2a/cntnap2b knockout larvae. Knockout larvae also had fewer GABAergic neurons in the forebrain. Second, Ashlin et al. (2018) found that the fingerprint of pitpnc1a knockout larvae clustered with anti-inflammatory compounds. Flumethasone, an anti-inflammatory corticosteroid, caused a lower increase in activity when added to knockout larvae compared to wild-type larvae. While these studies did not use precisely the same analysis that ZOLTAR runs, they used the same rationale and behavioural dataset to make these predictions (Rihel et al., 2010), which shows that approaches like ZOLTAR can point to causal processes.

Related to your next point, we may reduce the discussion on sorl1 and serotonin and add some of the present arguments instead, depending on the results from  testing a second SSRI (see next point).

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

We mostly agree with this criticism. One could interpret the larger spread of the data for sorl1 larvae treated with 10 µM citalopram as evidence that the knockout larvae do indeed react differently to the drug at this dose. However, the result indeed does not survive removing the top 5 (p = 0.87) or top 3 (p = 0.18) sorl1 larvae.

Given that the HCR did not reveal anything striking, we agree with you that too much of our argument relies on this result being robust. As you and reviewer #3 suggest, we plan on repeating this experiment with a different serotonin reuptake inhibitor (SSRI). If the other SSRI also shows a differential effect, this should strengthen the claim that ZOLTAR correctly predicted serotonin signalling as being affected by the loss of Sorl1, even if we did not discover the molecular mechanism.

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

There are no strong scientific reasons why this hypothesis was not tested. The lead author (F Kroll) moved to a different lab and country so the project was finalised at that time. We do not plan on testing this hypothesis at this stage. However, we will adapt the wording to make it clear this is one possible alternative hypothesis which could be tested in the future, rather than the only alternative.

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

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

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

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

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

On “it is well known that the upregulation of APP is the driver of Alzheimer’s, not downregulation”; we of course agree. Among others, the examples of Down syndrome, APP duplication (Sleegers et al., 2006), or mouse models overexpressing human APP show definitely that overexpression of APP is sufficient to cause AD. Having said that, we would not be so quick in dismissing APP knockout as potentially relevant to understanding of Alzheimer’s disease. Loss of soluble Aβ due to aggregation could contribute to pathology (Espay et al., 2023). Without getting too much into this intricate debate, links between levels of Aβ and risk of disease are often counter-intuitive too. For example, out of 138 PSEN1 mutations screened in vitro, 104 reduced total Aβ production and 11 even seemingly abolished the production of both Aβ40 and Aβ42 (Sun et al., 2017). In short, loss of soluble Aβ occurs in both AD and in our appa/appb knockout larvae, but the ideal approach would be to study zebrafish larvae with an in-frame deletion in the Aβ sequence within appa/appb.

We will adapt the language to address your point. We would not want to imply, for example, that the absence of a night-time sleep phenotype for appa/appb is contradictory to the body of literature showing links between Aβ and sleep, including in zebrafish (Özcan et al., 2020). As you say, our experiment tested loss of App, including Aβ, while the literature typically reports on overexpression of APP, as in APP/PSEN1-overexpressing mice (Jagirdar et al., 2021).

Reviewer #3 (Public Review):

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

A notable weakness is the introduction, which overly generalizes numerous concepts and fails to provide the necessary background to set the stage for the data.

Major points

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

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

It is true however that we do not give much information on how some of the less intuitive parameters, such as activity slope or fractal dimension, are calculated or what they describe about the dataset (e.g. roughness/smoothness for fractal dimension). We will improve this in our revised version.

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

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

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

b. psen2KO is one of the larger centerpieces of the paper. The authors should present more compelling evidence that animals are truly functionally null. Without this, how do we interpret their phenotypes?

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

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

We understand that the zebrafish community may be cautious about F0 phenotyping compared to stably generated mutants. As mentioned to Reviewer 2, we are planning to assemble a paper that expressly examines F0s vs. stable mutants to allay some of these concerns. We would also suggest that our current manuscript, which combines CRISPR-F0 rapid screening with in silico pharmacological predictions, ultimately represents a first step in characterizing the functions of genes.

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

Correct, there is great clutch-to-clutch variability in this behavioural assay. This is not specific to our experiments. Even within the same strain, wild-type larvae from different clutches (i.e. non-siblings) behave differently (Joo et al., 2021). This is why it is essential to compare behavioural phenotypes within individual clutches (i.e., from a single pair of parents, one male and one female), as we explain in Methods (section Behavioural video-tracking) and in the documentation of the FramebyFrame package. We often see two different experimental designs in literature: comparing non-sibling wild-type and mutant larvae, or pooling different clutches which include all genotypes (e.g., pooling multiple clutches from heterozygous in-crosses or pooling wild-type clutches before injecting them). The first experimental design causes false positive findings, as the clutch-to-clutch variability we and others (Joo et al., 2021) observe gets interpreted as a behavioural phenotype. The second experimental design should not cause false positives but will decrease the sensitivity of the assay by increasing the spread within genotypes. In both cases, the clutch-to-clutch variability is hidden, either by interpreting it as a phenotype (first case) or by adding it to animal-to-animal variability (second case). Our experimental design is technically more challenging as it requires obtaining large clutches from unique pairs of parents. However, this approach is better as it clearly separates the different sources of variability (clutch-to-clutch or animal-to-animal). As for every experiment, yes, a larger number of replicates would be better, but we do not plan to assay additional clutches at this time. Our work heavily focuses on the sorl1 and psen2 knockout behavioural phenotypes. The key aspects of these phenotypes were effectively tested in four clutches as sorl1 were also tested in the citalopram experiment (Fig. 5), and psen2 was also tested in the small molecule rescue experiment (Fig. 6 and Fig. 6–suppl. 1). In the citalopram experiment, one H2O-treated sorl1 knockout clutch (n = 10) replicates fairly well the baseline recordings in Fig. 4–suppl. 5, the other does not but had especially low sample size (n = 6).

We also plan to test another SSRI on sorl1 knockouts, so this point will be addressed.

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

This is a fair criticism but we do not make this claim, at least not from expression. The reviewer is probably referring to the following quote:

“[…] most of these were expressed in the brain of 5–6-dpf zebrafish larvae, suggesting they play a role in early brain development or function,”

which does not mention future risk of Alzheimer’s disease. We do suggest that these genes have a function in development. After all, every gene that plays a role in brain development must be expressed during development, so this wording seems reasonable. As noted, the primary goal was to check that the genes we selected were indeed expressed in zebrafish larvae before performing knockout experiments. Our discussion does raise the hypothesis that mutations in Alzheimer’s risk genes impact brain development and sleep early in life, but this argument primarily relies on our observation that knockout of late-onset Alzheimer’s risk genes causes sleep phenotypes in 7-day old zebrafish larvae and from previous work showing brain structural differences in infants and children at high genetic risk of Alzheimer’s disease (Dean et al., 2014; Quiroz et al., 2015), not solely on gene expression early in life.

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

This is a fair criticism. We agree it is a concern, especially in the case of psen2 as we claim that day-time sleep is increased while zebrafish are diurnal. We do not rely heavily on the day-time inactivity being sleep (the ZOLTAR predictions or the small molecule rescue do not change whether the parameter is called sleep or inactivity), but  our choice of labelling may be misleading. We will try to test this claim by plotting the distribution of the inactive period durations. If psen2 knockout larvae indeed sleep more during the day compared to controls, we might predict that inactive periods longer than 1 minute to increase disproportionately compared to the increase in shorter inactive periods.

To address, “are psen2 KO responsive to startling stimuli like controls when awake/when quiescent”, we can try to look at the behaviour of psen2 knockout larvae that were awake (i.e., moved in the preceding one minute) or ‘asleep’ (i.e., did not move in the preceding one minute) at the light transitions and count the proportion of psen2 knockout or control larvae which displayed a startle response. If most psen2 knockouts react to the light transition, it should at least exclude the concern that they are very unhealthy, as the reviewer suggests. This criticism seems challenging to definitely address experimentally though. A possible approach could be to use a closed-loop system which, after one minute of inactivity, triggers a stimulus which is sufficient to startle an awake larva but not an asleep larva. If psen2 knockout larvae indeed sleep more during the day, the stimulus should usually not be sufficient to startle them. Note, how to calibrate this stimulus is also not straightforward. We do not plan to test this, but our analysis of the light transitions may provide a decent proxy.

(5) The conclusions for the serotonin section are overstated. Behavioural pharmacology purports to predict a signaling pathway disrupted with sorl1 KO. But is it not just possible that the drug acts in parallel to the true disrupted pathway in these fish? There is no direct evidence for serotonin dysfunction - that conclusion is based on response to the drug. Moreover, it is just 1 drug - is the same phenotype present with another SSRI? Likewise, language should be toned down in the discussion, as this hypothesis is not "confirmed" by the results (consider "supported"). The lack of measured serotonin differences further raises concern that this is not the true pathway. This is another major point that deserves further experimental evidence, because without it, the entire approach (behavioral pharm screen) seems more shaky as a way to identify mechanisms. There are any number of testable hypotheses to pursue such as a) Using transient transgenesis to visualize 5HT neuron morphology (is development perturbed: cell number, neurite morphology, synapse formation); b) Using transgenic Ca reporters to assay 5HT neuron activity.

Regarding the comment, “is it not just possible that the drug acts in parallel to the true disrupted pathway”, we think no, assuming we understand correctly your question. Key to our argument is the fact that sorl1 knockout larvae react differently to the drug than control larvae. As an example, take night-time sleep bout length, which was not affected by knockout of sorl1 (Fig. 4–suppl. 5). For the sake of the argument, say only dopamine signalling (the “true disrupted pathway”) was affected in sorl1 knockouts but that serotonin signalling was intact. Assuming that citalopram specifically alters serotonin signalling, then treatment should cause the same increase in sleep bout length in both knockouts and controls as serotonin signalling is intact in both. This is not what we see, however. Citalopram caused a greater increase in sleep bout length in sorl1 knockouts than in scrambled-injected larvae. In other words, the effect is non-additive, in the sense that citalopram did not add the same number of Z-scores to sorl1 knockouts or controls. We think this shows that serotonin signalling is somehow different in sorl1 knockouts. Nonetheless, we would concede that the experiment does not necessarily says much about the importance of the serotonin disruption caused by loss of Sorl1. It could be, for example, that the most salient consequence of loss of Sorl1 is cholinergic disruption (see reply to Reviewer #1 above) and that serotonin signalling is a minor theme.

Furthermore, we agree with you and Reviewer #2 that the conclusions are overly confident. We will repeat this experiment with another SSRI as you suggest. Your suggestions to further test the serotonin system in the sorl1 knockouts are excellent as well, however we do not plan to pursue them at this stage.

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eLife assessment

van Vliet and colleagues show a correlation between internal states of a convolutional neural network (CNN) trained on visual word stimuli with three specific components of evoked MEG potentials during reading in humans. The findings are useful, but the current results remain incomplete, without evidence that the CNN can produce any of the phenomena that the human visual system is known to have (e.g., feedback connections, sensitivity to word frequency), or that the model has comparable performance to human behaviour (i.e., similar task accuracy with a comparable pattern of mistakes).

Reviewer #1 (Public Review):

Summary:

This study trained a CNN for visual word classification and supported a model that can explain key functional effects of the evoked MEG response during visual word recognition, providing an explicit computational account from detection and segmentation of letter shapes to final word-form identification.

Strengths:

This paper not only bridges an important gap in modeling visual word recognition, by establishing a direct link between computational processes and key findings in experimental neuroimaging studies, but also provides some conditions to enhance biological realism.

Weaknesses:

The interpretation of CNN results, especially the number of layers in the final model and its relationship with the processing of visual words in the human brain, needs to be further strengthened.

Reviewer #2 (Public Review):

van Vliet and colleagues present the results of a study correlating internal states of a convolutional neural network trained on visual word stimuli with evoked MEG potentials during reading.

In this study, a standard deep learning image recognition model (VGG-11) trained on a large natural image set (ImageNet) that begins illiterate but is then further trained on visual word stimuli, is used on a set of predefined stimulus images to extract strings of characters from "noisy" words, pseudowords and real words. This methodology is used in hopes of creating a model that learns to apply the same nonlinear transforms that could be happening in different regions of the brain - which would be validated by studying the correlations between the weights of this model and neural responses. Specifically, the aim is that the model learns some vector embedding space, as quantified by the spread of activations across a layer's units (L2 Norm after ReLu Activation Function), for the different kinds of stimuli, that creates a parameterized decision boundary that is similar to amplitude changes at different times for a MEG signal. More importantly, the way that the stimuli are ordered or ranked in that space should be separable to the degree we see separation in neural activity. This study shows that the activation corresponding to five different broad classes of stimuli statistically correlates with three specific components in the ERP. However, I believe there are fundamental theoretical issues that limit the implications of the results of this study.

As has been shown over many decades, many potential computational algorithms, with varied model architectures, can perform the task of text recognition from an image. However, there is no evidence presented here that this particular algorithm has comparable performance to human behavior (i.e. similar accuracy with a comparable pattern of mistakes). This is a fundamental prerequisite before attempting to meaningfully correlate these layer activations to human neural activations. Therefore, it is unlikely that correlating these derived layer weights to neural activity provides meaningful novel insights into neural computation beyond what is seen using traditional experimental methods.

One example of a substantial discrepancy between this model and neural activations is that, while incorporating frequency weighting into the training data is shown to slightly increase neural correlation with the model, Figure 7 shows that no layer of the model appears directly sensitive to word frequency. This is in stark contrast to the strong neural sensitivity to word frequency seen in EEG (e.g. Dambacher et al 2006 Brain Research), fMRI (e.g. Kronbichler et al 2004 NeuroImage), MEG (e.g. Huizeling et al 2021 Neurobio. Lang.), and intracranial (e.g. Woolnough et al 2022 J. Neurosci.) recordings. Figure 7 also demonstrates that the late stages of the model show a strong negative correlation with font size, whereas later stages of neural visual word processing are typically insensitive to differences in visual features, instead showing sensitivity to lexical factors.

Another example of the mismatch between this model and the visual cortex is the lack of feedback connections in the model. Within the visual cortex, there are extensive feedback connections, with later processing stages providing recursive feedback to earlier stages. This is especially evident in reading, where feedback from lexical-level processes feeds back to letter-level processes (e.g. Heilbron et al 2020 Nature Comms.). This feedback is especially relevant for the reading of words in noisy conditions, as tested in the current manuscript, as lexical knowledge enhances letter representation in the visual cortex (the word superiority effect). This results in neural activity in multiple cortical areas varying over time, changing selectivity within a region at different measured time points (e.g. Woolnough et al 2021 Nature Human Behav.), which in the current study is simplified down to three discrete time windows, each attributed to different spatial locations.

The presented model needs substantial further development to be able to replicate, both behaviorally and neurally, many of the well-characterized phenomena seen in human behavior and neural recordings that are fundamental hallmarks of human visual word processing. Until that point, it is unclear what novel contributions can be gleaned from correlating low-dimensional model weights from these computational models with human neural data.

Reviewer #3 (Public Review):

Summary:

The authors investigate the extent to which the responses of different layers of a vision model (VGG-11) can be linked to the cascade of responses (namely, type-I, type-II, and N400) in the human brain when reading words. To achieve maximal consistency, they add noisy-activations to VGG and finetune it on a character recognition task. In this setup, they observe various similarities between the behavior of VGG and the brain when when presented with various transformations of the words (added noise, font modification, etc).

Strengths:

- The paper is well-written and well-presented.

- The topic studied is interesting.

- The fact that the response of the CNN on unseen experimental contrasts such as adding noise correlated with previous results on the brain is compelling.

Weaknesses:

- The paper is rather qualitative in nature. In particular, the authors show that some resemblance exists between the behavior of some layers and some parts of the brain, but it is hard to quantitively understand how strong the resemblances are in each layer, and the exact impact of experimental settings such as the frequency balancing (which seems to only have a very moderate effect according to Figure 5).

- The experiments only consider a rather outdated vision model (VGG).

Author response:

We thank the reviewers for their efforts. They have pointed out several shortcomings and made very helpful suggestions. Below, we shortly address the weak points that the reviewers brought up and outline what improvements we intend to make for the revised paper in response.

Reviewer #1:

The interpretation of CNN results, especially the number of layers in the final model and its relationship with the processing of visual words in the human brain, needs to be further strengthened.

The results of our experimentation with the number of layers and the number of units in each layer can be found in the supplementary information. In the revised version, we will bring some of these results into the main text and discuss them more thoroughly.

Reviewer #2:

As has been shown over many decades, many potential computational algorithms, with varied model architectures, can perform the task of text recognition from an image. However, there is no evidence presented here that this particular algorithm has comparable performance to human behavior (i.e. similar accuracy with a comparable pattern of mistakes). This is a fundamental prerequisite before attempting to meaningfully correlate these layer activations to human neural activations. Therefore, it is unlikely that correlating these derived layer weights to neural activity provides meaningful novel insights into neural computation beyond what is seen using traditional experimental methods.

We very much agree with the reviewer that a qualitative analysis of whether the model can explain experimental effects needs to happen before a quantitative analysis, such as evaluating model-brain correlation scores. In fact, this is one of the key points we wished to make.

This starts with the observation that "traditional" models of reading (=those that do not rely on deep learning) cannot explain some very basic human behavioral results, such as humans being able to recognize a word regardless of exact letter shape, size, and (up to a point) rotation. This is not so much a failure on the part of traditional models as it is a difference in focus. There are models of vision that focus on these low-level things, currently dominated by deep learning, but these are rarely evaluated in the context of reading, which has its own literature and well-known experimental effects. We believe the current version of the manuscript makes insufficiently clear what the goals of our modeling effort are exactly, which is something we will attempt to correct in the revision.

Since our model only covers the first phase of reading, with a special focus on letter shape detection, we sought to compare it with neuroimaging data that can provide "snapshots" of the state of the brain during these early phases, rather than comparing it with behavioral results that occur at the very end. However, we very much make this comparison in the spirit hinted at by the reviewer. The different MEG components have a distinct "behavior" to them in the way they respond to different experimental conditions (Figure 2), and the model needs to replicate this behavior (Figure 4). Only then do we move on to a quantitative analysis.

One example of a substantial discrepancy between this model and neural activations is that, while incorporating frequency weighting into the training data is shown to slightly increase neural correlation with the model, Figure 7 shows that no layer of the model appears directly sensitive to word frequency. This is in stark contrast to the strong neural sensitivity to word frequency seen in EEG (e.g. Dambacher et al 2006 Brain Research), fMRI (e.g. Kronbichler et al 2004 NeuroImage), MEG (e.g. Huizeling et al 2021 Neurobio. Lang.), and intracranial (e.g. Woolnough et al 2022 J. Neurosci.) recordings. Figure 7 also demonstrates that the late stages of the model show a strong negative correlation with font size, whereas later stages of neural visual word processing are typically insensitive to differences in visual features, instead showing sensitivity to lexical factors.

We are glad the reviewer brought up the topic of frequency balancing, as it is a good example of the importance of the qualitative analysis. As the reviewer points out, frequency balancing during training only had a moderate impact on correlation scores and from that point of view does not seem impactful. However, when we look at the qualitative evaluation, we see that with a large vocabulary, a model without frequency balancing fails to properly distinguish between consonant strings and (pseudo)words (Figure 4, 5th row). Hence, from the point of view of being able to reproduce experimental effects, frequency balancing had a large impact. It is true that the model, even with frequency balancing, only captures letter- and bigram-frequency effects and not word-frequency effects, as we know the N400 is sensitive to. This could mean that N400 word-frequency effects are driven by mechanics that our current model lacks, such as top-down effects from systems further up the processing pipeline.

We agree with the reviewer that the late-stage sensitivity of the model to font size must be seen as a flaw. Of course, we say as much when we discuss this result in the paper. Important context for this flaw is that the main aim of the model is to reproduce the experimental effects of Vartiainen et al. (2011), which does not include manipulation of word length. The experimental contrasts in Figure 7 are meant to explore a bit beyond the boundaries of that particular study, but were never considered "failure points". When presenting a model, it's important to show its limitations too.

Another example of the mismatch between this model and the visual cortex is the lack of feedback connections in the model. Within the visual cortex, there are extensive feedback connections, with later processing stages providing recursive feedback to earlier stages. This is especially evident in reading, where feedback from lexical-level processes feeds back to letter-level processes (e.g. Heilbron et al 2020 Nature Comms.). This feedback is especially relevant for the reading of words in noisy conditions, as tested in the current manuscript, as lexical knowledge enhances letter representation in the visual cortex (the word superiority effect). This results in neural activity in multiple cortical areas varying over time, changing selectivity within a region at different measured time points (e.g. Woolnough et al 2021 Nature Human Behav.), which in the current study is simplified down to three discrete time windows, each attributed to different spatial locations.

In this study, we make a start in showing how deep learning techniques could be beneficial to enhance models of reading by showing how even a simple CNN, after a few enhancements, can account for several experimental MEG effects that we see in reading tasks, but are outside the focus of traditional models of reading. We never intended to claim that our model offers a complete view of all the processes involved. This is why we have dedicated a section in the Discussion to the various ways in which our simple CNN is incomplete as a model of reading. In this section we hint at the usage of recurrent connections, but the reviewer does an excellent job of highlighting the importance of top-down connections even in models focusing on early visual processes, which we are very happy to include in this section.

The presented model needs substantial further development to be able to replicate, both behaviorally and neurally, many of the well-characterized phenomena seen in human behavior and neural recordings that are fundamental hallmarks of human visual word processing. Until that point, it is unclear what novel contributions can be gleaned from correlating low-dimensional model weights from these computational models with human neural data.

The CNN model we present in this study is a small piece in a bigger effort to employ deep learning techniques to further enhance already existing models of reading. For our revision, we plan to expand on the question of where to go from here and outline our vision on how these techniques could help us better model the phenomena the reviewer speaks of. We agree with the reviewer that there is a long way to go, and we are excited to be a part of it.

Reviewer #3:

The paper is rather qualitative in nature. In particular, the authors show that some resemblance exists between the behavior of some layers and some parts of the brain, but it is hard to quantitively understand how strong the resemblances are in each layer, and the exact impact of experimental settings such as the frequency balancing (which seems to only have a very moderate effect according to Figure 5).

The large focus on a qualitative evaluation of the model is intentional. The ability of the model to reproduce experimental effects (Figure 4) is a pre-requisite for any subsequent qualitative metrics (such as correlation) to be valid. The introduction of frequency balancing is a good example of this. As the reviewer points out, frequency balancing during training has only a moderate impact on correlation scores and from that point of view does not seem impactful. However, when we look at the qualitative evaluation, we see that with a large vocabulary, a model without frequency balancing fails to properly distinguish between consonant strings and (pseudo)words (Figure 4, 5th row). Hence, from the point of view of being able to reproduce experimental effects, frequency balancing has a large impact.

That said, the reviewer is right to highlight the value of quantitative analysis. An important limitation of the "traditional" models of reading that do not employ deep learning is that they operate in unrealistically simplified environments (e.g. input as predefined line segments, words of a fixed length), which makes a quantitative comparison with brain data problematic. The main benefit that deep learning brings may very well be the increase in scale that makes more direct comparisons with brain data possible. In our revision we will attempt to capitalize on this benefit more. The reviewer has provided some helpful suggestions for doing so in their recommendations.

The experiments only consider a rather outdated vision model (VGG).

VGG was designed to use a minimal number of operations (convolution-and-pooling, fully-connected linear steps, ReLU activations, and batch normalization) and rely mostly on scale to solve the classification task. This makes VGG a good place to start our explorations and see how far a basic CNN can take us in terms of explaining experimental MEG effects in visual word recognition. However, we agree with the reviewer that it is easy to envision more advanced models that could potentially explain more. For our revision, we plan to expand on the question of where to go from here and outline our vision on what types of models would be worth investigating and how one may go about doing that in a way that provides insights beyond higher correlation values.

eLife assessment

This study provides useful insights for anyone focusing on exonic regions when looking into the investigation of DNA fragmentation patterns (fragmentomics) for circulating tumor DNA (ctDNA) data for cancer detection. The method expands the DELFI method of Cristiano and colleagues (2019), but the datasets chosen are not ideal and the analysis remains incomplete.

Reviewer #1 (Public Review):

Summary:

The authors are looking to assess fragmentomics effects using the Delfi method in exonic regions (Exome sequencing). They argue that this is to make the test more cost effective by extracting this information from exome sequencing.

Strengths:

Well written and explained. Different ML approaches tried.

Weaknesses:

To assess fragmentomics in WES, it doesn't seem valid to downsample WGS. WES is generated by a different library preparations so to answer this question, it would be necessary to try this in WES samples. The coverage of WES is generally done much higher because this is necessary to assess mutation calls therefore the approach of combining seems flawed because these were not generated by the same experiment.

The authors do not really show why they included longer fragment sizes in their model that had previously been excluded from the original Delfi publication

As a proof of concept this is a good idea but really needs a bit of a rethink on the utility and impact.

Reviewer #2 (Public Review):

Apiwat Sangphukieo et al. have developed machine learning models, exomeDELFI and xDELFI trained on 4 public datasets comprising 721 cfDNA samples. They demonstrate the exomeDELFI model utilizing DNA from whole exome, exhibits higher AUC values compared to the original DELFI model at equal whole-genome sequencing depth for distinguishing patients with and without cancer. Additionally, the xDELFI model, integrating coverage of overall fragments, fragments within 3 fragment size thresholds (short, medium, long) and fragment size distribution (FSD), resulting in 2,952 features, shows improved enhanced prediction performance. Furthermore, the authors have devised a multiclass machine learning model capable of classifying the tissue of origin for eight cancer types, using distinct tissue-specific fragmentomic patterns in cfDNA from whole-exome regions.

However, the conclusions drawn in this paper rely heavily on cross-validation of machine learning models constructed from hundreds of samples but employing thousands of features, posing a risk of overfitting. Thus, more rigorous validation is warranted.

(1) The claim in line 18 is misleading. The authors assert that the high cost of whole-genome sequencing (WGS) limited the application of cfDNA in clinic, and therefore imply their model are more cost-efficient by using fewer DNA molecules only originated from exosmic regions. However, WGS is essential in their analysis. Instead of using whole-exome sequencing data, they extracted DNA molecules from WGS data which fall within gene exome regions for feature extraction and downstream analysis, resulting in the same cost for DNA sequencing. In this regard, xDELFI, which selectively uses DNA from exomic regions, demonstrates inferior performance compared to the DELFI model using all WGS data (AUC: 0.896 vs. 0.920) at the same cost using same WGS data.

(2) The utilization of WGS data from 4 distinct datasets (Jiang et al., 2015, Snyder et al., 2016, Cristiano et al., 2019 and Sun et al., 2019) raises concerns about potential batch effects arising from different DNA library preparation kits (e.g., Kapa Library Preparation Kit (Kapa Biosystems); ThruPLEX DNA-seq kits (Rubicon Genomics); NEBNext DNA Library Prep Kit for Illumina (New England Biolabs); and KAPA HTP Library Preparation Kit (Kapa Biosystems), receptivity). Each kit may induce varying pre-analytical effects on cfDNA fragmentomic features, as evidenced by differing size distribution profiles (e.g., in Fig.4 in Jiang et al., 2015, the cfDNA size distribution profiles show the major peak at ~166 bp with frequency of ~3%. However, in Fig.1B in Snyder et al., 2016, the major peak at ~166 bp is ~2%). To enhance the robustness of their models, the authors should develop sophisticated normalization pipeline to mitigate batch effects and split training and testing sets without mixing any dataset. The author should demonstrate their model performs equally well between training and testing sets and across different datasets.

(3) The uneven distribution of cancer patients across different datasets introduces another layer of complexity, potentially confounding the analysis of tissue of origin. In line 300, the authors find that liver, colorectal, and lung cancers had the highest prediction accuracy in their models. However, the cancer patient distribution is not even across different datasets (e.g., liver cancer patients are all from Jiang et al., 2015; colorectal cancer patients are mostly from Sun et al., 2019, and Cristiano et al., 2019; and lung cancer patients are mainly from Cristiano et al., 2019. The potential pre-analytical differences in each dataset, coupled with overwhelming cancer types in each database, underscores the importance of addressing these discrepancies to ensure the validity of tissue of origin predictions.

(4) In Line 145, the authors mention selection of features used in the xDELFI model but did not specify the number of remaining features in each fragmentomic category post-selection. Providing this information would enhance the transparency and reproducibility of their methodology.

eLife assessment

Supported by solid evidence, this work provides valuable insights into theanine metabolism and regulation at single-cell resolution. The study paves the way for addressing the multicellular compartmentation of secondary metabolites in various plant systems, making it a valuable resource for future research.

Reviewer #1 (Public Review):

Summary:

The study used root tips from semi-hydroponic tea seedlings. The strategy followed sequential steps to draw partial conclusions.

Initially, protoplasts obtained from root tips were processed for scRNA-seq using the 10x Genomics platform. The sequencing data underwent pre-filtering at both the cell and gene levels, leading to 10,435 cells. These cells were then classified into eight clusters using t-SNE algorithms. The present study scrutinised cell typification through protein sequence similarity analysis of homologs of cell type marker genes. The analysis was conducted to ensure accuracy using validated genes from previous scRNA-seq studies and the model plant Arabidopsis thaliana. The cluster cell annotation was confirmed using in situ RT-PCR analyses. This methodology provided a comprehensive insight into the cellular differentiation of the sample under study. The identified clusters, spanning 1 to 8, have been accurately classified as xylem, epidermal, stem cell niche, cortex/endodermal, root cap, cambium, phloem, and pericycle cells.

Then, the authors performed a pseudo-time analysis to validate the cell cluster annotation by examining the differentiation pathways of the root cells. Lastly, they created a differentiation heatmap from the xylem and epidermal cells and identified the biological functions associated with the highly expressed genes.

Upon thoroughly analysing the scRNA-seq data, the researchers delved into the cell heterogeneity of nitrate and ammonium uptake, transport, and nitrogen assimilation into amino acids. The scRNA-seq data was validated by in situ RT-PCR. It allows the localisation of glutamine and alanine biosynthetic enzymes along the cell clusters and confirms that both constituent the primary amino acid metabolism in the root. Such investigation was deemed necessary due to the paramount importance of these processes in theanine biosynthesis since this molecule is synthesised from glutamine and alanine-derived ethylamine.

Afterwards, the authors analysed the cell-specific expression patterns of the theanine biosynthesis genes, combining the same molecular tools. They concluded that theanine biosynthesis is more enriched in cluster 8 "pericycle cells" than glutamine biosynthesis (Lines 271-272). However, the statement made in Line 250 states that the highest expression levels of genes responsible for glutamine biosynthesis were observed in Clusters 1, 3, 4, 6, and 8, leading to an unclear conclusion.

The regulation of theanine biosynthesis by the MYB transcription factor family is well-established. In particular, CsMYB6, a transcription factor expressed specifically in roots, has been found to promote theanine biosynthesis by binding to the promoter of the TSI gene responsible for theanine synthesis. However, their findings indicate that CsMYB6 expression is present in Cluster 3 (SCN), Cluster 6 (cambium cells), and Cluster 1 (xylem cells) but not in Cluster 8 (pericycle cells), which is known for its high expression of CsTSI. Similarly, their scRNA-seq data indicated that CsMYB40 and CsHHO3, which activate and repress CsAlaDC expression, respectively, did not show high expression in Cluster 1 (the cell cluster with high CsAlaDC expression). Based on these findings, the authors hypothesised that transcription factors and target genes are not necessarily always highly expressed in the same cells. Nonetheless, additional evidence is essential to substantiate this presumption.

Lastly, the authors have discovered a novel transcription factor belonging to the Lateral Organ Boundaries Domain (LBD) family known as CsLBD37 that can co-regulate the synthesis of theanine and the development of lateral roots. The authors observed that CsLBD37 is located within the nucleus and can repress the CsAlaDC promoter's activity. To investigate this mechanism further, the authors conducted experiments to determine whether CsLBD37 can inhibit CsAlaDC expression in vivo. They achieved this by creating transiently CsLBD37-silenced or over-expression tea seedlings through antisense oligonucleotide interference and generation of transgenic hairy roots. Based on their findings, the authors hypothesise that CsLBD37 regulates CsAlaDC expression to modulate the synthesis of ethylamine and theanine.

Additionally, the available literature suggests that the transcription factors belonging to the Lateral Organ Boundaries Domain (LBD) family play a crucial role in regulating the development of lateral roots and secondary root growth. Considering this, they confirmed that pericycle cells exhibit a higher expression of CsLBD37. A recent experiment revealed that overexpression of CsLBD37 in transgenic Arabidopsis thaliana plants led to fewer lateral roots than the wild type. From this observation, the researchers concluded that CsLBD37 regulates lateral root development in tea plants. I respectfully submit that the current conclusion may require additional research before it can be considered definitive.

Further efforts should be made to investigate the signalling mechanisms that govern CsLBD37 expression to arrive at a more comprehensive understanding of this process. In the context of Arabidopsis lateral root founder cells, the establishment of asymmetry is regulated by LBD16/ASL18 and other related LBD/ASL proteins, as well as the AUXIN RESPONSE FACTORs (ARF7 and ARF19). This is achieved by activating plant-specific transcriptional regulators such as LBD16/ASL18 (Go et al., 2012, https://doi.org/10.1242/dev.071928). On the other hand, other downstream homologues of LBD genes regulated by cytokinin signalling play a role in secondary root growth (Ye et al., 2021, https://doi.org/10.1016/j.cub.2021.05.036). It is imperative to shed light on the hormonal regulation of CsLBD37 expression in order to gain a comprehensive understanding of its involvement in the morphogenic process.

Strength:

The manuscript showcases significant dedication and hard work, resulting in valuable insights that serve as a fundamental basis for generating knowledge. The authors skillfully integrated various tools available for this type of study and meticulously presented and illustrated every step involved in the survey. The overall quality of the work is exceptional, and it would be a valuable addition to any academic or professional setting.

Weaknesses:

In its current form, the article presents certain weaknesses that need to be addressed to improve its overall quality. Specifically, the authors' conclusions appear to have been drawn in haste without sufficient experimental data and a comprehensive discussion of the entire plant. It is strongly advised that the authors devote additional effort to resolving the abovementioned issues to bolster the article's credibility and dependability. This will ensure that the article is of the highest quality, providing readers with reliable and trustworthy information.

Reviewer #2 (Public Review):

Summary:

In their manuscript, Lin et al. present a comprehensive single-cell analysis of tea plant roots. They measured the transcriptomes of 10,435 cells from tea plant root tips, leading to the identification and annotation of 8 distinct cell clusters using marker genes. Through this dataset, they delved into the cell-type-specific expression profiles of genes crucial for the biosynthesis, transport, and storage of theanine, revealing potential multicellular compartmentalization in theanine biosynthesis pathways. Furthermore, their findings highlight CsLBD37 as a novel transcription factor with dual regulatory roles in both theanine biosynthesis and lateral root development.

Strengths:

This manuscript provides the first single-cell dataset analysis of roots of the tea plants. It also enables detailed analysis of the specific expression patterns of the gene involved in theanine biosynthesis. Some of these gene expression patterns in roots were further validated through in-situ RT-PCR. Additionally, a novel TF gene CsLBD37's role in regulating theanine biosynthesis was identified through their analysis.

Weaknesses:

Several issues need to be addressed:

(1) The annotation of single-cell clusters (1-8) in Figure 2 could benefit from further improvement. Currently, the authors utilize several key genes, such as CsAAP1, CsLHW, CsWAT1, CsIRX9, CsWOX5, CsGL3, and CsSCR, to annotate cell types. However, it is notable that some of these genes are expressed in only a limited number of cells within their respective clusters, such as CsAAP1, CsLHW, CsGL3, CsIRX9, and CsWOX5. It would be advisable to utilize other marker genes expressed in a higher percentage of cells or employ a combination of multiple marker genes for more accurate annotation.

(2) Figure 3 could enhance clarity by displaying the trajectory of cell differentiation atop the UMAP, similar to the examples demonstrated by Monocle 3.

(3) The identification of CsLBD37 primarily relies on bulk RNA-seq data. The manuscript could benefit from elaborating on the role of the single-cell dataset in this context.

(4) The manuscript's conclusions predominantly rely on the expression patterns of key genes. This reliance might stem from the inherent challenges of tea research, which often faces limitations in exploring molecular mechanisms due to the lack of suitable genetic and molecular methods. The authors may consider discussing this point further in the discussion section.

Reviewer #3 (Public Review):

Summary:

Lin et al., performed a scRNA-seq-based study of tea roots, as an example, to elucidate the biosynthesis and regulatory processes for theanine, a root-specific secondary metabolite, and established the first map of tea roots comprised of 8 cell clusters. Their findings contribute to deepening our understanding of the regulation of the synthesis of important flavor substances in tea plant roots. They have presented some innovative ideas.

It is notable that the authors - based on single-cell analysis results - proposed that TFs and target genes are not necessarily always highly expressed in the same cells. Many of the important TFs they previously identified, along with their target genes (CsTSI or CsAlaDC), were not found in the same cell cluster. Therefore, they proposed a model in which the theanine biosynthesis pathway occurs via multicellular compartmentation and does not require high co-expression levels of transcription factors and their target genes within the same cell cluster. Since it is not known whether the theanine content is absolutely high in the cell cluster 1 containing a high CsAlaDC expression level (due to the lack of cell cluster theanine content determination, which may be a current technical challenge), it is difficult to determine whether this non-coexpressing cell cluster 1 is a precise regulatory mechanism for inhibiting theanine content in plants. In fact, there are actually a small number of cells where TFs and CsAlaDC are simultaneously highly expressed, but the quantity is insufficient to form a separate cluster. However, these few cells may be sufficient to meet the current demands for theanine synthesis. This possibility may better align with some previous experiments and validation results in this study. Moreover, I feel that under normal conditions, plants may not mobilize a large number of cells to synthesize a particular substance. Perhaps, cell cluster 1 is actually a type of cell that inhibits the synthesis of theanine, aiming to prevent excessive theanine production? I do not oppose the model proposed by the author, but I feel there is a possibility as I mentioned. If it seems reasonable, the author may consider adding it to an appropriate position in the discussion.