Author Response

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

Reviewer #1 (Recommendations For The Authors):

My main request is to show the phylogeny in the main text, so the reader knows what nodes are being compared.

Full phylogeny was added to the main text as Fig. 2. Additionally, phylogenetic tree in Newick format is presented as a Supplementary file 2.

I also suggest the authors check their figure legends carefully. At least in figure one, I think there is some mix-up with the letter labelling of the panels.

Our mistake. Figure legend was corrected. In this version of the manuscript Figure 1 was split into Fig. 1 and Fig. 3. Corrected version is presented in the legend to Fig. 3.

And lastly, I urge the authors to deposit the tree, alignment, and reconstructed sequences in a public repository.

Alignment in fasta format and phylogenetic tree in Newick format were added as supplementary files to the publication (supplementary file 1 and supplementary file 2, respectively). Reconstructed sequences (both Most likely and AltAll variants) were shown as a figure supplement (Figure 3 – figure supplement 2). Posterior probabilities for all positions of the reconstructed sequences were added as a supplementary file (supplementary file 3).

Reviewer #2 (Recommendations For The Authors):

-I find the term "secondarily single sHsp" to be a little confusing, especially because it is often used in relation to IbpA/B, but it is just IbpA in another species. I think it would be more clear for the reader to consistently refer to it as Erwiniaceae IbpA vs Escherichia IbpA, or something similar.

In the introduction we clarified (page 4 lines 11-13) that the term “secondarily single” IbpA refers to IbpA that lacks partner protein as a result of ibpB gene loss. This is in opposition to “single-protein” IbpA from a clade in which gene duplication leading to creation of two – protein sHsp system did not occur (like Vibrionaceae or Aeromonadaceae) - see Obuchowski et al., 2019.

-Figure 1B. The labels are not defined. What is L? A and B refer to IbpA and IbpB but this should be made more clear to the reader. Why is this panel only referred to in the Introduction and not the Results? Why is there a second panel for E.amy, rather than including it in the same panel, as for other experiments? What are the error bars? (That goes for every error bar in the paper, none are defined).

Labels in Fig.1B were corrected; “L” was used in reference to “luciferase alone” and it has been corrected for consistency to “no sHsp”. The sHsps activity measurements (obtained in the same experiment) were split into two separate panels as a correspondence to the two branches of the simplified tree in Fig. 1. The figure was modified to make it clearer and avoid confusion. Definitions of error bars were added to this and other figures.

-"AncA0 exhibited sequestrase activity on the level comparable to IbpA from Escherichia coli (IbpAE.coli). AncA1 was moderately efficient in this process and IbpA from Erwinia amylovora (IbpAE.amyl) was the least efficient sequestrase (Fig. 1D)." - First, this should be referring to Fig. 1C. Second, the text doesn't quite match the panel. A0 appears to have the strongest sequestrase activity over most concentrations. Can the authors comment on in what concentration range these differences are most meaningful?

Figure legend was corrected. Descriptions of panels C and D were fixed. Now these data are presented in panels A and B of a new Fig. 3. In our opinion differences in sequestration are most meaningful at lower sHsp concentrations (in this case lower than 5 µM), as with high enough sHsp concentration even less effective sequestrases seem to be able to effectively sequester aggregated proteins. Comment about it was added to the main text (page 5, line 6)

-"Ancestral proteins' interaction with the aggregated substrates was stronger than in the case of extant E. amylovora IbpA, but weaker than in the case of extant E. coli IbpA (Fig. 1C)." - Is this referring to Fig. 1C, or to the unlabelled panel on the bottom right panel of Fig 1 (that is not referred to in the legend)? Can the authors comment on why they think the 2 ancestral proteins are much more similar to each other than they are to either of the native IbpAs?

Due to our mistake descriptions of panels C and D were switched.

Figure 1 was rearranged and split into Figures 1 and 3. Former figure S1 (full phylogeny) was inserted into the main text, as Fig. 2, per request of reviewer #1. Former panel 1D (now 3B) was rearranged, as graph was not apparent to be a part of that panel and looked as if it was unlabeled.

The fact that the two ancestral proteins are more similar to each other than to the extant E. coli and E. amylovora proteins in their interaction with model substrate might be caused by higher sequence identity between the two ancestral proteins than between ancestral and extant proteins (10 amino acid differences between AncA0 and AncA1 compared to 20 differences between AncA1 and IbpA from E. amylovora or 11 differences between AncA0 and IbpA from E. coli). One also has to remember that this property is only one aspect of sHsp activity – proteins AncA0 and AncA1 are much less similar to each other if other activities such as sequestrase activity are considered. Substrate affinity and sequestrase activity are connected to each other, but there isn’t a strict correlation, as can be seen in the case of free ACD domains, which strongly bind aggregated substrate while effectively lacking sequestrase activity (fig. 5 A, fig. 5 – figure supplement 4 A,B).

-Figure 1E should have E. coli IbpA and IbpB, by themselves, included for comparison. Strangely, it seems, by comparison to Fig 1B, that the "inhibitory" activity of A0 is not present in the E. coli protein, and the authors should comment on this. Similarly, A1 disaggregation looks like it might not be significantly different than the E. coli protein. Can the authors comment on why disaggregation might be so low in A1 compared to E.amy?

E. coli IbpA alone was added to Fig. 1E (Fig. 3C in the new version) as suggested.

AncA1 indeed exhibits similar activity to extant IbpA from E. coli, which, at the conditions of the experiment, does not possess inhibitory effect observed for AncA0. This suggests that:

-There was an additional increase in ability to stimulate luciferase disaggregation between AncA1 and extant IbpA from E. amylovora

-There was also an increase of ability to stimulate luciferase refolding between AncA0 and extant E. coli IbpA, albeit to a significantly lesser degree than in the Erwiniaceae branch.

It is quite likely that after separation of Erwiniaceae and Enterobacteriaceae sHsp systems, they underwent further optimization through evolution. This might have led to observed higher effectiveness of modern IbpAs from both clades in refolding stimulation in comparison to the reconstructed ancestral proteins.

Despite the above, effects of substitutions on positions 66 and 109 on activities of the extant E. coli and E. amylovora proteins suggests that the two identified positions still play key role in differentiating extant IbpAs from Erwiniaceae and Enterobacteriaceae.

Nevertheless, additional mutations that lead to increased ability to stimulate luciferase reactivation must have occurred in both Erwiniaceae and Enterobacteriaceae branches of the phylogeny during evolution. These substitutions would be a worthwhile subject of further study.

-Fig 1D - lizate should be lysate.

The typo was corrected.

-What is the bottom right panel in Fig 1? It doesn't seem to be referred to in the legend.

This panel was intendent to be the part of figure 1D, but it was not clearly visible. This figure was rearranged to make it clearer. Now these data are presented as Fig. 3B.

-Sequences are provided for the ancestral proteins, but I don't see them anywhere for the alternative ancestral proteins. How similar are the Anc proteins to the AltAlls? If they are very similar, this may not tell us anything about "robustness".

Sequences of alternative proteins are added as a figure supplement (Fig. 3 - figure supplement 2). Full sequences of ML and alternative ancestors with posterior probabilities for each reconstructed position are presented in supplementary file 3

The testing of the robustness to statistical uncertainty was intended to test to what extent properties of reconstructed ancestral proteins could be influenced by uncertainty present in a given reconstruction due to probabilistic nature of the process. Relatively high similarity between ML and AltAll sequences would indicate low uncertainty of the reconstruction (most likely due to high conservation during evolution). In such a case similar properties of AltAll and ML proteins would simply indicate that they are robust to the level of uncertainty present in a given reconstruction (which may be low). It would not tell us much about “general” robustness to mutations, but it was not relevant to research questions considered.

-If the functional gain by IbpA comes down to only two amino acid substitutions, I'm not convinced this would be meaningfully reflected in any tests of positive selection.

After considering Reviewer #1’s comments about limitations of models used for selection analysis we added acknowledgment in the discussion (page 9, line 9 - 13) that results indicating positive selection in our dataset should not be considered conclusive (see answer to Reviewer #1’s public review below).

-The full MSA should be provided as supplemental material.

The full MSA in fasta format is presented in the supplementary file 1.

-For the aggregate binding panels in Figs 3 and 4, it would be helpful to show the native and ancestral proteins for comparison. I know this is a bit redundant, as they're present in Fig 1, but I find it hard to judge the scale of change. This is especially important because A0 and A1 are very similar in Fig 1, so I want to see what kind of difference the 2 mutations make.

Data presented in Fig. 3C (Fig. 5C in the new version) refer to the binding of α-crystallin domains (A0ACD and A0ACD Q66H G109D) and not full length sHsps to E. coli proteins aggregated on a BLI sensor. Our intention was to show the influence of the two crucial substitutions (Q66H G109D) on the properties of A0 ancestral α-crystallin domain.

Figure 4 (Fig. 6 in the new version) represent the effects of the substitutions on the identified positions 66 and 109 on the properties of extant IbpA orthologs from E. coli and E. amylovora, showing that these two positions play a key role in differentiating properties of those extant proteins. Changes in binding to aggregated substrate caused by those substitutions, as shown in Figure 6 B,C (new version), are indeed larger than observed between AncA0 and AncA1, as shown in Fig. 3B (new version).

One has to remember, however, that the experiment shown in Fig.3 (new version) shows the effects of all 10 amino acid changes between the nodes A0 and A1 and not only the two analyzed substitutions, as was the case in experiment shown in Fig. 6 B,C (new version). Moreover, due to relatively large number of differences between ancestral and extant sequences (11 differences between AncA0 and E. coli IbpA, 20 differences between AncA1 and E. amylovora IbpA), substitutions in the two experiments are introduced into different sequence context.

Because of the above, we believe that direct comparison of the results obtained for ancestral proteins with the results obtained for substitutions introduced into extant proteins would not meaningfully contribute to answering the question of the role of analyzed substitution in the context of extant proteins, while decreasing clarity of presented information.

-Some of the luciferase plots show a time course, but others just show a single %. What is the time point used for the single % plots?

Information was added to appropriate figure legends that for experiments showing a single timepoint the luciferase activity was measured after 1h of refolding.

Reviewer #3 (Recommendations For The Authors):

1. In the Introduction, it would be beneficial to explore additional instances where this evolutionary simplification process has been observed in nature. Investigating the prevalence of this phenomenon and identifying other multi-protein systems that have undergone simplification could enhance the understanding of its significance and implications.

The section of the introduction concerning gene loss and differential paralog retention was expanded with additional examples of gene loss that is considered adaptive (page 3 lines 1 - 12).

1. I am intrigued by the reasons why certain organisms continue to maintain a two-protein system despite the viability of a single-protein system. This aspect is particularly relevant for bacteria, considering the fitness cost associated with maintaining extra gene copies. Do you have any hypotheses or theories that may shed light on this intriguing observation?

Refolding of proteins from aggregates requires the functional cooperation of sHsps and chaperones from Hsp70 system and Hsp100 disaggregase. In two protein sHsps system one sHsp (IbpA) is specialized in substrate binding, while the second one (IbpB) possesses low substrate binding potential and enhances sHps dissociation from substrates (Obuchowski et al, 2019). Thus, the presence of IbpB reduces the amount of chaperones from Hsp70 system required to outcompete sHsps from aggregated substrates to initiate refolding process. The cost associated with maintaining extra sHsp gene copy (ibpB) in bacteria might be compensated by lower requirement for Hsp70 chaperones for efficient and fast protein refolding following stress conditions.

In this study we have demonstrated how such a system could have been simplified to a single – protein system capable of efficient substrate sequestration as well as stimulation of reactivation. This indeed leads to the question why such single – protein system isn’t more prevalent in Enterobacterales.

One possibility may be that there are very specific requirements for efficient reactivation by a single – protein sHsp system. We have shown that new, more efficient IbpA functionality observed in Erwiniaceae required at least two separate mutations. It is possible, that such combinations of two substitutions simply did not occur in Enterobacteriaceae clade, in which IbpA still required partner protein for efficient reactivation stimulation.

One must also remember that experiments performed in this study were performed in vitro in a specific set of conditions, which most likely does not represent whole spectrum of challenges faced by different bacteria. It is possible that two – protein system has some other additional adaptive effects, counterbalancing the additional cost of gene maintenance. It was for example recently shown (Miwa & Taguchi, PNAS, 120 (32) e2304841120) that bacterial sHsps play an important role in regulation of stress response. Two – protein system could potentially allow for more complex regulation.

1. Incorporating X-ray crystallization as an additional technique in the methodology would offer detailed molecular insights into the effects of Q66H and G109D substitutions on ACD-C-terminal peptide and ACD-substrate interactions. The inclusion of such data would further strengthen the results section and provide robust support for your findings. Since the x-ray data might be difficult to collect, the authors might think to get alphafold model or some rosetta score for the model to discuss the finding further.

In response to reviewer comment we added the comparison of the structural models of AncA0 and AncA0 Q66H G109D ACD dimers complexed with the C-terminal peptides, representing middle structures of largest clusters obtained from equilibrium molecular dynamics simulation trajectories based on the AlphaFold2 prediction and in silico mutagenesis (Fig. 5 – figure supplement 2). Model comparison as well as C-terminal peptide – ACD contact analysis did not reveal any major changes in mode of peptide binding or α-crystallin domain conformation, although we do acknowledge that simulation timescale limits the conformational sampling.

Reviewer #1 (Public Review):

The work in this paper is in general done carefully. Reconstructions are done appropriately and the effects of statistical uncertainty are quantified properly. My only slight complaint is that I couldn't find statistics about posterior probabilities anywhere and that the sequences and trees do not seem to be deposited.

Posterior probabilities for all positions of reconstructed proteins were added as a supplementary file 3. MSA of all sequences used for ancestral reconstruction as well as phylogenetic tree in Newick format were added as supplementary files 1 and 2, respectively.

I would also have preferred to have the actual phylogeny in the main text. This is a crucial piece of data that the reader needs to see to understand what exactly is being reconstructed.

Full phylogeny was added to the main text as Fig. 2.

The paper identifies which mutations are crucial for the functional differences between the ancestors tested. This is done quite carefully - the authors even show that the same substitutions also work in extant proteins. My only slight concern was the authors' explanation of what these substitutions do. They show that these substitutions lower the affinity of the C-terminal peptide to the alpha-crystallin domain - a key oligomeric interaction. But the difference is very small - from 4.5 to 7 uM. That seems so small that I find it a bit implausible that this effect alone explains the differences in hydrodynamic radius shown in Figure S8. From my visual inspection, it seems that there is also a noticeable change in the cooperativity of the binding interaction. The binding model the authors use is a fairly simple logarithmic curve that doesn't appear to consider the number of binding sites or potential cooperativity. I think this would have been nice to see here.

The binding model we used is equivalent to the Hill equation as it accounts for the variable slope of sigmoid function by inclusion of input scaling factor k, which is equivalent to the hill coefficient. Simple one site binding model and two site binding model were also considered but provided worse fits to the data than model including binding cooperativity. Not providing values of fitted parameter k was our mistake, and it was corrected (Fig. 5. with a legend). Additionally, output scaling parameter L is not necessary as fraction bound takes values from 0 to 1, therefore we have fitted the curves again without this parameter. The new values of fitted parameters are very similar to the previous ones. To make text more accessible to the reader, we have used a conventional form of Hill equation. Indeed, AncA0 Q66H G109D ACD displays higher binding cooperativity than more ancestral AncA0 ACD (hill coefficient 2.3 for AncA0 vs 3.7 for AncA0 Q66H G109D). Fitted values of Hill coefficients are higher than one can expect for 2-site ACD dimer, which is probably caused by an experimental setup of BLI, where C-terminal peptide is immobilized on the sensor and ACD is present in solution as bivalent analyte leading to emergence of avidity effects. Both cooperativity and avidity are reflected in the value of Hill coefficient, however as ligand density on the sensor is the same in all experiments only change in ACD binding cooperativity can account for observed difference in the value of Hill coefficients. Difference in the C-terminal peptide binding cooperativity may influence the process of sHsp oligomerization and assembly formation despite similar binding affinity, especially if avidity of multiple binding sites within oligomer is considered.

In addition, we changed the legend to Figure S8 (now called Fig. 5 – figure supplement 4A ) to clarify the fact that the differences in average hydrodynamic radius are in fact ferly small. To highlight the observation that there are two populations of particles in AncA0 and AncA0 Q66H G109D measured at 25, 35 and 45 °C with different hydrodynamic diameters, we used % of intensity in DLS measurement. It allows us to show the change in the hydrodynamic diameter distribution that is relatively small. We recognize it was not properly explained in the article and added a clarification in figure description.

Lastly, the authors use likelihood methods to test for signatures of selection. This reviewer is not a fan of these methods, as they are easily misled by common biological processes (see PMID 37395787 for a recent critique). Perhaps these pitfalls could simply be acknowledged, as I don't think the selection analysis is very important to the impact of the work.

We thank the reviewer for pointing to the recent research about limitations of methods used in our work in selection analysis. As per recommendation we added acknowledgment of limitations of methods used to discussion (page 9, line 9 - 13), modifying wording of our conclusions to deemphasize significance of selection analysis results.

Author Response:

We thank the editors and reviewers for their time in reviewing our manuscript. We would like to post a brief response to the peer reviews at this stage, and we will revise the manuscript and re-post at a later time.

The main concerns regarding our molecular dating approach consist of the limited number of marker genes used for phylogenetic reconstruction, the molecular clock model employed, and the calibrations used. Firstly, regarding the marker genes that we used in our phylogenetic reconstruction, we will point out that we have extensively benchmarked these methods in a previous study (Martinez-Gutierrez and Aylward, 2021). We initially planned on presenting all of these results together in the same manuscript, but we decided that benchmarking phylogenetic marker genes across all Bacteria and Archaea together with an extensive molecular dating analysis was too much for a single study, and we therefore divided the results into two papers. In short, we agree with R1 that the use of different marker genes will lead to marked differences in the posterior ages of our Bayesian molecular dating analysis; however, we demonstrated that several of the few marker genes shared between Bacteria and Archaea lack of a strong phylogenetic signal and therefore introduce topological biases in the final phylogeny (i.e., long branch attraction). Consequently, using poorly-performing marker genes for molecular dating does not add valuable information to the overall analysis.

Secondly, regarding the autocorrelated Log-normal model used in our study (-ln on Phylobayes), we believe this is appropriate. Besides being biologically meaningful for our study, it represents a compromise between a relaxed model with rate variation across branches and the assumption of correlation between parent and descent branches (Thorne et al., 1998). In contrast, a fully uncorrelated model that assumes rate independence across branches would make our analysis extremely time-consuming and intractable given our study encompasses all of Bacteria and Archaea. Nonetheless we understand the concerns raised, and in a future manuscript we will include age estimates resulting from the CIR and UGAM models in order to explore the potential effect of model selection in posterior dates.

Thirdly and lastly, we will point out that calibrations for molecular dating of Bacteria and Archaea are always highly controversial, and there are essentially no calibrations for the early evolution of life on Earth that would not be contested to some degree. Researchers are therefore left to use their best judgment and provide reasonable rationale, which we have done here. We understand that strong opinions abound in this area, and many researchers will disagree with our approach, but that alone does not invalidate our study. Moreover, the main novelty of our approach is the use of a large tree that combines Bacteria and Archaea; extensive benchmarking of different calibration points on such a large tree is not possible here as it may be on a smaller set. One of the main concerns is the use of the age estimate of the Great Oxidation Event (GOE, 2.4 Ga) as minimum and maximum constraints for oxygenic Cyanobacteria, and Ammonia Oxidizing Archaea and aerobic Marinimicrobia, respectively. We agree that oxygen may have existed before the GOE as proposed previously (e.g., Ostrander et al., 2021), however; the strongest geochemical evidence so far (Mass Independent Fractionation of Sulfur, MIFs, (Farquhar et al., 2000)) indicates a significant accumulation of oxygen around that time. We therefore feel that this is a reasonable calibration to use for microbial lineages that have a physiology that is tightly linked to the production or consumption of oxygen. Similar reasoning has been used in other molecular dating studies, so our logic is not out of step with much research in the field (Liao et al., 2022; Ren et al., 2019).

Due to the limitations of molecular dating studies of microorganisms, we have been very careful to avoid strong conclusions based on the absolute dates we calculated, and the primary interest of readers will likely be the relative divergence times of the marine clades we study (i.e., the overall timeline of microbial diversification in the ocean). We will provide a more in-depth assessment of models and calibrations for Bacteria and Archaea in a future draft, but in the meantime we hope to convey that our study is not without merit despite the substantial challenges of research in this area.

References:

• Farquhar J, Bao H, Thiemens M. 2000. Atmospheric influence of Earth’s earliest sulfur cycle. Science 289:756–759.
• Liao T, Wang S, Stüeken EE, Luo H. 2022. Phylogenomic Evidence for the Origin of Obligate Anaerobic Anammox Bacteria Around the Great Oxidation Event. Mol Biol Evol 39. doi:10.1093/molbev/msac170
• Martinez-Gutierrez CA, Aylward FO. 2021. Phylogenetic Signal, Congruence, and Uncertainty across Bacteria and Archaea. Mol Biol Evol 38:5514–5527.
• Ren M, Feng X, Huang Y, Wang H, Hu Z, Clingenpeel S, Swan BK, Fonseca MM, Posada D, Stepanauskas R, Hollibaugh JT, Foster PG, Woyke T, Luo H. 2019. Phylogenomics suggests oxygen availability as a driving force in Thaumarchaeota evolution. ISME J 13:2150–2161.
• Ostrander CM, Johnson AC, Anbar AD. 2021. Earth's first redox revolution. Annu Rev Earth Planet Sci. 49, 337-366.
• Thorne JL, Kishino H, Painter IS. 1998. Estimating the rate of evolution of the rate of molecular evolution. Mol Biol Evol 15:1647–1657.

Author Response

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

Thank you for your time and effort in handling and reviewing our manuscript. We have responded to all comments below.

Reviewer #1 (Public Review):

Martinez-Gutierrez and colleagues presented a timeline of important bacteria and archaea groups in the ocean and based on this they correlated the emergence of these microbes with GOE and NOE, the two most important geological events leading to the oxygen accumulation of the Earth. The whole study builds on molecular clock analysis, but unfortunately, the clock analysis contains important errors in the calibration information the study used, and is also oversimplified, leaving many alternative parameters that are known to affect the posterior age estimates untested. Therefore, the main conclusion that the oxygen availability and redox state of the ocean is the main driver of marine microbial diversification is not convincing.

We do not conclude that “oxygen availability and redox state of the ocean is the main driver of marine microbial diversification”. Our conclusion is much more nuanced. We merely discuss our findings in light of the major oxygenation events and oxygen availability (among other things) given the important role this molecule has played in shaping the redox state of the ocean.

Regarding the methodological concerns, to address them we have provided additional analyses to account for different clock models and calibration points.

Basically, what the molecular clock does is to propagate the temporal information of the nodes with time calibrations to the remaining nodes of the phylogenetic tree. So, the first and the most important step is to set the time constraints appropriately. But four of the six calibrations used in this study are debatable and even wrong.

(1) The record for biogenic methane at 3460 Ma is not reliable. The authors cited Ueno et al. 2006, but that study was based on carbon isotope, which is insufficient to demonstrate biogenicity, as mentioned by Alleon and Summons 2019.

Thank you for pointing out the limitations of using the geochemical evidence of methane as calibrations. Indeed, several commentaries have suggested that the biotic and abiotic origin of the methane reported by Ueno et al. are equally plausible (Alleon and Summons, 2019; Lollar and McCollom, 2006), however; we used that calibration as a minimum for the presence of life on Earth, not methanogenesis. Despite the controversy regarding the origin of methane, there are other lines of evidence suggesting the presence of life around ~3.4 Ga. For example stromatolites from the Dresser Formation, Pilbara, Western Australia (Djokic et al., 2017; Walter et al., 1980; Buick and Dunlop, 1990), and more recently (Hickman-Lewis et al., 2022). To avoid confusion, we have added a more extended explanation for the use of that calibration and additional evidence of life around that time in Table 1 and lines 100-104.

(2) Three calibrations at Aerobic Nitrososphaerales, Aerobic Marinimicrobia, and Nitrite oxidizing bacteria have the same problem - they are all assumed to have evolved after the GOE where the Earth started to accumulate oxygen in the atmosphere, so they were all capped at 2320 Ma. This is an important mistake and will significantly affect the age estimates because maximum constraint was used (maximum constraint has a much greater effect on age estimates and minimum constraint), and this was used in three nodes involving both Bacteria and Archaea. The main problem is that the authors ignored the numerous evidence showing that oxygen can be produced far before GOE by degradation of abiotically-produced abundant H2O2 by catalases equipped in many anaerobes, also produced by oxygenic cyanobacteria evolved at least 500 Ma earlier than the onset of GOE (2500 Ma), and even accumulated locally (oxygen oasis). It is well possible that aerobic microbes could have evolved in the Archaean.

We appreciate the suggestion of assessing the validity of the calibrations used in our analyses. We initially evaluated the informative power of the priors used for the Bayesian molecular dating (Supplemental File 5), and found that the only calibration that lacked enough information for the purposes of our study was Ammonia Oxidizing Archaea (AOA). In contrast to previous evidence (Ren et al., 2019; Yang et al., 2021), we associate this finding to the potential earlier diversification of AOA. Due to the limitations of several of the calibrations used, we performed an additional molecular dating analysis on 1000 replicate trees using a Penalized Likelihood strategy. This analysis consisted in excluding the calibrations that assumed the presence of oxygen as a maximum constraint. Our analysis shows similar age estimates of the marine microbial clades regardless of the exclusion of these calibrations (Supplemental File 8; TreePL Priors set 2). Our findings thus suggest that the age estimates reported in our study are consistent regardless of whether or not the presence of oxygen is used to calibrate several nodes in the tree. We describe the results of this analysis in lines 490-499 and include estimates in Supplemental File 8. Our results are therefore robust regardless of the use of these somewhat controversial calibrations.

Once the phylogenetic tree is appropriately calibrated with fossils and other time constraints, the next important step is to test different clock models and other factors that are known to significantly affect the posterior age estimates. For example, different genes vary in evolutionary history and evolutionary rate, which often give very different age estimates. So it is very important to demonstrate that these concerns are taken into account. These are done in many careful molecular dating studies but missing in this study.

We agree that the selection of marker genes will have a profound impact on the final age estimates. First, it is important to understand that very few genes present in modern Bacteria and Archaea can be traced back to the Last Universal Common Ancestor, so there are very few genes to use for this purpose. Studies that focus on particular groups of Bacteria and Archaea may have larger selections of genes to choose from, but for our purposes there are only about ~40 different genes - mostly encoding for ribosomal proteins, RNA polymerase subunits, and tRNA synthetases - that can be use for this purpose (Creevey et al., 2011; Wu and Scott, 2012). In a previous study we have extensively benchmarked methods for the reconstruction of high-resolution phylogenetic trees of Bacteria and Archaea using these genes (Martinez-Gutierrez and Aylward, 2021). Our analyses demonstrated that some of these genes (mainly tRNA synthetases) have undergone ancient lateral gene transfer events and are not suitable for deep phylogenetics or molecular dating. In this previous study we also evaluated different sets of marker genes to examine which provide the most robust phylogenetic inference. We arrived at a set of ribosomal proteins and RNA polymerase subunits that performs best for phylogenetic reconstruction, and we have used that in the current study.

Furthermore, we tested the role of molecular dating model selection on the final Bayesian estimates by running four independent chains under the models UGAM and CIR, respectively. Overall, the results did not vary substantially compared with the ages obtained using the log-normal model reported on our manuscript (Supplemental File 8). The additional results are described in lines 478-488 and shown in Supplemental File 8. The clades that showed more variation when using different Bayesian models were SAR86, SAR11, and Crown Cyanobacteria (Supplemental File 8). Despite observing some differences in the age estimates when using different molecular models, the conclusion that the different marine microbial clades presented in our study diversified during distinct periods of Earth’s history remains. Moreover, the main goal of our study is to provide a relative timeline of the diversification of abundant marine microbial clades without focusing on absolute dates.

Reviewer #2 (Public Review):

In this paper, Martinez-Gutierrez and colleagues present a dated, multidomain (= Archaea+Bacteria) phylogenetic tree, and use their analyses to directly compare the ages of various marine prokaryotic groups. They also perform ancestral gene content reconstruction using stochastic mapping to determine when particular types of genes evolved in marine groups.

Overall, there are not very many papers that attempt to infer a dated tree of all prokaryotes, and this is a distinctive and up-to-date new contribution to that oeuvre. There are several particularly novel and interesting aspects - for example, using the GOE as a (soft) maximum age for certain groups of strictly aerobic Bacteria, and using gene content enrichment to try to understand why and how particular marine groups radiated.

Thank you for your thorough evaluation and comments on our manuscript.

Comments

One overall feature of the results is that marine groups tend to be quite young, and there don't seem to be any modern marine groups that were in the ocean prior to the GOE. It might be interesting to study the evolution of the marine phenotype itself over time; presumably some of the earlier branches were marine? What was the criterion for picking out the major groups being discussed in the paper? My (limited) understanding is that the earliest prokaryotes, potentially including LUCA, LBCA and LACA, was likely marine, in the sense that there would not yet have been any land above sea level at such times. This might merit discussion in the paper. Might there have been earlier exclusively marine groups that went extinct at some point?

Thank you for pointing this out - this is a very interesting idea.<br /> Firstly, the major marine lineages that we study here have largely already been defined in previous studies and are known to account for a large fraction of the total diversity and biomass of prokaryotes in the ocean. For example, Giovannoni and Stingl described most of these groups previously when discussing cosmopolitan and abundant marine lineages (Giovannoni and Stingl, 2005). The main criteria to select the marine clades studied here are 1) these groups have large impacts in the marine biogeochemical cycles and represent a large fraction of the microbial biomass in the open ocean, 2) they have an appropriate representation on genomic databases such that they can be confidently included in a phylogenetic tree, 3) the clades included can be confidently classified as being marine, in the sense that consequently the last common ancestor had a marine origin. This is explained in lines 83-86. We were primarily interested in lineages that encompassed a broad phylogenetic breadth, and we therefore did not include many groups that can be found in the ocean but are also readily isolated from a range of other environments (i.e., Pseudomonas spp., some Actinomycetes, etc.).

We agree that some of the earlier microbial branches in the Tree of Life were likely marine. The study of the marine origin of LUCA, LBCA, LACA, although interesting, is out of the scope of our study, and our results cannot offer any direct evidence of their habitat. We have therefore sought to focus on the origins of extant marine lineages.

What do the stochastic mapping analyses indicate about the respective ancestors of Gracilicutes and Terrabacteria? At least in the latter case, the original hypothesis for the group was that they possessed adaptations to life on land - which seems connected/relevant to the idea of radiating into the sea discussed here - so it might be interesting to discuss what your analyses say about that idea.

Thank you for your recommendation to perform additional analysis regarding the characterization of the ancestor of the superphyla Gracilicutes and Terrabacteria. We agree that this analysis would be very interesting, but we wish to focus the manuscript primarily on the marine clades in question, and other supergroups are listed in Figure 2 mainly for context. However, we did check the results of the stochastic mapping analysis and we now report the list of genes predicted to be gained and lost at the ancestor of the Gracilicutes and Terrabacteria clades, however; it is out of the scope of this study.

I very much appreciate that finding time calibrations for microbes is challenging, but I nonetheless have a couple of comments or concerns about the calibrations used here:

The minimum age for LBCA and LACA (Nodes 1 and 2 in Fig. 1) was calibrated with the earliest evidence of biogenic methane ~3.4Ga. In the case of LACA, I suppose this reflects the view that LACA was a methanogen, which is certainly plausible although perhaps not established with certainty. However, I'm less clear about the logic of calibrating the minimum age of Bacteria using this evidence, as I am not aware that there is much evidence that LBCA was a methanogen. Perhaps the line of reasoning here could be stated more explicitly. An alternative, slightly younger minimum age for Bacteria could perhaps be obtained from isotope data ~3.2Ga consistent with Cyanobacteria (e.g., see https://pubmed.ncbi.nlm.nih.gov/30127539/).

Thank you for pointing this out. We used the presence of methane as a minimum for life on Earth, not as a minimum for methanogenesis. Despite using this calibration as a minimum for the root of Bacteria and not having methanogenic representatives within this domain, there are independent lines of evidence that point to the presence of microbial life around the same time (~3.5 Ga, for example stromatolites from the Dresser Formation, Pilbara, Western Australia (~3.5 Ga) (Djokic et al., 2017; Walter et al., 1980; Buick and Dunlop, 1990), and more recently (Hickman-Lewis et al., 2022). We added a rationale for the use of the evidence of methane as a minimum age for life on Earth to the manuscript (Table 1 and 100104).

I am also unclear about the rationale for setting the minimum age of the photosynthetic Cyanobacteria crown to the time of the GOE. Presumably, oxygen-generating photosynthesis evolved on the stem of (photosynthetic) Cyanobacteria, and it therefore seems possible that the GOE might have been initiated by these stem Cyanobacteria, with the crown radiating later? My confusion here might be a comprehension error on my part - it is possible that in fact one node "deeper" than the crown was being calibrated here, which was not entirely clear to me from Figure 1. Perhaps mapping the node numbers directly to the node, rather than a connected branch, would help? (I am assuming, based on nodes 1 and 2, that the labels are being placed on the branch directly antecedent to the node of interest)?

Thank you so much for your suggestion. As pointed out, the calibrations used were applied at the crown node of existing Cyanobacterial clades, not at the stem of photosynthetic Cyanobacteria. We agree that photosynthesis and therefore the production of molecular oxygen may have been present in more ancient Cyanobacterial clades, however; these groups have not been discovered yet or went extinct. We have improved Fig. 1 to avoid confusion and now it is part of the updated version of our manuscript.

Alleon J, Summons RE. 2019. Organic geochemical approaches to understanding early life. Free Radic Biol Med 140:103–112.

Buick R, Dunlop JSR. 1990. Evaporitic sediments of Early Archaean age from the Warrawoona Group, North Pole, Western Australia. Sedimentology 37: 247-277.

Creevey CJ, Doerks T, Fitzpatrick DA, Raes J, Bork P. 2011. Universally distributed single-copy genes indicate a constant rate of horizontal transfer. PLoS One 6:e22099.

Djokic T, Van Kranendonk MJ, Campbell KA, Walter MR, Ward CR. 2017. Earliest signs of life on land preserved in ca. 3.5 Ga hot spring deposits. Nat Commun 8:15263.

Giovannoni SJ, Stingl U. 2005. Molecular diversity and ecology of microbial plankton. Nature 437: 343-348. Hickman-Lewis K, Cavalazzi B, Giannoukos K, D'Amico L, Vrbaski S, Saccomano G, et al. 2023. Advanced two-and three-dimensional insights into Earth's oldest stromatolites (ca. 3.5 Ga): Prospects for the search for life on Mars. Geology 51: 33-38.

Lollar BS, McCollom TM. 2006. Geochemistry: biosignatures and abiotic constraints on early life. Nature. Martinez-Gutierrez CA, Aylward FO. 2021. Phylogenetic Signal, Congruence, and Uncertainty across Bacteria and Archaea. Mol Biol Evol 38:5514–5527.

Ren M, Feng X, Huang Y, Wang H, Hu Z, Clingenpeel S, Swan BK, Fonseca MM, Posada D, Stepanauskas R, Hollibaugh JT, Foster PG, Woyke T, Luo H. 2019. Phylogenomics suggests oxygen availability as a driving force in Thaumarchaeota evolution. ISME J 13:2150–2161.

Walter M R, R Buick, JSR Dunlop. 1980. Stromatolites 3,400–3,500 Myr old from the North pole area, Western Australia. Nature 284: 443-445.

Wu M, Scott AJ. 2012. Phylogenomic analysis of bacterial and archaeal sequences with AMPHORA2. Bioinformatics 28:1033–1034.

Yang Y, Zhang C, Lenton TM, Yan X, Zhu M, Zhou M, Tao J, Phelps TJ, Cao Z. 2021. The Evolution Pathway of Ammonia-Oxidizing Archaea Shaped by Major Geological Events. Mol Biol Evol 38:3637–3648.

Author Response

Reviewer #1 (Public Review):

Summary:

This work successfully identified and validated TRLs in hepatic metastatic uveal melanoma, providing new horizons for enhanced immunotherapy. Uveal melanoma is a highly metastatic cancer that, unlike cutaneous melanoma, has a limited effect on immune checkpoint responses, and thus there is a lack of formal clinical treatment for metastatic UM. In this manuscript, the authors described the immune microenvironmental profile of hepatic metastatic uveal melanoma by sc-RNAseq, TCR-seq, and PDX models. Firstly, they identified and defined the phenotypes of tumor-reactive T lymphocytes (TRLs). Moreover, they validated the activity of TILs by in vivo PDX modeling as well as in vitro co-culture of 3D tumorsphere cultures and autologous TILs. Additionally, the authors found that TRLs are mainly derived from depleted and late-activated T cells, which recognize melanoma antigens and tumor-specific antigens. Most importantly, they identified TRLs-associated phenotypes, which provide new avenues for targeting expanded T cells to improve cellular and immune checkpoint immunotherapy.

Strengths:

Jonas A. Nilsson, et al. has been working on new therapies for melanoma. The team has also previously performed the most comprehensive genome-wide analysis of uveal melanoma available, presenting the latest insights into metastatic disease. In this work, the authors performed paired sc-RNAseq and TCR-seq on 14 patients with metastatic UM, which is the largest single-cell map of metastatic UM available. This provides huge data support for other studies of metastatic UM.

We thank the reviewer for these kind words about our work.

Weaknesses:

Although the paper does have strengths in principle, the weaknesses of the paper are that these strengths are not directly demonstrated. That is, insufficient analyses are performed to fully support the key claims in the manuscript by the data presented. In particular：

The author's description of the overall results of the article should be logical, not just a description of the observed phenomena. For example, the presentation related to the results of TRLs lacked logic. In addition, the title of the article emphasizes the three subtypes of hepatic metastatic UM TRLs, but these three subtypes are not specifically discussed in the results as well as the discussion section. The title of the article is not a very comprehensive generalization and should be carefully considered by the authors.

We thank the reviewer for the critical reading of our work. We agree that there is need of more discussion and will do this in a revised version.

The authors' claim that they are the first to use autologous TILs and sc-RNAseq to study immunotherapy needs to be supported by the corresponding literature to be more convincing. This can help the reader to understand the innovation and importance of the methodology.

We will go through the manuscript and literature to see where there might be missing references.

In addition, the authors argue that TILs from metastatic UM can kill tumor cells. This is the key and bridging point to the main conclusion of the article. Therefore, the credibility of this conclusion should be considered. Metastatic UM1 and UM9 remain responsive to autologous tumors under in vitro conditions with their autologous TILs.

UM1 responds also in vivo in the subcutaneous model in the paper. We have also finished an experiment where we show that this model also responds in a liver metastasis model. These data will be added in next version of the paper.

In contrast, UM22, also as a metastatic UM, did not respond to TIL treatment. In particular, the presence of MART1-responsive TILs. The reliability of the results obtained by the authors in the model of only one case of UM22 liver metastasis should be considered. The authors should likewise consider whether such a specific cellular taxon might also exist in other patients with metastatic UM, producing an immune response to tumor cells. The results would be more comprehensive if supported by relevant data.

The reviewer has interpreted the results absolutely right, the allogenic and autologous MART1-specific TILs cells while reactive in vitro against UM22, cannot kill this tumor either in a subcutaneous or liver metastases model. We hypothesize this has to do with an immune exclusion phenotype and show weak immunohistochemistry that suggest this. We hope the addition of more UM1 data can be viewed as supportive of tumor-reactivity also in vivo.

In addition, the authors in that study used previously frozen biopsy samples for TCR-seq, which may be associated with low-quality sequencing data, high risk of outcome indicators, and unfriendly access to immune cell information. The existence of these problems and the reliability of the results should be considered. If special processing of TCR-seq data from frozen samples was performed, this should also be accounted for.

We agree with the reviewers and acknowledge we never anticipated the development of single-cell sequencing techniques when we started biobank 2013. We performed dead cell removal before the 10x Genomics experiment. We have also done extensive quality controls and believe that the data from the biopsies should be viewed as a whole and that quantitative intra-patient comparisons cannot be done.

Reviewer #2 (Public Review):

Summary:

The study's goal is to characterize and validate tumor-reactive T cells in liver metastases of uveal melanoma (UM), which could contribute to enhancing immunotherapy for these patients. The authors used single-cell RNA and TCR sequencing to find potential tumor-reactive T cells and then used patient-derived xenograft (PDX) models and tumor sphere cultures for functional analysis. They discovered that tumor-reactive T cells exist in activated/exhausted T cell subsets and in cytotoxic effector cells. Functional experiments with isolated TILs show that they are capable of killing UM cells in vivo and ex vivo.

Strengths:

The study highlights the potential of using single-cell sequencing and functional analysis to identify T cells that can be useful for cell therapy and marker selection in UM treatment. This is important and novel as conventional immune checkpoint therapies are not highly effective in treating UM. Additionally, the study's strength lies in its validation of findings through functional assays, which underscores the clinical relevance of the research.

We thank the reviewer for these kind words about our work.

Weaknesses:

The manuscript may pose challenges for individuals with limited knowledge of single-cell analysis and immunology markers, making it less accessible to a broader audience.

The first draft of the manuscript (excluding methods) was written by a person (J.A.N) who is not a bioinformatician. It has been corrected to include the correct nomenclature where applicable but overall it is written with the aim to be understandable. We will make an additional effort for the next version.

Author Response

The following is the authors’ response to the previous reviews

We would like to thank you again for your thorough review of the manuscript. We have taken all comments into account in the revised version of the manuscript. Please find below our detailed responses to your comments.

Reviewing Editor

The manuscript has been improved, but there are some remaining issues that need to be addressed, as outlined in the reviewers' comments. In particular, please pay attention to Figures 1A and 2A as they appear to be the same. Moreover, the original gel images for Western blots should be made available given the concerns raised by Reviewer #1.

Thank you for your recommendations. We have carefully considered all comments and made the requested revisions to improve the manuscript.

Reviewer #1 (Public Review):

In this manuscript, the authors aimed to compare, from testis tissues at different ages from mice in vivo and after culture, multiple aspects of Leydig cells. These aspects included mRNA levels, proliferation, apoptosis, steroid levels, protein levels, etc. A lot of work was put into this manuscript in terms of experiments, systems, and approaches. The technical aspects of this work may be of interest to labs working on the specific topics of in vitro spermatogenesis for fertility preservation.

Second review:

The authors should be commended for substantial improvement in their manuscript for resubmission.

Thank you very much for this second review and your help to improve this manuscript.

Recommendations For The Authors:

Going forward, the authors would be well-served to put a similar amount of effort on first drafts as well, which would both increase reviewer enthusiasm and reduce reviewer workload to document all the deficiencies! Abstract is much improved, and clearly articulates the point of the study.

We are very grateful for all your constructive comments, which have greatly contributed to the improvement of our manuscript.

1) 54 - replace "could be" with was

“could be” was replaced by “was”

2) 75 - delete "being"

“being” was deleted.

3) 103 - would say "indirectly promotes" since Rhox5 is a transcription factor that presumably activates genes in Sertoli cells whose products then affect neighboring germ cells, either by direct action or by influencing Sertoli cell behavior changes

“indirectly” was added in the sentence.

4) 139, 155, elsewhere - haven't seen dpp italicized before, certainly not the norm

In dpp (days post-partum), “pp” is italicized as it is a Latin word.

5) 265 - delete "found"

“found” was deleted.

6) 263-273 - Is the CYP19 protein referred to encoded by the Cyp19a1 gene (line 263)? Should standardize nomenclature...

The CYP19 protein (aromatase) is indeed encoded by the Cyp19a1 gene. The nomenclature was standardized: “CYP19” was replaced by “CYP19A1” in the entire manuscript.

7) 280 - "homolog" doesn't seem like the right word, as it has a very specific meaning with regards to the evolutionary genetic relatedness of genes. Maybe analog?

“homolog” was replaced by “analog”.

8) 306 - would reword to something like "proportions of seminiferous tubules containing round and elongating spermatids" - the because the tubules don't reach spermatid stages

This sentence was reworded as suggested.

9) 310 - delete "resulted in", unnecessary

“resulted in” was deleted.

10) Why are the images shown in Figures 1A and 2A the same? That seems odd - was that intentional? Curious overall why the data is presented in such a way that it's done twice...

We mistakenly presented immunofluorescence images twice. Duplicate images have been removed. In the modified version of this manuscript, Figure 1A shows 3-HSD immunofluorescence staining in cultures of fresh testicular tissues and in their in vivo counterparts while Figure 1 – figure supplement 1A (not Figure 2A) shows 3-HSD immunofluorescence staining in cultures of frozen/thawed testicular tissues.

11) In all the western blots, the cropping is done awfully close to the bands - why is this? Can full gels be shown in a Supplement? And especially in the westerns in Fig. 5C, esp for CYP17A1, the cropping is unacceptable. This reviewer is wondering whether this is an oversight, or whether there is another band below that one that is being masked? Again, should show whole blot for transparency and to ensure Rigor and Reproducibility.

Full gels are shown in the Supplementary File 2. For CYP17A1, we have shown that only one band of the expected molecular weight is obtained with the antibody (Please see photo below). After this verification, the nitrocellulose membranes were cut at the 55 kDa molecular weight band in order to reveal CYP17A1 expression in the upper part of the membranes and the protein used for normalization in the lower part of the membranes.

Author response image 1.

12) For all figures, wondering why the font sizes are so disparate? This will need to be addressed before publication so it looks more professional.

All figures have been reworked as requested.

Reviewer #3 (Public Review):

Moutard, Laura, et al. investigated the gene expression and functional aspects of Leydig cells in a cryopreservation/long-term culture system. The authors found that critical genetic markers for Leydig cells were diminished when compared to the in-vivo testis. The testis also showed less androgen production and androgen responsiveness. Although they did not produce normal testosterone concentrations in basal media conditions, the cultured testis still remained highly responsive to gonadotrophin exposure, exhibiting a large increase in androgen production. Even after the hCG-dependent increase in testosterone, genetic markers of Leydig cells remained low, which means there is still a missing factor in the culture media that facilitates proper Leydig cell differentiation. Optimizing this testis culture protocol to help maintain proper Leydig cell differentiation could be useful for future human testis biopsy cultures, which will help preserve fertility and child cancer patients.

Overall, the authors addressed most comments and questions from the previous review. The additional data regarding the necrotic area is helpful for interpreting the quality of the cultures. The authors did not conduct a multiple comparison tests although there are multiple comparisons conducted on for a single dependent variable (Fig 2J, Fig 3F, among many others), however, the addition of this multiple comparison is unlikely to change the conclusions of the paper or the figure and, thus is a minor technical detail in this case.

Thank you very much for this second review and your help to improve this manuscript.

Author Response

eLife assessment

This work describes new validated conditional double KO (cDKO) mice for LRRK1 and LRRK2 that will be useful for the field, given that LRRK2 is widely expressed in the brain and periphery, and many divergent phenotypes have been attributed previously to LRRK2 expression. The manuscript presents solid data demonstrating that it is the loss of LRRK1 and LRRK2 expression within the SNpc DA cells that is not well tolerated, as it was previously unclear from past work whether neurodegeneration in the LRRK double Knock Out (DKO) was cell autonomous or the result of loss of LRRK1/LRRK2 expression in other types of cells. Future studies may pursue the biochemical mechanisms underlying the reason for the apoptotic cells noted in this study, as here, the LRRK1/LRRK2 KO mice did not replicate the dramatic increase in the number of autophagic vacuoles previously noted in germline global LRRK1/LRRK2 KO mice.

We thank the editors for handling our manuscript and for the succinct summary that recognizes the significance of our findings and points out interesting directions for future studies. We also thank the reviewers for their helpful comments and positive evaluation of our work. Below, we have provided point-by-point responses to the reviewers’ comments.

Reviewer #1 (Public Review):

Summary:

This is an important work showing that loss of LRRK function causes late-onset dopaminergic neurodegeneration in a cell-autonomous manner. One of the LRRK members, LRRK2, is of significant translational importance as mutations in LRRK2 cause late-onset autosomal dominant Parkinson's disease (PD). While many in the field assume that LRRK2 mutant causes PD via increased LRRK2 activity (i.e., kinase activity), it is not a settled issue as not all disease-causing mutant LRRK2 exhibit increased activity. Further, while LRRK2 inhibitors are under clinical trials for PD, the consequence of chronic, long-term LRRK2 inhibition is unknown. Thus, studies evaluating the long-term impact of LRRK deficit have important translational implications. Moreover, because LRRK proteins, particularly LRRK2, are known to modulate immune response and intracellular membrane trafficking, the study's results and the reagents will be valuable for others interested in LRRK function.

Strengths:

This report describes a mouse model where the LRRK1 and LRRK2 gene is conditionally deleted in dopaminergic neurons. Previously, this group showed that while loss of LRRK2 expression does not cause brain phenotype, loss of both LRRK1 and LRRK2 causes a later onset, progressive degeneration of catecholaminergic neurons and dopaminergic (DAergic) neurons in the substantia nigra (SN), and noradrenergic neurons in the locus coeruleus (LC). However, because LRRK genes are widely expressed with some peripheral phenotypes, it was unknown if the neurodegeneration in the LRRK double knockout (DKO) was cell autonomous. To rigorously test this question, the authors have generated a double conditional (cDKO) allele where both LRRK1 and LRRK2 genes were targeted to contain loxP sites. In my view, this was beyond what is usually required, as most investigators might might combine one KO allele with another floxed allele. The authors provide a rigorous validation showing that the Driver (DAT-Cre) is expressed in most DAergic neurons in the SN and that LRRK levers are decreased selectively in the ventral midbrain. Using these mice, the authors show that the number of DAergic neurons is normal at 15 but significantly decreased at 20 months of age. Moreover, the authors show that the number of apoptotic neurons is increased by ~2X in aged SN, demonstrating increased ongoing cell death, as well as an increase in activated microglia. The degeneration is limited to DAergic neurons as LC neurons are not lost as this population does not express DAT. Overall, the mouse genetics and experimental analysis were performed rigorously, and the results were statistically sound and compelling.

Weaknesses:

I only have a few minor comments. First is that in PD and other degenerative conditions, loss of axons and terminals occurs prior to cell bodies. It might be beneficial to show the status of DAergic markers in the striatum. Second, previous studies indicate that very little, if any, LRRK1 is expressed in SN DAergic neurons. This also the case with the Allen Brain Atlas profile. Thus, authors should discuss the discrepancy as authors seem to imply significant LRRK1 expression in DA neurons.

We appreciate the reviewer’s recognition of the importance of the study as well as our rigorous experimental approaches and compelling results. Our responses to the reviewer's two minor comments are below.

1) DAergic markers in the striatum:

We performed TH immunostaining in the striatum and quantified TH+ DA terminals in the striatum of DA neuron-specific LRRK cDKO and littermate control mice at the ages of 15 and 24 months. We found similar levels of TH immunoreactivity in the striatum of LRRK cDKO and littermate control mice at the age of 15 months (p = 0.6565, unpaired Student’s t-test) and significantly reduced levels of TH immunoreactivity in the striatum of LRRK cDKO, compared to control mice at the age of 24 months (~19%, p = 0.0215), suggesting an age-dependent loss of dopaminergic terminals in the striatum of DA neuron-specific LRRK cDKO mice. These results are now included as Figure 5 of the revised manuscript.

2) LRRK1 expression in the SNpc:

It is shown in the Mouse brain RNA-seq dataset and the Allen Mouse brain ISH dataset (https://www.proteinatlas.org/ENSG00000154237-LRRK1/brain) that LRRK1 is broadly expressed in the mouse brain and is expressed at modest levels in the midbrain, comparable to the cerebral cortex. Indeed, our Western analysis also showed that levels of LRRK1 detected in the dissected ventral midbrain and the cerebral cortex of control mice are similar (40µg total protein loaded per lane; Figure 2E). Furthermore, we previously demonstrated that deletion of LRRK2 (or LRRK1) alone does not cause age-dependent loss of DA neurons in the SNpc, but deletions of both LRRK1 and LRRK2 result in age-dependent loss of DA neurons in LRRK DKO mice, indicating the functional importance of LRRK1 in the protection of DA neuron survival in the aging mouse brain (Tong et al., PNAS 2010, 107: 9879-9884, Giaime et al., Neuron 2017, 96: 796-807).

Reviewer #2 (Public Review):

Summary:

In this manuscript, Shen and collaborators described the generation of cDKO mice lacking LRRK1 and LRRK2 selectively in DAT-positive DAergic neurons. The Authors asked whether selective deletion of both LRRK isoforms could lead to a Parkinsonian phenotype, as previously reported by the same group in germline double LRRK1 and LRRK2 knockout mice (PMID: 29056298). Indeed, cDKO mice developed a late reduction of TH+ neurons in SNpc that partially correlated with the reduction of NeuN+ cells. This was associated with increased apoptotic cell and microglial cell numbers in SNpc.

Unlike the constitutive DKO mice described earlier, however, cDKO mice did not replicate the dramatic increase in the number of autophagic vacuoles. The study supports the authors' hypothesis that loss of function rather than gain of function of LRRK2 leads to PD.

Strengths:

The study described for the first time a model where both the PD-associated gene LRRK2 and its homolog LRRK1 are deleted selectively in DAergic neurons, offering a new tool to understand the physiopathological role of LRRK2 and the compensating role of LRRK1 in modulating DAergic cell function.

Weaknesses:

The model has no construct validity since loss of function mutations of LRRK2 are well-tolerated in humans and do not lead to PD. The evidence of a Parkinsonian phenotype in these cDKO mice is limited and should be considered preliminary.

We thank the reviewer for commenting on the usefulness of this new PD mouse model.

The reviewer did not include a reference citation for the statement "loss of function mutations of LRRK2 are well-tolerated in humans and do not lead to PD." It is possible that the reviewer was referring to a human population study (Whiffin et al., Nat Med 2020, 26: 869-877), entitled "The effect of LRRK2 lossof-function variants in humans." In this study, the authors analyzed 141,456 individuals sequenced in the Genome Aggregation Database, 49,960 exome-sequenced individuals from the UK Biobank, and more than 4 million participants in the 23andMe genotyped dataset, and they looked for human genetic variants predicted to cause loss-of-function of protein-coding genes (pLoF variants). The reported findings were interesting, and the authors were careful in stating their conclusions. However, this is not a linkage study of large pedigrees carrying a single, clear-cut loss-of-function mutation (e.g. large deletions of most exons and coding sequences). Therefore, the experimental evidence is not compelling enough to conclude whether loss-of-function mutations in LRRK2 cause PD or do not cause PD.

The current report is an unbiased genetic study in an effort to reveal the normal physiological role of LRRK in dopaminergic neurons. It was not intended to produce Parkinsonian phenotypes in LRRK cDKO mice, which would be a biased effort. However, the unequivocal discovery of the cell intrinsic role of LRRK in the protection of DA neurons from age-dependent degeneration and apoptotic cell death should be considered seriously, while we contemplate the disease mechanism and how LRRK2 mutations may cause DA neuron loss and PD.

Reviewer #3 (Public Review):

Kang, Huang, and colleagues investigated the impact of LRRK1 and LRRK2 deletion, specifically in dopaminergic neurons, using a novel cDKO mouse model. They observed a significant reduction in DAergic neurons in the substantia nigra in their conditional LRRK1 and LRRK2 KO mice and a corresponding increase in markers of apoptosis and gliosis. This work set out to address a longstanding question within the field around the role and importance of LRRK1 and LRRK2 in DAergic neurons and suggests that the loss of both proteins triggers some neurodegeneration and glial activation.

The studies included in this work are carefully performed and clearly communicated, but additional studies are needed to strengthen further the authors' claims around the consequences of LRRK2 deletion in DAergic neurons.

1. In Figures 2E and F, the authors assess the protein levels of LRRK1 and LRRK2 in their cDKO mouse model to confirm the deletion of both proteins. They observe a mild loss of LRRK1 and LRRK2 signals in the ventral midbrain compared to wild-type animals. While this is not surprising given other cell types that still express LRRK1 and LRRK2 would be present in their dissected ventral midbrain samples, it does not sufficiently confirm that LRRK1 and LRRK2 are not expressed in DAergic neurons. Additional data is needed to more directly demonstrate that LRRK1 and LRRK2 protein levels are reduced in DAergic neurons, including analysis of LRRK1 and LRRK2 protein levels via immunohistochemistry or FACS-based analysis of TH+ neurons.

We thank the reviewer for highlighting this incredibly important but often overlooked issue. We agree that the data in Figure 2E, F alone would be inadequate to validate DA neuron-specific LRRK cDKO mice.

Cell type-specific conditional knockouts are a mosaic with KO cells mixed with other cell types expressing the gene normally. DA neuron-specific cDKO is particularly challenging, as DA neurons are a subset of cells embedded in the ventral midbrain. Rather than using immunostaining, which relies upon specific, good LRRK1 and LRRK2 antibodies for IHC, or FACS sorting of TH+ neurons followed by Western blotting (few cells, mixed cell populations, etc.), we chose a clean genetic approach by generating germline mutant mice carrying the deleted LRRK1 and LRRK2 alleles in all cells from the floxed LRRK1 and LRRK2 alleles. This approach permits characterization of these deletion mutations in germline mutant mice using molecular approaches that yield unambiguous results.

We crossed CMV-Cre deleter mice with floxed LRRK1 and LRRK2 mice to generate respective germline LRRK1 KO and LRRK2 KO mice, in which all cells carry the LRRK1 or LRRK2 deleted alleles that are identical to those in DA neurons of cDKO mice. We then performed Northern, extensive RTPCR followed by sequencing, and Western analyses to show the absence of the full length LRRK1 and LRRK2 mRNA (Figure 1G, H, Figure 1-figure supplement 8 and 10), and the expected truncation of LRRK1 and LRRK2 mRNA (Figure 1-figure supplement 9 and 11), and the absence of LRRK1 and LRRK2 proteins (Figure 1I). These analyses together demonstrate that in the presence of Cre, either CMV-Cre expressed in all cells or DAT-Cre expressed selectively in DA neurons, the floxed LRRK1 and LRRK2 exons are deleted, resulting in null alleles. We further demonstrated the specificity of DAT-Cremediated recombination (deletion) by crossing DAT-Cre mice with a GFP reporter, showing that 99% TH+ DA neurons in the SNpc are also GFP+ (Figure 2A, B), indicating that DAT-Cre-mediated recombination of the floxed alleles occurs in essentially all TH+ DA neurons in the SNpc.

1. The authors observed a significant but modest effect of LRRK1 and LRRK2 deletion on the number of TH+ neurons in the substantia nigra (12-15% loss at 20-24 months of age). It is unclear whether this extent of neuron loss is functionally relevant. To strengthen the impact of these data, additional studies are warranted to determine whether this translates into any PD-relevant deficits in the mice, including motor deficits or alterations in alpha-synuclein accumulation/aggregation.

Yes, the reduction of DA neurons in the SNpc of cDKO mice at the age of 20-24 months is modest. At 15 months of age, the number of TH+ DA neurons in the SNpc is similar between LRRK cDKO mice (10,000 ± 141) and littermate controls (10,077 ± 310, p > 0.9999). At 20 months of age, the number of DA neurons in the SNpc of LRRK cDKO mice (8,948 ± 273) is significantly reduced (-12.7%), compared to control mice (10,244 ± 220, F1,46 = 16.59, p = 0.0002, two-way ANOVA with Bonferroni’s post hoc multiple comparisons, p = 0.0041). By 24 months of age, the number of DA neurons in the SNpc of LRRK cDKO mice (8,188 ± 452) relative to controls (9,675 ± 232, p = 0.0010) is further reduced (15.4%).

Similar results were obtained by an independent quantification by another investigator, also conducted in a genotype blind manner, using the fractionator and optical dissector method, by which TH+ cells were quantified in 25% areas. These results are included as Figure 3-figure supplement 1 in the revised manuscript. Because of the more limited sampling, the quantification data are more variable, compared to quantification of TH+ cells in all areas of the SNpc, shown in Figure 3. With both methods, we quantified TH+ cells in every 10th sections encompassing the entire SNpc (3D structure), as sampling using every 5th or every 10th sections yielded similar results.

We also performed behavioral analysis of LRRK cDKO mice and littermate controls at the ages of 10 and 25 months using the beam walk test (10 mm and 20 mm beam) and the pole test, which are sensitive to impairment of motor coordination. We found that LRRK cDKO mice at 10 months of age showed significantly more hindlimb errors (p = 0.0005, unpaired two-tailed Student’s t-test) and longer traversal time (p = 0.0075) in the 10mm beam walk test, compared to control mice, though their performance is similar in the 20 mm beam walk (hindlimb slips: p = 0.0733, traversal time: p = 0.9796) and in the pole test. At 22 months of age, the performance of LRRK cDKO mice and littermate controls is more variable and worse, compared to the younger mice, and is not significantly different between the genotypic groups. These results are now included as Figure 9 of the revised manuscript.

1. The authors demonstrate that, unlike in the germline LRRK DKO mice, they do not observe any alterations in electron-dense vacuoles via EM. Given their data showing increased apoptosis and gliosis, it remains unclear how the loss of LRRK proteins leads to DAergic neuronal cell loss. Mechanistic studies would be insightful to understand better potential explanations for how the loss of LRRK1 and LRRK2 may impair cellular survival, and additional text should be added to the discussion to discuss potential hypotheses for how this might occur.

We agree that this phenotypic difference between germline DKO and DA neuron-specific cDKO mice is intriguing, suggesting a non-cell autonomous contribution of LRRK in age-dependent accumulation of autophagic and lysosomal vacuoles in SNpc neurons of germline LRRK DKO mice. We will discuss the phenotypic difference further in the revised manuscript. We are generating microglial specific LRRK cDKO mice to investigate the role of LRRK in microglia and whether microglia contribute in a cell extrinsic manner to the regulation of the autophagy-lysosomal pathway in DA neurons.

1. The authors discuss the potential implications of the neuronal cell loss observed in cDKO mice for LRRK1 and LRRK2 for therapeutic approaches targeting LRRK2 and suggest this argues that LRRK2 variants may exert their effects through a loss-of-protein function. However, all of the data generated in this work focus on a mouse in which both LRRK1 and LRRK2 have been deleted, and it is therefore difficult to make any definitive conclusions about the consequences of specifically targeting LRRK2. The authors note potential redundancy between the two LRRK proteins, and they should soften some of their conclusions in the discussion section around implications for the effects of LRRK2 variants. Human subjects that carry LRRK2 loss-of-function alleles do not have an increased risk for developing PD, which argues against the author's conclusions that LRRK2 variants associated with PD are loss-offunction. Additional text should be included in their discussion to better address these nuances and caution should be used in terms of extrapolating their data to effects observed with PD-linked variants in LRRK2.

We will modify the discussion accordingly in the revised manuscript.

Author Response

Reviewer #1 (Public Review):

Weaknesses: There appears to be a lack of basic knowledge of the process of spermatogenesis. For instance, the statement that "During the first week of postnatal life, a population of SCs continues to proliferate to give rise to undifferentiated Asingle (As), Apaired (Apr) and Aaligned (Aal) cells. The remaining SCs differentiate to form chains of daughter cells that become primary and secondary permatocytes around postnatal day (PND) 10 to 12." is inaccurate. The Aal cells are the spermatogonial chains, the two are not distinct from one another. In addition, the authors fail to mention spermatogonial stem cells which form the basis for steady-state spermatogenesis. The authors also do not acknowledge the well-known fact that, in the mouse, the first wave of spermatogenesis is distinct from subsequent waves. Finally, the authors do not mention the presence of both undifferentiated spermatogonia (aka - type A) and differentiating spermatogonia (aka - type B). The premise for the study they present appears to be the implication that little is known about the dynamics of chromatin during the development of spermatogonia. However, there are published studies on this topic that have already provided much of the information that is presented in the current manuscript.

We acknowledge the reviewer’s criticism about the inaccuracy and incompleteness of some of the statements about spermatogonial cells and spermatogenesis. We will be improve the text accordingly in the reviewed manuscript. We will also clarify the premise of the study which was to complement existing datasets on spermatogonial cells by providing parallel transcriptomic and chromatin accessibility maps of high resolution from the same cell populations at early postnatal, late postnatal and adult stages collected from single individuals (for adults). These features make our datasets comprehensive and an important additional resource for people in the community. We will also revise the description of published studies to be more inclusive.

It is not clear which spermatogonial subtype the authors intended to profile with their analyses. On the one hand, they used PLZF to FACS sort cells. This typically enriches for undifferentiated spermatogonia. On the other hand, they report detection in the sorted population of markers such as c-KIT which is a well-known marker of differentiating spermatogonia, and that is in the same population in which ID4, a well-known marker of spermatogonial stem cells, was detected. The authors cite multiple previously published studies of gene expression during spermatogenesis, including studies of gene expression in spermatogonia. It is not at all clear what the authors' data adds to the previously available data on this subject.

The authors analyzed cells recovered at PND 8 and 15 and compared those to cells recovered from the adult testis. The PND 8 and 15 cells would be from the initial wave of spermatogenesis whereas those from the adult testis would represent steady-state spermatogenesis. However, as noted above, there appears to be a lack of awareness of the well-established differences between spermatogenesis occurring at each of these stages.

The reviewer correctly points that our samples contain both undifferentiated spermatogonial stem cells and differentiated spermatogonia, which is expected from the chosen FACS strategy. We clearly mention the fact that our populations are mixed and that our samples are 85-95% PLZF+ enriched. We also acknowledge the possible presence of contaminating cells that may influence the results and data interpretation in the section “Limitations”. We believe that this does not diminish the value of the datasets. But to further increase their usefulness and improve their interpretation, we will conduct new analyses and apply computational methods to deconvolute our bulk RNA-seq datasets in silico (PMID: 37528411) using publicly available single-cell RNA-seq datasets. Such analyses shall correct for cell-type heterogeneity and provide information about the cellular composition of our cell preparations clarifying the representation of undifferentiated and differentiated spermatogonial cells and the possible presence of somatic cells.

In general, the authors present observational data of the sort that is generated by RNA-seq and ATAC-seq analyses, and they speculate on the potential significance of several of these observations. However, they provide no definitive data to support any of their speculations. This further illustrates the fact that this study contributes little if any new information beyond that already available from the numerous previously published RNA-seq and ATAC-seq studies of spermatogenesis. In short, the study described in this manuscript does not advance the field.

We acknowledge that RNA-seq and ATAC-seq datasets like ours are observational and that their interpretation can be speculative. Nevertheless, our datasets represent an additional useful resource for the community because they are comprehensive and high resolution, and can be exploited for instance, for studies in environmental epigenetics and epigenetic inheritance examining the immediate and long-term effects of postnatal exposure and their dynamics. The depth of our RNA sequencing allowed detect transcripts with a high dynamic range, which has been limited with classical RNA sequencing analyses of spermatogonial cells and with single-cell analyses (which have comparatively low coverage). Further, our experimental pipeline is affordable (more than single cell sequencing approaches) and in the case of adults, provides data per animal informing on the intrinsic variability in transcriptional and chromatin regulation across males. These points will be discussed in the revised manuscript.

The phenomenon of epigenetic priming is discussed, but then it seems that there is some expression of surprise that the data demonstrate what this reviewer would argue are examples of that phenomenon. The authors discuss the "modest correspondence between transcription and chromatin accessibility in SCs." Chromatin accessibility is an example of an epigenetic parameter associated with the primed state. The primed state is not fully equivalent to the actively expressing state. It appears that certain histone modifications along with transcription factors are critical to the transition between the primed and actively expressing states (in either direction). The cell types that were investigated in this study are closely related spermatogenic, and predominantly spermatogonial cell types. It is very likely that the differentially expressed loci will be primed in both the early (PND 8 or 15) and adult stages, even though those genes are differentially expressed at those stages. Thus, it is not surprising that there is not a strict concordance between +/- chromatin accessibility and +/- active or elevated expression.

The reviewer is right that a strict concordance between chromatin accessibility and transcription is not necessarily expected. The text of the revised manuscript will be modified accordingly. However, we would like to note that our data strengthen the observations made by others that in cells from the same lineage, the global landscape of chromatin accessibility is more stable than their transcriptional programs over developmental time.

Reviewer #2 (Public Review):

The objective of this study from Lazar-Contes et al. is to examine chromatin accessibility changes in "spermatogonial cells" (SCs) across testis development. Exactly what SCs are, however, remains a mystery. The authors mention in the abstract that SCs are undifferentiated male germ cells and have self-renewal and differentiation activity, which would be true for Spermatogonial STEM Cells (SSCs), a very small subset of total spermatogonia, but then the methods they use to retrieve such cells using antibodies that enrich for undifferentiated spermatogonia encompass both undifferentiated and differentiating spermatogonia. Data in Fig. 1B prove that most (85-95%) are PLZF+, but PLZF is known to be expressed both by undifferentiated and differentiating (KIT+) spermatogonia (Niedenberger et al., 2015; PMID: 25737569). Thus, the bulk RNA-seq and ATAC-seq data arising from these cells constitute the aggregate results comprising the phenotype of a highly heterogeneous mixture of spermatogonia (plus contaminating somatic cells), NOT SSCs. Indeed, Fig. 1C demonstrates this by showing the detection of Kit mRNA (a well-known marker of differentiating spermatogonia - which the authors claim on line 89 is a marker of SCs!), along with the detection of markers of various somatic cell populations (albeit at lower levels).

The reviewer is correct that our spermatogonial cell populations are mixed and include undifferentiated and differentiated cells, hence the name of spermatogonia (SCs), and probably also contain some somatic cells. We acknowledge that this is a limitation of our isolation approach. To circumvent this limitation, we will conduct in silico deconvolution analysis using publicly available single cell RNA sequencing datasets to obtain information about markers corresponding to undifferentiated and differentiated spermatogonia cells, and somatic cells. These additional analyses will provide information about the cellular composition of the samples and clarify the representation of undifferentiated and differentiated spermatogonial cells and other cells.

This admixture problem influences the results - the authors show ATAC-seq accessibility traces for several genes in Fig. 2E (exhibiting differences between P15 and Adult), including Ihh, which is not expressed by spermatogenic cells, and Col6a1, which is expressed by peritubular myoid cells. Thus, the methods in this paper are fundamentally flawed, which precludes drawing any firm conclusions from the data about changes in chromatin accessibility among spermatogonia (SCs?) across postnatal testis development.

The reviewer raises concern about the lack of correspondence between chromatin accessibility and expression observed for some genes, arguing that this precludes drawing firm conclusions. However, a dissociation between chromatin accessibility and gene expression is normal and expected since chromatin accessibility is only a readout of protein deposition and occupancy e.g. by transcription factors, chromatin regulators, nucleosomes, at specific genomic loci that does not give functional information of whether there is ongoing transcriptional activity or not. A gene that is repressed or poised for expression can still show clear signal of chromatin accessibility at regulatory elements. The dissociation between chromatin accessibility and transcription has been reported in many different cells and conditions (PMID: 36069349, PMID: 33098772) including in spermatogonial cells (PMID: 28985528) and in gonads in different species (PMID: 36323261). Therefore, the dissociation between accessibility and transcription is not a reason to conclude that our data are flawed.

In addition, there already are numerous scRNA-seq datasets from mouse spermatogenic cells at the same developmental stages in question.

This is true but full transcriptomic profiling like ours on cell populations provides different transcriptional information that is deeper and more comprehensive. Our datasets identified >17,000 genes while scRNA-seq typically identifies a few thousands of genes. Our analyses also identified full length transcripts, variants, isoforms and low abundance transcripts. These datasets are therefore a valuable addition to existing scRNA-seq.

Moreover, several groups have used bulk ATAC-seq to profile enriched populations of spermatogonia, including from synchronized spermatogenesis which reflects a high degree of purity (see Maezawa et al., 2018 PMID: 29126117 and Schlief et al., 2023 PMID: 36983846 and in cultured spermatogonia - Suen et al., 2022 PMID: 36509798) - so this topic has already begun to be examined. None of these papers was cited, so it appears the authors were unaware of this work.

We apologize for not mentioning these studies in our manuscript, we will do so in the revised version.

The authors' methodological choice is even more surprising given the wealth of single-cell evidence in the literature since 2018 demonstrating the exceptional heterogeneity among spermatogonia at these developmental stages (the authors DID cite some of these papers, so they are aware). Indeed, it is currently possible to perform concurrent scATAC-seq and scRNA-seq (10x Genomics Multiome), which would have made these data quite useful and robust. As it stands, given the lack of novelty and critical methodological flaws, readers should be cautioned that there is little new information to be learned about spermatogenesis from this study, and in fact, the data in Figures 2-5 may lead readers astray because they do not reflect the biology of any one type of male germ cell. Indeed, not only do these data not add to our understanding of spermatogonial development, but they are damaging to the field if their source and identity are properly understood. Here are some specific examples of the problems with these data:

1. Fig. 2D - Gata4 and Lhcgr are not expressed by germ cells in the testis.

2. Fig. 3A - WT1 is expressed by Sertoli cells, so the change in accessibility of regions containing a WT1 motif suggests differential contamination with Sertoli cells. Since Wt1 mRNA was differentially high in P15 (Fig. 3B) - this seems to be the most likely explanation for the results. How was this excluded?

3. Fig. 3D - Since Dmrt1 is expressed by Sertoli cells, the "downregulation" likely represents a reduction in Sertoli cell contamination in the adult, like the point above. Did the authors consider this?

We acknowledge that concurrent scATAC-seq and scRNA-seq analyses have been done by others but our datasets add to these analyses by providing concurrent chromatin and expression analyses at high resolution in spermatogonial populations at 2 postnatal stages and in adulthood and from individual males (for adult cells). This provides a set of information that adds to the current literature. Doing such analyses in single cells is not tractable financially so we offer an economical alternative that delivers high resolution datasets for these different time points. Our analyses were not meant to study spermatogenesis but to provide a thorough and comprehensive profiling of chromatin accessibility and transcription in postnatal and adult spermatogonial cells.

Our data need careful interpretation to avoid any misleading conclusions. Fig. 2D does not show expression but accessibility which does not tell if a particular locus or gene is expressed or not. Thus, candidates like Gata4 and Lhcgr shown in Fig. 2D are simply associated with DARs but this does not mean that they are expressed. Likewise in Fig. 3A, motifs refer to decreased accessibility and not to expression. Fig. 1C indicates that PND15 cells have low to no expression of 3 Sertoli cells markers (Vim, Tspan17 and Rhox), suggesting little contamination by Sertoli cells. The presence of WT1 in PND15 cells will however be examined more carefully and re-analysed by in silico deconvolution methods using single cell datasets for the revised manuscript. In Fig. 3D, differential contamination by Sertoli cells is possible, this will also be examined by deconvolution methods.

Reviewer #3 (Public Review):

In this study, Lazar-Contes and colleagues aimed to determine whether chromatin accessibility changes in the spermatogonial population during different phases of postnatal mammalian testis development. Because actions of the spermatogonial population set the foundation for continual and robust spermatogenesis and the gene networks regulating their biology are undefined, the goal of the study has merit. To advance knowledge, the authors used mice as a model and isolated spermatogonia from three different postnatal developmental age points using a cell sorting methodology that was based on cell surface markers reported in previous studies and then performed bulk RNA-sequencing and ATAC-sequencing. Overall, the technical aspects of the sequencing analyses and computational/bioinformatics seem sound but there are several concerns with the cell population isolated from testes and lack of acknowledgment for previous studies that have also performed ATAC-sequencing on spermatogonia of mouse and human testes. The limitations, described below, call into question the validity of the interpretations and reduce the potential merit of the findings.

I suggest changing the acronym for spermatogonial cells from SC to SPG for two reasons. First, SPG is the commonly used acronym in the field of mammalian spermatogenesis. Second, SC is commonly used for Sertoli Cells.

We thank the reviewer for the suggestion and will rename SCs into SPGs in the revised manuscript.

The authors should provide a rationale for why they used postnatal day 8 and 15 mice.

We will provide a rationale for the use of postnatal 8 and 15 stages in the revised manuscript. Briefly, these stages are interesting to study because early to mid postnatal life is a critical window of development for germ cells during which environmental exposure can have strong and persistent effects. The possibility that changes in germ cells can happen during this period and persist until adulthood is an important area of research linked to disciplines like epigenetic toxicology and epigenetic inheritance.

The FACS sorting approach used was based on cell surface proteins that are not germline-specific so there were undoubtedly somatic cells in the samples used for both RNA and ATAC sequencing. Thus, it is essential to demonstrate the level of both germ cell and undifferentiated spermatogonial enrichment in the isolated and profiled cell populations. To achieve this, the authors used PLZF as a biomarker of undifferentiated spermatogonia. Although PLZF is indeed expressed by undifferentiated spermatogonia, there have been several studies demonstrating that expression extends into differentiating spermatogonia. In addition, PLZF is not germ-cell specific and single-cell RNA-seq analyses of testicular tissue have revealed that there are somatic cell populations that express Plzf, at least at the mRNA level. For these reasons, I suggest that the authors assess the isolated cell populations using a germ-cell specific biomarker such as DDX4 in combination with PLZF to get a more accurate assessment of the undifferentiated spermatogonial composition. This assessment is essential for the interpretation of the RNA-seq and ATAC-seq data that was generated.

The reviewer is right that our cell populations likely contain undifferentiated and differentiated spermatogonial cells and a small percentage of somatic cells including Sertoli cells. As suggested, we examined the expression of the germ-cell marker Ddx4 in our datasets and observed that Ddx4 is highly expressed. It is indeed more highly expressed than the SSC marker Id4 (average log2CPM of 5 vs 8, respectively). We will include this information in the revised manuscript. Further, the deconvolution analyses that will be conducted are expected to clarify the cellular composition of our cell populations.

A previous study by the Namekawa lab (PMID: 29126117) performed ATAC-seq on a similar cell population (THY1+ FACS sorted) that was isolated from pre-pubertal mouse testes. It was surprising to not see this study referenced in the current manuscript. In addition, it seems prudent to cross-reference the two ATAC-seq datasets for commonalities and differences. In addition, there are several published studies on scATAC-seq of human spermatogonia that might be of interest to cross-reference with the ATAC-seq data presented in the current study to provide an understanding of translational merit for the findings.

We thank the reviewer for pointing out this study as well as other studies in human spermatogonia. We will cross-reference all of them in the revised manuscript.

Author Response

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

Reviewer 1

We thank the reviewer for their thoughtful comments. We have addressed them below, and we believe that have significantly strengthened the clarity of the manuscript.

Main Comments:

In Fig. 2C-D, I am not sure I understand why ≈ 100 mutations fix with β = 0. In the absence of epistasis, and since the coefficients hi are sampled from a symmetric distribution centered at zero, it is to be expected that roughly half of the mutations will have positive fitness effects and thus will eventually fix in the population. With L = 250, I would have expected to see the number of fixed mutations approach ≈ 125 for β = 0. Perhaps I am missing something?

• In our simulations, we initialize all populations from a state where there are only 100 available beneficial mutations (i.e., the initial rank is always 100). Without epistasis, these initial beneficial mutations are the only beneficial mutations that will be present throughout the entire trajectory. Hence, for β = 0, only 100 beneficial mutations can fix. Previously, this information could be found in the “Materials and methods” section of the SI. To make this aspect of our simulation more clear in the revision, we have added a discussion of the initial rank to the “Landscape structure” subsection of the model definition section. In addition, we have merged “Materials and methods” with “Further simulation details” in the SI into one section, and have listed the values for the simulation parameters in the model definition section.

Along these lines, the authors show that increasing β leads to a higher number of fixed mutations. I am not sure I understand their explanation for this. In line 209 they write that as β increases, “mutations are needed to cease adaptation”. The way I see it, in the absence of epistasis the fitness peak should correspond to a genotype with ≈ L/2 mutations (the genotype carrying all mutations with hi > 0). Increasing the magnitude of microscopic epistasis (i.e., increasing β ), and assuming that there is no bias towards positive epistasis (which there shouldn’t be based on the model formulation, i.e., section "Disorder statistics" on page 4), can change the “location” of the fitness peak, such that it now corresponds to a different genotype. Statistically speaking, however, there are more genotypes with L/2 mutations than with any other number of mutations, so I would have expected that, on average, the number of mutations fixed in the population would still have been ≈ L/2 (naturally with somewhat large variation across replicates, as seems to be the case).

• With epistasis, the situation becomes more complex. The structure of our model imposes significant sign epistasis in general (i.e. mutations can be beneficial on one background genotype and deleterious on another). This means that in the presence of epistasis, more than 100 mutations can be required to reach a local optimum even when the initial rank was 100. Intuitively, this occurs because mutations that were deleterious on the ancestral background genotype can become beneficial on future genotypes. We find that this occurs consistently throughout adaptation, leading to the accumulation of more mutations with increasing epistasis.

• Please note that we use the value L = 1000 in our simulations. We have also made the fact that we use L = 1000 more clear by moving the description of the simulation parameters to the main text.

I do see how, in the clonal interference regime, there can be multiple genotypes in the population at a given time (each with a different mutational load), thus making the number of fixed mutations larger than L/2 when aggregating over all genotypes in the population. But this observation makes less intuitive sense to me in the SSWM regime. In lines 207-208, the authors state that “as beta increases, a greater number of new available beneficial mutations are generated per each typical fixation event”. While this is true, it is also the case that a greater number of mutations that would have been beneficial in the absence of epistasis are now deleterious due to negative epistasis (if I am understanding what the authors mean correctly).

• The reviewer is correct to note that in the strong clonal interference regime, there will be more accumulated mutations across the entire population than in any single strain. However, we report the number mutations that have fixed, i.e., become present in the entire population.

• We find that the typical decrease in rank (per fixation event) of the population decreases with increasing epistasis — i.e., the number of available beneficial mutations that are “consumed” when a mutation fixes is typically lower in systems with stronger epistasis.

Similarly, I am not sure I understand how one goes from equation (6) to equation (7). In particular, it would seem to me that the term 4αiαj Ji j in equation (6) should be equally likely to be positive or negative (again assuming no bias towards positive Ji j). I thus do not see why ηi j in equation (7) is sampled from a normal distribution with mean µβ instead of just mean zero.

• The reviewer is correct that, for a uniformly random initial state, αi , αj , and Ji j will be uncorrelated so that the distribution of 4αiαj Ji j can be computed exactly (and has mean zero). However, we initialize from a state with rank 100, so that we need to compute the distribution of the random variable E[αiαj Ji j|αiαj Ji j > 0, R = 100]. This is mathematically very challenging, because there are nontrivial correlations between spins even at initialization. For these reasons, we found the uniformly random approximation insufficient. This is described in the paragraph following Equation (7) in the resubmission.

Minor Comments:

The authors use a model including terms up to second-order epistasis. To be clear, I think this choice is entirely justified: as they mention in their manuscript, this structure allows to approximate any fitness model defined on a Boolean hypercube. As I understand it, the reason for not incorporating higher-order terms (as in e.g. Reddy and Desai, eLife 2021) has to do with computational efficiency, i.e., accommodating higher-order terms in equation (10) may lead to a substantial increase in computation time. Is this the case?

• The author is correct that the incorporation of higher-order terms leads to significantly more expensive computation. It’s an interesting direction of future inquiry to see if our adaptive fast fitness computation method can be extended to higher-order interactions.

Reviewer 2

We would like to thank the reviewer for their careful reading and their useful comments connecting our work to spin glass physics. We believe the resulting additions to the paper have made our contributions stronger, and that they reveal some novel connections between the substitution trajectory and correlation functions in spin glasses. A summary of our investigation is provided below, and we have added two paragraphs to the discussion section under the heading “Connections to spin glass physics”.

Main Comments:

In spin glasses, slowdown of dynamics could have contributions from stretched exponential relaxation of spin correlations as well as aging, each of which are associated with their own exponents. In the present model, these processes could be quantified by computing two-point correlations associated with genomic overlap, as a function of lag time as well as waiting time (generation number). The population dynamics of competing strains makes the analysis more complicated. But it should be possible to define these correlations by separately averaging over lineages starting from a single parent genome, and over distinct parent genomes. It would be interesting to see how exponents associated with these correlations relate to the exponent c associated with asymptotic fitness growth.

• To investigate this point, we first considered the two-point correlation function 〈αi (tw)αi (tw+ ∆t)〉 for waiting time tw and lag time ∆t. Because all spins are statistically identical, it is natural to average this over the spin index i, leading to the quantity

Viewed as a function of ∆t for any fixed tw, it is clear that . If m mutations with respect to α(tw) have fixed at time tw + ∆t, a similar calculation shows that . Surprisingly, this simple derivation reveals that the two-spin correlation function commonly studied in spin glass physics is an affine transformation of the substitution trajectory commonly studied in population genetics. Moreover, it shows that the effect of tw is to change the definition of the ancestral strain, so that we may set tw = 0 without loss of generality and study the correlation function χ2(t) = 1 − 2m(t) where m(t) is the mean substitution trajectory of the population. Much of our analysis proceeds by analyzing the effect of epistasis on the accumulation of mutations. This relation provides a novel connection between this analysis and the analysis of correlation functions in the spin glass literature.

• It is well known that in the SSWM limit without epistasis, the substitution trajectory follows a power law similar to the fitness trajectory with relaxation exponent 1.0 [1]. Informed by this identity, we performed simulations in the SSWM limit and fit power laws to the correlation function χ2 as a function of time. We have verified that χ2(t) obeys a power- law relaxation with exponent roughly 1.0 for β = 0; moreover, as anticipated by the reviewer, the corresponding exponent decreases with increasing β . Nevertheless, we find that these relaxation exponents are distinct from those found for the fitness trajectory, despite following the same qualitative trend. This point is particularly interesting, as it highlights that the dynamics of fixation induce a distinct functional form at the level of the correlation functions when compared to, for example, the Glauber dynamics in statistical physics.

The strength of dynamic correlations in spin glasses can be characterized by the four-point susceptibility, which contains information about correlated spin flips. These correlations are maximized over characteristic timescales. In the context of evolution, such analysis may provide insights on the correlated accumulation of mutations on different sets of loci over different timescales. It would be interesting to see how these correlations change as a function of the mutation rate as well as the strength of epistasis.

• To study this point, we considered the four-point correlation function

Because spins are statistically identical, we found numerically that the genotype average is roughly equivalent to the angular average over trajectories. Inter-changing the order of the summation and the angular averaging, we then find that

so that the information contained in the four-point correlation function is the same as the information contained in the two-point correlation function.

Fig. 2E and Fig. 5 together suggests an intriguing possibility when interpreted in the spin glass context. It is clear that in the absence of epistasis, clonal interference accelerates fitness growth. Fig. 2E additionally suggests that this scenario will continue to hold even in the presence of weak, but finite epistasis, but disappears for sufficiently strong epistasis. I wonder if the two regimes are separated by a phase transition at some non-trivial strength of epistasis. Indeed, the qualitative behavior appears to change from that of a random field Ising spin glass for small β , to that of a zero field Sherrington-Kirkpatrick spin glass for sufficiently large β . While the foregoing comments are somewhat speculative, perhaps a discussion along these lines, and what it means in the context of evolution could be a useful addition to the discussion section of the paper.

• We thank the reviewer for this interesting suggestion, and we have added a discussion of this point to the text in the future directions section, lines 483–489.

Minor Comments:

1. In the abstract (line 17-18), I recommend use of the phrase "a simulated evolving population" to avoid a possible misinterpretation of the work as experimental as opposed to numerical.

• We have added the word “simulated”.

1. In line 70, the word "the" before "statistical physics" is redundant.

• We have removed “the”.

1. To make the message in lines 294-295 visually clear, I recommend keeping the Y-axis scale bars constant across Fig. 4A and Fig. 4B.

• We appreciate the suggestion. However, we found that when putting the two figures on the same scale, because the agreement is only qualitative and not quantitative (as emphasized in the text), it becomes difficult to view the trend in both systems. For this reason, we have chosen to keep the figure as-is.

1. Fig. 6 caption states: "Without epistasis, the rank decreases with increasing µ". It should be "rank increases".

• We have fixed this.

1. In the last sentence in the caption to Fig. 8, the labels "(A, β =0)" and "(B, β =0.25)" need to be swapped.

• We have fixed this.

Editor Comments

We thank the editor for pointing our attention towards these three interesting references, in particular the second, which appears most relevant to our work. We have added a discussion of reference 2 in the future directions section (lines 471–482), commenting on how to determine the contribution of within-path clonal interference to the fitness dynamics in our model. We have also added a reference to article 3 in the model description, commenting on the importance of sign epistasis and the prevalence of sign epistasis in our model with β > 0.

References:

1. Good BH, Desai MM. The impact of macroscopic epistasis on long-term evolutionary dynamics. Genetics. 2015.

Author Response

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This study aims to further resolve the history of speciation and introgression in Heliconius butterflies. The authors break the data into various partitions and test evolutionary hypotheses using the Bayesian software BPP, which is based on the multispecies coalescent model with introgression. By synthesizing these various analyses, the study pieces together an updated history of Heliconius, including a multitude of introgression events and the sharing of chromosomal inversions.

Strengths:

Full-likelihood methods for estimating introgression can be very computationally expensive, making them challenging to apply to datasets containing many species. This study provides a great example of how to apply these approaches by breaking the data down into a series of smaller inference problems and then piecing the results together. On the empirical side, it further resolves the history of a genus with a famously complex history of speciation and introgression, continuing its role as a great model system for studying the evolutionary consequences of introgression. This is highlighted by a nice Discussion section on the implications of the paper's findings for the evolution of pollen feeding.

Weaknesses:

The analyses in this study make use of a single method, BPP. The analyses are quite thorough so this is okay in my view from a methodological standpoint, but given this singularity, more attention should be paid to the weaknesses of this particular approach.

In the Discussion, we have now added a discussion of the limitations of our approach in the section 'Approaches for estimating species phylogeny with introgression from whole-genome sequence data: advantages and limitations.'

Additionally, little attention is paid to comparable methods such as PhyloNet and their strengths and weaknesses in the Introduction or Discussion.

We have also mentioned other methods (PhyloNet and starBEAST) in our Discussion. Our attempts to obtain usable estimates from PhyloNet were unsuccessful. In another study, the full likelihood version of PhyloNet (comparable in intent to the BPP methodology used here) could run with only small datasets of ~100 loci; see Edelman et al. (2019).

BPP reduces computational burden by fixing certain aspects of the parameter space, such as the species tree topology or set of proposed introgression events. While this approach is statistically powerful, it requires users to make informed choices about which models to test, and these choices can have downstream consequences for subsequent analyses. It also might not be as applicable to systems outside of Heliconius where less previous information is available about the history of speciation and introgression. In general, it is likely that most modelling decisions made in the study are justified, but more attention should be paid to how these decisions are made and what the consequences of them could be, including alternative models.

We agree with the reviewer that inferring the species tree topology and placing introgression events on the species tree, although well justified here, may be challenging in many groups of organisms and may affect downstream analyses. We now discuss this as a limitation of our approach in the Discussion. In general, the initial MSC analysis without gene flow should provide information about possible species trees and introgression events. We can construct multiple introgression models and perform parameter estimation and model comparison to decide which best fits the data. This is summarized in the last paragraph of the section 'Approaches for estimating species phylogeny with introgression from whole-genome sequence data: advantages and limitations.' It would, of course, be nice to have a completely unsupervised method that could work with large phylogenies, but this is currently computationally impossible.

• Co-estimating histories of speciation and introgression remains computationally challenging. To circumvent this in the study, the authors first estimate the history of speciation assuming no gene flow in BPP. While this approach should be robust to incomplete lineage sorting and gene tree estimation, it is still vulnerable to gene flow. This could result in a circular problem where gene flow causes the wrong species tree to be estimated, causing the true species tree to be estimated as a gene flow event.

The goal of this initial analysis is to obtain a list of possible species trees with introgression events. We assume that gene flow results in a topology that is informative about the lineages involved. We also focus on common MAP trees with high posterior probabilities as less frequent trees or trees with low posterior probabilities reflect high uncertainty and are more likely to be erroneous. A difficulty is to decide which tree topology is most likely to be the true species tree. We summarize our approach in the Discussion.

This is a flaw that this approach shares with summary-statistic approaches like the D-statistic, which also require an a-priori species tree.

In a sense, this is true, but BPP is more flexible because it can be used to explore an arbitrary introgression model on any type of tree, while summary methods like D-statistic assume a specific species phylogeny with a particular introgression between nonsister lineages as well as fixed sampling configurations. Furthermore, as shown in the paper, we can compare different assumed trees, and test between them; we do this repeatedly in the paper for difficult branch placement issues. In contrast, summary methods such as the D-statistic works with species quartets only and do not work with either smaller or larger species trees.

Enrichment of particular topologies on the Z chromosome helps resolve the true history in this particular case, but not all datasets will have sex chromosomes or chromosome-level assemblies to test against.

Yes, we have the privilege of having chromosome-level assemblies available for Heliconius. In general, a spatial pattern of species tree estimates across genomic blocks can be informative about possible topologies that could represent the true species relationship. Then these candidate species trees can be tested by fitting different introgression models (as in Figure 1D,E) or by using the recombination rate argument (Figure 1F), which prefers trees common in low recombination rate regions of the genome, although this requires knowing a recombination rate map. In our case, we used a chromosome-level recombination rate per base pair, which is negatively correlated with the chromosome size. We have clarified this in the text. Ultimately, multiple lines of evidence should be examined before deciding on the most likely species tree. We now mention these potential difficulties with applying our methods to other datasets as limitations of our approach in the Discussion.

• The a-priori specification of network models necessarily means that potentially better-fitting models to the data don't get explored. Models containing introgression events are proposed here based on parsimony to explain patterns in gene tree frequencies. This is a reasonable and common assumption, but parsimony is not always the best explanation for a dataset, as we often see with phylogenetic inference. In general, there are no rigorous approaches to estimating the best-fitting number of introgression events in a dataset.

Joint inference of species topologies and possible introgression events remains computationally challenging. PhyloNet implements this joint inference but is limited to small datasets (<100 loci) and we found it to be unreliable.

Likewise, the study estimates both pulse and continuous introgression models for certain partitions, though there is no rigorous way to assess which of these describes the data better.

The Bayes factor can be used to compare different models fitted to the same data, for example, different MSC-I models with different introgression events, or MSC-I models with gene flow in pulses versus MSC-M models with continuous gene flow. We did not attempt this as it was clear to us that a better model would include both modes of gene flow, but such an option is not currently implemented in any software. Rather, we relied on our exploratory analysis (BPP MSC and 3s) and previous knowledge to inform a likely introgression model. In the case of groups that we fitted the MSC-M models, we chose to provide an intuitive justification as to why they might be more realistic than the MSC-I model without formally performing model selection.

• Some aspects of the analyses involving inversions warrant additional consideration. Fewer loci were able to be identified in inverted regions, and such regions also often have reduced rates of recombination. I wonder if this might make inferences of the history of inverted regions vulnerable to the effects of incomplete lineage sorting, even when fitting the MSC model, due to a small # of truly genealogically independent loci.

We agree with the reviewer that it is challenging to infer the history of a small region of the genome, such as the inversions studied here. Indeed, the presence of only a few loci in the 15b inversion means there is only limited information in the data for the species tree, as reflected in the low posterior probabilities for the MAP tree (Figure 3A). The effect of using tightly linked loci in the inversion should be increased uncertainty in the estimates, but not a systematic bias towards any particular species tree topology. Since major patterns of species relationships in each of the 15a, 15b and 15c regions are clear, we do not expect these effects to strongly influence our conclusions.

Additionally, there are several models where introgression events are proposed to explain the loss of segregating inversions in certain species. It is not clear why these scenarios should be proposed over those in which the inversion is lost simply due to drift or selection.

We know that the 15b inversion is absent in most species except for H. numata and H. pardalinus, at least, and that introgression of the inversion occurred between these two species, based on previous studies such as Jay et al (2018) and our own analysis. Polymorphism at this inversion forms a well-known “supergene” that affects mimicry, and is maintained by documented balancing selection in H. numata. Given this information, we propose a few possible scenarios of how the inversion might have originated, and when and where the introgression might have occurred, shown in Figure 3. In particular, the direction of introgression is something we test specifically. One way to test among these scenarios is to date the origin and introgression event of the inversion, but doing so properly is beyond the scope of this work. Nonetheless, we argue that it is at least likely that one difference between H. pardalinus and its sister species H. elevatus is the presence of the 15b inversion. Since other evidence shows that colour patterning loci in H. elevatus originated from an unrelated species, H. melpomene (i.e. the 15b and other non-inverted colour patterning loci), it is indeed likely that the inversion was “swapped out” by an uninverted sequence from H. melpomene during the formation of H. elevatus.

We are aware that hypotheses such as these might appear highly elaborate and unparsimonious. But these are the conclusions where the data lead us. In the melpomene-silvanform clade, many speciation and introgression events occurred in short succession, and wild-caught hybrids prove that occasional hybridizations can occur across all 15 or so species in the group. We now detail how we have looked only for the major introgression patterns using a limited number of key speces. We leave fuller analyses for future work.

In the main text, we have revised our discussion of the four proposed scenarios for 15b to improve clarity. We have also updated the introgression model from the melpomene-cydno clade to H. elevatus to be unidirectional based on the BPP results in Figure S18.

Reviewer #2 (Public Review):

Thawornwattana et al. reconstruct a species tree of the genus Heliconius using the full-likelihood multispecies coalescent, an exciting approach for genera with a history of extensive gene flow and introgression. With this, they obtain a species tree with H. aoede as the earliest diverging lineage, in sync with ecological and morphological characters. They also add resolution to the species relationships of the melpomene-silvaniform clade and quantify introgression events. Finally, they trace the origins of an inversion on chromosome 15 that exists as a polymorphism in H. numata, but is fixed in other species. Overall, obtaining better species tree resolutions and estimates of gene flow in groups with extensive histories of hybridization and introgression is an exciting avenue. Being able to control for ILS and get estimates between sister species are excellent perks. One overall quibble is that the paper seems to be best suited to a Heliconius audience, where past trees are easily recalled, or members of the different clades are well known.

We thank the reviewer for the accurate summary and positive comments. Although our data and some of the discussion are specific to Heliconius, we believe our analysis framework will be useful to study species phylogeny and introgression in other taxa as well.

Overall, applying approaches such as these to gain greater insight into species relationships with extensive gene flow could be of interest to many researchers. However, the conclusions could be strengthened with a bit more clarity on a few points.

1) The biggest point of concern was the choice of species to use for each analysis. In particular the omission of H. ismenius in the resolution of the BNM clade species tree. The analysis of the chromosome 15 inversion seems to rely on the knowledge that H. ismenius is sister to H. numata, so without that demonstrated in the BNM section the resulting conclusions of the origin of that inversion are less interruptible.

The choice of species to be included was mainly based on available high-quality genome resequence data from Edelman et al (2019), which were chosen to cover most of the major lineages within the genus. We agree that inclusion of H. ismenius would strengthen the analysis of the melpomene-silvaniform clade. In particular, it would be interesting to know which of only H. numata or H. numata+H. ismenius are responsible for the main source of genealogical variation across the genome in this group in Figure 2. The reviewer is correct in saying that we do assume that H. ismenius and H. numata are sister species. This relationship is supported by our analysis (Figure 3A) and previous analyses of genomic data, e.g. Zhang et al (2016), Cicconardi et al. (2023) and Rougemont et al. (2023). We made this clearer in the text:

"Although this conclusion assumes that H. numata and H. ismenius are sister species while H. ismenius was not included in our species tree analysis of the melpomene-silvaniform clade (Figure 2), this sister relationship agrees with previous genomic studies of the autosomes and the sex chromosome (Zhang et al. 2016; Cicconardi et al. 2023; Rougemont et al. 2023)."

2) An argument they make in support of the branching scenario where H. aoede is the earliest diverging branch is based on which chromosomes support that scenario and the key observation that less introgression is detected in regions of low recombination. Yet, they go no further to understand the relationship between recombination rate and species trees produced.

We believe Figure 1F does examine this relationship, showing that trees under scenario 2 are more common in regions of the genome with lower recombination rates (i.e. in longer chromosomes). We added more clarification in the text where Figure 1F is mentioned. The relationship between recombination and introgression in Heliconius was earlier discovered and shown using windowed estimated gene trees in Martin et al. (2019) and in Edelman et al. (2019), so we did not re-test this here.

3) How the loci were defined could use more clarity. From the methods, it seems like each loci could vary quite a bit in total bp length and number of informative sites. Understanding the data processing would make this paper a better resource for others looking to apply similar approaches.

We added a new supplemental figure, Figure S20, to illustrate how coding and noncoding loci were extracted from the genome.

Reviewer #3 (Public Review):

The authors use a full-likelihood multispecies coalescent (MSC) approach to identify major introgression events throughout the radiation of Heliconius butterflies, thereby improving estimates of the phylogeny. First, the authors conclude that H. aoede is the likely outgroup relative to other Heliconius species; miocene introgression into the ancestor of H. aoede makes it appear to branch later. Topologies at most loci were not concordant with this scenario, though 'aoede-early' topologies were enriched in regions of the genome where interspecific introgression is expected to be reduced: the Z chromosome and larger autosomes. The revised phylogeny is interesting because it would mean that no extant Heliconius species has reverted to a non-pollen-feeding ancestral state. Second, the authors focus on a particularly challenging clade in which ancient and ongoing gene flow is extensive, concluding that silvaniform species are not monophyletic. Building on these results, a third set of analyses investigates the origin of the P1 inversion, which harbours multiple wing patterning loci, and which is maintained as a balanced polymorphism in H. numata. The authors present data supporting a new scenario in which P1 arises in H. numata or its ancestor and is introduced to the ancestor of H. pardilinus and H. elevatus - introgression in the opposite direction to what has previously been proposed using a smaller set of taxa and different methods.

The analyses were extensive and methodologically sound. Care was taken to control for potential sources of error arising from incorrect genotype calls and the choice of a reference genome. The argument for H. aoede as the earliest-diverging Heliconius lineage was compelling, and analyses of the melpomene-silvaniform clade were thorough.

The discussion is quite short in its current form. In my view, this is a missed opportunity to summarise the level of support and biological significance of key results. This applies to the revised Melpomenesilvaniform phylogeny and, in particular, the proposed H. numata origin of P1. It would be useful to have a brief overview of the relationships that remain unclear, and which data (if any) might improve estimates.

We added a paragraph in the Discussion to summarize our key findings in 'An updated phylogeny of Heliconius', and discuss issues that remain uncertain.

It was good to see the authors reflect on the utility of full-likelihood approaches more generally, though the discussion of their feasibility and superiority was at times somewhat overstated and reductive. Alternative MSC-based methods that use gene tree frequencies or coalescence times can be used to infer the direction and extent of introgression with accuracy that is satisfactory for a wide variety of research questions. In practice, a combination of both approaches has often been successful. Although full-likelihood approaches can certainly provide richer information if specific parameter estimates are of interest, they quickly become intractable in large species complexes where there is extensive gene flow or significant shifts in population size. In such cases, there may be hundreds of potentially important parameters to estimate, and alternate introgression scenarios may be impossible to disentangle. This is particularly challenging in systems, unlike Heliconius where there is little a priori knowledge of reproductive isolation, genome evolution, and the unique life history traits of each species. It would be useful for the authors to expand on their discussion of strategies that can simplify inference problems in such systems, acknowledging the difficulties therein.

We agree that approximate methods based on summary statistics (e.g. gene tree topologies) are computationally much cheaper and are sometimes useful. We now discuss limitations of our approach regarding strategies for constructing possible introgression models, computational cost and analysis of large phylogenies, and modeling assumptions in the MSC framework in the first section of the Discussion.

Reviewer #1 (Recommendations For The Authors):

In addition to the comments raised in the public review, I have some minor suggestions:

• In the Introduction, "Those methods have limited statistical power" implies summary-statistic methods have a high false negative rate for inferring the presence of introgression, which I don't think is true.

We removed 'statistical' as we used the term power loosely to mean ability to estimate more parameters in the model by making a better use of information in the sequence data and not in the sense of a true positive rate.

• When discussing full-likelihood approaches in a general sense, please cite additional methods than just BPP, such as PhyloNet.

We added references for PhyloNet (Wen & Nakhleh, 2018) and starBEAST (Zhang et al., 2018) in the Introduction and Discussion.

• Consider explicitly labelling chromosomal region 21 as the Z chromosome in relevant Figures, for ease of interpretation.

In the main figures, we changed the chromosome label from 21 to Z.

• From reading the main text it's not clear what a "3s analysis" is

The 3s analysis estimates pairwise migration rates between two species by fitting an MSC-withmigration (MSC-M) model, also known as isolation-with-migration (IM), for three species, where gene flow is allowed between the two sister species while the outgroup is used to improve the power but does not involved in gene flow. We changed the text from

"We use estimates of migration rates between each pair of species with a 3s analysis under the IM model of species triplets ..."

to

"We use estimates of migration rates between each pair of species under the the MSC-withmigration (MSC-M or IM) model of species triplets (3s analysis) ..."

• "This agrees with the scenario in which H. elevatus is a result of hybrid speciation between H. pardalinus and the common ancestor of the cydno-melpomene clade [42, 43]." I don't think this model provides any support for hybrid speciation in particular, over a standard post-speciation introgression scenario.

We took the finding that the introgression from the melpomene-cydno clade into H. elevatus occurs almost right after H. elevatus split off from H. pardalinus as evidence for hybrid speciation. We revised the text to make this clearer:

"Our finding that divergence of H. elevatus and introgression from the cydno-melpomene clade occurred almost simultaneously provides evidence for a hybrid speciation origin of H. elevatus resulting from introgression between H. pardalinus and the common ancestor of the cydno-melpomene clade (Rosser et al. 2019; Rosser et al. 2023)."

In particular, the Rosser et al. (2023) paper has now been submitted, and is the main paper to cite for the hybrid speciation hypothesis for H. elevatus.

• "while clustering with H. elevatus would suggest the opposite direction of introgression" careful with terminology here; is this about direction (donor vs. recipient species) or taxa involved (which is not direction)?

This is about the direction of introgression, not the taxa involved. We modified the text to make this clearer:

"By including H. ismenius and H. elevatus, sister species of H. numata and H. pardalinus respectively, different directions of introgression should lead to different gene tree topologies. Clustering of (H. numata with the inversion, H. pardalinus) with H. numata without the inversion would suggest the introgression is H. numata → H. pardalinus while clustering of (H. numata with the inversion, H. pardalinus) with H. elevatus would suggest H. pardalinus → H. numata introgression."

Reviewer #3 (Recommendations For The Authors):

The work is methodologically sound and rigorous but could have been reported and discussed with greater clarity.

It was difficult to assess the level of support for the proposed P1 introgression scenario without digging through the extensive supplementary materials. The discussion would ideally be used to clarify and summarise this.

We have substantially revised the section on the P1 inversion. We also mention in the Results (in the final paragraph of the inversion section) and Discussion that our data provided robust evidence that the introgression of the inversion is from H. numata into H. pardalinus while its precise origin (in which lineage and when it originated) remains uncertain.

The authors may also wish to compare their results to the recent work by Rougemont et al. on introgression between H. hecale and H. ismenius in the discussion.

We now mention Rougemont et al. (2023) in the Discussion as an example of introgression of small regions of the genome involved in wing patterning. We also acknowledge that our updated phylogeny does not include this kind of local introgression.

It was not initially obvious which number corresponded to the Z chromosome in any of the figures, even though this is critical to their interpretation.

We changed the label for chromosome 21 to Z in the main figures.

The supplementary tables should be described in more detail. For example, what is 'log_bf_check' and 'prefer_pred' in supplementary table S11?

We added more details explaning necessary quantities in the table heading in both SI file and in the spreadsheet.

Minor comments:

First paragraph of 'Complex introgression in the 15b inversion region (P locus):' Rephrase "This suggests another introgression between the common...".

We modified the text as follows:

"Another feature of this 15b region is that among the species without the inversion, the cydnomelpomene clade clusters with H. elevatus and is nested within the pardalinus-hecale clade (without H. pardalinus). This is contrary to the expectation based on the topologies in the rest of the genome (Figure 2A, scenarios a–c) that the cydno-melpomene clade would be sister to the pardalinus-hecale clade (without H. pardalinus). One explanation for this pattern is that introgression occurred between the common ancestor of the cydno-melpomene clade and either H. elevatus or the common ancestor of H. elevatus and H. pardalinus together with a total replacement of the non-inverted 15b in H. pardalinus by the P1 inversion from H. numata (Jay et al. 2018). We confirm and quantify this introgression below."

Second paragraph of 'Major Introgression Patterns in the melpomene-silvaniform clade:' "cconclusion" should be "conclusion."

Corrected.

Paragraph preceding discussion: sentences toward the end of the paragraph should be rephrased for clarity. E.g. "different tree topologies are expected under different direction of introgression."

We revised this paragraph. The sentence now says:

"By including H. ismenius and H. elevatus, sister species of H. numata and H. pardalinus respectively, different directions of introgression should lead to different gene tree topologies.<br /> Clustering of (H. numata with the inversion, H. pardalinus) with H. numata without the inversion would suggest the introgression is H. numata → H. pardalinus while clustering of (H. numata with the inversion, H. pardalinus) with H. elevatus would suggest H. pardalinus → H. numata introgression."

I enjoyed reading this paper and I am certain it will generate discussion and future research.

Author Response

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

Reviewer #1 (Public Review):

While the manuscript was reasonably clearly written and the methodology and results sound, it is not clear what the real contribution of the work is. The authors' findings - that ultrasonic stimulation is capable of altering intracellular Ca2+ to effect an increase in EV secretion from cells as long as the irradiation does not affect cell viability-is well established (see, for example, Ambattu et al., Commun Biol 3, 553, 2020; Deng et al., Theranostics, 11, 9 2021; Li et al., Cell Mol Biol Lett 28, 9, 2023). Moreover, the authors' own work (Maeshige et al., Ultrasonics 110, 106243, 2021) using the exact same stimulation (including the same parameters, i.e., intensity and frequency) and cells (C2C12 skeletal myotubes) reported this. Similarly, the authors themselves reported that EV secretion from C2C12 myotubes has the ability to regulate macrophage inflammatory response (Yamaguchi et al., Front Immunol 14, 1099799, 2023). It would then stand to reason that a reasonable and logical deduction from both studies is that the ultrasonic stimulation would lead to the same attenuation of inflammatory response in macrophages through enhanced secretion of EVs from the myotubes.

We appreciate your comments and suggestions. Ambattu et al. in their report stated that the high frequency acoustic stimulation they used has a less effect on cell membranes than the 1 MHz ultrasound that we used in this study. Deng et al. and Li et al. applied low intensity pulsed ultrasound (LIPUS) (about 300 mW/cm2) in their studies. In this study, we assumed that ultrasound induced increase in EV secretion via increased Ca2+ influx into the cell by enhancing cell membrane permeability, and since it has been reported that the effect of ultrasound-induced enhancement in cell membrane permeability increases in an intensity-dependent manner (Zeghimi et al., 2015), we applied intensities of 1-3 W/cm2. While previous studies using LIPUS have used 15 minutes of irradiation, the high intensity employed in this study was capable to promote EV release after 5 minutes of stimulation. We have added the above explanation to the introduction in the revised version of the manuscript. Furthermore, while the previous studies used other types of cells, the main purpose of this study was to determine the optimal ultrasound intensity to promote EV release from skeletal muscle and to determine whether ultrasound-induced EVs are qualitatively altered compared to those released under normal conditions, thereby validating the anti-inflammatory effects of ultrasound-induced muscle EVs. Our previous study (Maeshige et al. 2021) used the same muscle cells but did not investigate an intensity dependence, so this is the first study to show that ultrasound irradiation promotes EV release in an intensity-dependent manner in muscle. In addition, we would like to emphasize that this study also goes beyond our previous study in the method of stimulation. Specifically, the present study a more efficient 5-minute irradiation protocol was used, whereas the previous study have adopted a 9-minute intervention.

We understand that the results of this study are predictable from two of our previous studies, but since stimulus-induced EVs may be qualitatively different compared to EVs released under normal conditions (Kawanishi et al., 2023; Li et al., 2023), it is worthwhile to examine the effects of stimulus-induced EVs. This explanation has been added in the introduction of revised version of the manuscript.

The authors' claim that 'the role of Ca2+ in ultrasound-induced EV release and its intensity-dependency are still unclear', and that the aim of the present work is to clarify the mechanism, is somewhat overstated. That ultrasonic stimulation alters intracellular Ca2+ to lead to EV release, therefore establishing their interdependency and hence demonstrating the mechanism by which EV secretion is enhanced by the ultrasonic stimulation, was detailed in Ambattu et al., Commun Biol 3, 553, 2020. While this was carried out at a slightly higher frequency (10 MHz) and slightly different form of ultrasonic stimulation, the same authors have appeared to since establish that a universal mechanism of transduction across an entire range of frequencies and stimuli (Ambattu, Biophysics Rev 4, 021301, 2023).

In this study, we showed that Ca2+ is involved in ultrasound-induced EV release using Ca2+-depleted culture medium, but since we did not examine the mechanism in more detail than that, we modified the introduction to avoid overstating.

Similarly, the anti-inflammatory effects of EVs on macrophages have also been extensively reported (Li et al., J Nanobiotechnol 20, 38, 2022; Lo Sicco et al., Stem Cells Transl Med 6, 3, 2017; Hu et al., Acta Pharma Sin B 11, 6, 2021), including that by the authors themselves in a recent study on the same C2C12 myotubes (Yamaguchi et al., Front Immunol 14, 1099799, 2023). Moreover, the authors' stated aim for the present work - clarifying the mechanism of the anti-inflammatory effects of ultrasound-induced skeletal muscle-derived EVs on macrophages - appears to be somewhat redundant given that they simply repeated the microRNA profiling study they carried out in Yamaguchi et al., Front Immunol 14, 1099799, 2023. The only difference was that a fraction of the EVs (from identical cells) that they tested were now a consequence of the ultrasound stimulation they imposed.

That the authors have found that their specific type of ultrasonic stimulation maintains this EV content (i.e., microRNA profile) is novel, although this, in itself, appears to be of little consequence to the overall objective of the work which was to show the suppression of macrophage pro-inflammatory response due to enhanced EV secretion under the ultrasonic irradiation since it was the anti-inflammatory effects were attributed to the increase in EV concentration and not their content.

In comparison with the current study, our previous study observed EVs secreted only from muscle in normal condition. However, the purpose of the current study is to answer the question whether ultrasound treatment could enhance the effect of EVs and change the encapsuled miRNAs. Although we identified several miRNAs which are specifically induced by ultrasound, further studies are needed to demonstrate the effect of those miRNAs derived from ultrasound-treated muscles on macrophages. We have mentioned this limitation in the discussion of the revised manuscript.  

Reviewer #1 (Recommendations For The Authors):

This reviewer felt that there was a lack of novelty in the manuscript and that the results of the work confirm conclusions that could have been logically deduced from a combination of the authors' preceding work (Maeshige et al., Ultrasonics 110, 106243, 2021 and Yamaguchi et al., Front Immunol 14, 1099799, 2023). The contribution of the work could perhaps be elevated if the authors were to focus more on whether the 0.01% of altered miRNA has any impact on cellular activity.

As mentioned above, the present study is novel compared to our previous studies for examining the effects of ultrasound-induced EVs. In addition, the fact that EV content is maintained after ultrasound stimulation rather indicates that ultrasound can be used as a highly stable and effective method of promoting EV release.

A further, albeit more minor, recommendation is to omit lines 73-80 in the manuscript. The discussion on physical exercise for promoting EV secretion together with the non-invasive nature of ultrasound therapy is very misleading as it creates the impression that the authors' work can be applied as a direct intervention on a patient. This was not shown in the work, which was limited to irradiating cells ex vivo.

We agree and have edited the introduction.

Reviewer #2 (Public Review):

1. The exploration of output parameters for US induction appears limited, with only three different output powers (intensities) tested, thus narrowing the scope of their findings.

We appreciate your comments and suggestions. The intensity of LIPUS is basically in the ~0.3 W/cm2 range, and in clinical practice, ~2.5 W/cm2 is considered to be a safe intensity to irradiate the human body (Draper, 2014). Therefore, 3.0 W/cm2 is also a fairly high intensity for the human body, so 3.0 W/cm2 was set as the maximum intensity in this study.

1. Their claim of elucidating mechanisms seems to be only partially met, with a predominant focus on the correlation between calcium responses and EV release.

The focus of this study was to examine the effects of ultrasound-induced EVs on the inflammatory responses of macrophages and not on the detailed mechanism of calcium involvement. We revised the introduction to make the purpose of this study clearer.

1. While the intracellular calcium response is a dynamic activity, the method used to measure it could risk a loss of kinetic information.

Although we did not examine the kinetic action of calcium, we believe that Ca2+ is at least proven to be involved to the EV-promoting effect of ultrasound on muscle, since the enhancement of EV release by ultrasound was canceled by elimination of calcium from the culture medium. Furthermore, real-time measurement of Ca2+ after ultrasound irradiation has shown that ultrasound irradiation promotes Ca2+ influx into cells immediately after the irradiation. (Fan et al., 2010).  

1. The inclusion of miRNA sequencing is commendable; however, the interpretation of this data fails to draw clear conclusions, diminishing the impact of this segment.

Although we identified several miRNAs which are specifically induced by ultrasound, further studies are needed to demonstrate the effect of those miRNAs derived from US-treated muscles on macrophages. We have mentioned this limitation in the discussion of the revised version of manuscript.

While the authors have shown the anti-inflammatory effects of US-induced EVs on macrophages, there are gaps in the comprehensive understanding of the mechanisms underlying US-induced EV release. Certain aspects, like the calcium response and the utility of miRNA sequencing, were not fully explored to their potential. Therefore, while the study establishes some findings, it leaves other aspects only partially substantiated.

As stated above, the main purpose of this study was to examine the effects of ultrasound-induced EVs on the inflammatory responses of macrophages. We set detailed investigation on the mechanism of ultrasound-induced EV release as our next step and have revised the introduction and discussion of the revised manuscript to make the purpose and limitation of this study clearer.  

Reviewer #2 (Recommendations For The Authors):

The author's exploration into the role of Ca2+ in the context of US-induced EV release is a timely endeavor, especially given the growing interest in understanding the cellular dynamics associated with external stimulants like ultrasound. Nevertheless, the manuscript does not unambiguously define the mechanism of action and its broader implications.

Ca2+ has long been established as a versatile intracellular messenger, governing a myriad of cellular processes. There is a wealth of methodologies, from specific inhibitors to specialized assays, tailored to dissect the role of Ca2+ in diverse contexts. In the specific case of US-induced Ca2+ activity, the expectation would be for a clear, mechanistic delineation of how this ionic surge drives EV release. Yet, this study stops short of providing those details. It is imperative for the authors to dig deeper, employing a diverse set of tools at their disposal, to fill this knowledge gap.

Recently, it was reported that increased Ca2+ influx causes an increase in EV secretion via the plasma membrane repair protein annexin A6 (Williams et al. 2023). However, the full mechanism of how an increase in intracellular Ca2+, let alone ultrasound-induced Ca2+, promotes EV release has not yet been understood yet, and it is beyond the scope of this study to elucidate this part of the mechanism.

Furthermore, the paper raises another important question: Which specific proteins are pivotal in orchestrating the US-induced Ca2+ entry in myotubes? Addressing this would not only enhance the manuscript's novelty but would also contribute a vital piece to the puzzle of understanding US-cellular interactions.

Ultrasound increases Ca2+ uptake by increasing cell membrane permeability by sonoporation, rather than via protein reactions (Fan et al., 2010). We added this explanation to the introduction in the revised version of manuscript.  

Lastly, while the report touches upon the influence of varying US output power on EV concentrations, it piques curiosity about potential effects beyond the 3W/cm2 threshold. It's observed that cell viability isn't compromised at this intensity, suggesting room for further exploration. Would a higher intensity yield a proportionally increased EV release, or is there a saturation point? Conversely, could intensities beyond 3W/cm2 begin to have deleterious effects on the cells? These are crucial considerations that merit investigation to realize the full potential of US as a modulatory tool, both for research and therapeutic applications.

As mentioned above, 3.0 W/cm2 was adopted as the maximum intensity in this study with reference to the intensity used in clinical practice. In addition, since the cytotoxicity and therapeutic effects of ultrasound depend not only on intensity but also on other parameters such as duty cycle, acoustic frequency, pulse repetition frequency and duration, so a comprehensive analysis of the effects of ultrasound on cells at various parameter settings would be valuable as an independent study.

Author Response

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

We greatly appreciate your positive assessment and the comments by the two reviewers on the previous version of our manuscript, all of which are very helpful and greatly improved our manuscript. We have incorporated all changes and corrections requested by these reviewers and we believe their suggestions have enhanced the overall quality of our manuscript.

As for Reviewer #1.

We thank Reviewer 1 very much for her/his very positive and detailed remarks, all of which have been introduced into the revised version of our manuscript.

We have added the information about the biological control on the development of phosphatic-shelled brachiopod columns in the introduction, so that our late narrative can be more understandable. The Cambrian Explosion is the innovation of metazoan body plans and radiation of animals during a relatively short geological time. The expansion of new body plans in different groups of brachiopods in the early Cambrian was likely driven by the Cambrian Explosion. The columnar architectures are not developed in living lingulate brachiopods, and thus it is important to get a better understanding of this extinct shell architecture from the fossil records on a global scale in order to study the evolutionary trend of shell architectures and compositions in brachiopods. We hope the current comparison study of columnar shell architectures from some of the oldest known brachiopods will help to pursue this goal. Furthermore, the adaptive innovation of biomineralized columnar architecture in early brachiopods is discussed in the revised manuscript.

As for Reviewer #2.

We thank Reviewer 2 very much for her/his very constructive and detailed remarks. All the comments have been thoroughly considered, and introduced into the revised version of the manuscript.

The current information on the shell structures of early linguliform brachiopods is unclear, which has been introduced in the revised manuscript and the supplementary Appendix 1. We also state that more detailed studies of the complexity and diversity of linguliform brachiopod architectures (especially their early fossil representatives) require further investigations. As the shell structure and biomineralization process are crucial to unravel the poorly resolved phylogeny and early evolution of Brachiopoda, in this paper, we undertake a primary study of exquisitely well-preserved brachiopods from the Cambrian Series 2. The shapes and sizes of microscopic cylindrical columns are described in detail in this research, and this work will be useful for further comparative studies on brachiopod shell architecture. The important reference paper on brachiopod shells by Butler et al. (2015) has been added to the revised manuscript. The structure and language of the manuscript are revised based on the very helpful suggestions.

Concerning the families Eoobolidae and Lingulellotretidae, we are aware of the current problematic situation of these families, and we have added more discussion about the detailed characters of Eoobolidae in the Systematic Palaeontology part of the manuscript. However, the revision of the families Eoobolidae and Lingulellotretidae falls outside the scope of this paper. We prefer to leave it now as it will be part of an upcoming publication based on more global materials from China, Australia, Sweden and Estonia that we are currently working on.

On behalf of my co-authors, I thank you for taking the time to consider our manuscript for publication in eLife and I hope that with the changes we have made to our paper, it is now suitable for publication. If you have any further questions about our revised manuscript, please do not hesitate to get in contact. Thank you very much for your time and consideration.

Author Response

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

The authors deeply appreciate the reviewer’s constructive criticism.

Answers to the public review from Reviewer 1

1. The pathogenesis of truncating LRRC23 in asthenozoospermia needs to be further considered. The molecular mechanism of LRRC23 demonstrated in mice should be tested in patients with the LRRC23 variant. As it may be difficult to determine the structures of RS3 in the infertile male sperm, the LRRC23 localization should be observed in the sperm from patients with the LRRC23 variant.

We understand the reviewer’s point. Unfortunately, the patients declined to continue in the project after the initial clinical evaluation and blood draw, so we were unable to follow up.

1. The absence of the RS3 head in LRRC23Δ/Δ mouse sperm is not sufficient to support the specific localization of LRRC23 in RS3 head. Although LRRC23 might bind to RS head protein RSPH9, the authors state that "RSPH9 is a head component of RS1 and RS2 like in C. reinhardtii (Gui et al, 2021), but not of RS3" as the protein level and the localization of RSPH9 is not altered in LRRC23Δ/Δ sperm. Thus, the specific localization of LRRC23 in RS3 head should be further confirmed.

Thank you for your comment. We agree with the reviewer that the specific localization of LRRC23 within the RS3 head needs to be further confirmed, but this requires an atomic resolution structure of the RS3 head, which is beyond the scope of the current study. We will pursue this direction in our future study.

3) The interaction between LRRC23 and RSPH9 needs to be defined. AlphaFold models could help determine the likelihood of a direct interaction. In addition, the structure of the 96-nm modular repeats of axonemes from the flagella of human respiratory cilia has been determined (PMID: 37258679), and the localization of LRRC23 in RS could be further predicted.

We appreciate the comment. We are pursuing an atomic resolution structure of the RS3 head, and thus leave the prediction and detailed localization to future studies.

4) The ortholog of the RSP15 may also be predicted or confirmed by using the reported structure in human respiratory cilia (PMID: 37258679). Whether the LRCC34 in RS2 is LRRC34?

Based on the amino acid sequence and AlphaFold predicted structure comparison, we proposed LRRC34 as the RSP15 orthologue. We agree that further clarification of whether the reported RSP15 structure in human respiratory cilia is LRRC34 is valuable, but we would like to focus the current study on re-annotating LRRC23 function to RS3 and male infertility.

Answers to the public review from Reviewer 2

1. While the author generated mutant mice expressing truncated LRRC23 proteins, the expression of these truncated proteins was not detected in sperm. This implies that, in terms of sperm structure, the mutant LRRC23 protein behaves similarly to the complete knockout of the LRRC23 protein, which has been previously reported and characterized (Zhang et al., 2021).

We partially agree with the reviewer’s comments. Indeed, the spermatozoa from truncated mutant LRRC23 mice may be similar to those from the complete knockout. However, the truncated LRRC23 in the testis could in part contribute to the assembly and structural organization of the RS3 head and/or bridge during spermatogenesis, and thus it is possible that complete absence of the LRRC23 could result in more severe structural defects in the RS3 and bridge structure. Therefore, to simply infer the same defects requires a direct comparison.

1. This reviewer questions the proposal that LRRC23 is an integral component of RS3, as the results indicate not only the loss of the RS3 head structure but also an incomplete RS2-RS3 junction structure. In addition, the interaction of LRRC23 with RSPH9 alone does not fully explain its involvement solely in RS3 assembly. Additional evidence is required to examine the influence of LRRC23 on the RS2-RS3 junction.

Thank you for the reviewer’s point. In a previous study, LRRC23 was detected in tracheal cilia that lack the bridge structure. Thus, we concluded that LRRC23 is a component in the RS3 head, but not necessarily in the RS2-RS3 bridge structure, although the bridge structure is also affected. Broad structural defects due to single protein loss of function are often observed in sperm flagella. For example, deficiency of RSPH6A, an RS head component, affects not only the RS structure but the entire flagellar structure in a non-uniform manner, resulting in multiple morphological flagellar abnormalities. We anticipate that our future study to determine the molecular architecture in the RS3 head and bridge structure will provide further insights into this question.

1. The article does not explore how these mutations affect the flagella structure in human sperm, which needs further study. Expanding the study to include human sperm structure would undoubtedly enhance the quality of the article.

We agree with the importance of further pursuing the effect of these mutations in human samples, but faced practical difficulties. As responded to reviewer 1, the patients not only dropped out of the project, but also are distantly located in remote region of Pakistan, making the application of cryo-ET not feasible.

Answers to the recommendations of Reviewer 1

1. The statistics analysis should be performed in Figures 2E and 2F.

We appreciate the reviewer’s recommendation. For 2E, since the standard deviations for two groups are equal to 0, it is not possible to perform appropriate statical analyses. For 2F, since the knockout males do not sire, it is not possible to know the number of litters in this case. Therefore, litter size information is not available for knockout males, and statistical analyses are not applicable.

1. In Figure 3A, the human sperm RS structures (PMID: 36593309) should be provided.

Thanks for the suggestion. We have included human sperm RS structures as suggested.

1. The molecular weight markers should also be added in Figure 3F (left), EV4B, and EV5B (AKAP3, RSPH9, AcTub).

In the original Figure 3F, the markers were shown as the white lines in the blot images due to the space limitations. Since the previous markers are not clearly visible, we have changed the color to yellow. The marker information in EV4B and 5B has also been updated.

Answers to the recommendations of Reviewer 2

1. Line 119, Table S1 is incorrectly shown.

We have corrected the Table nomenclature to Table EV1.

1. Line 132, the author suggests that LRRC23 mutations do not affect female reproduction based on the fertility of the mother. However, this conclusion may lack rigor since it overlooks the sterility of IV-4. To address this, the author needs to examine the fertility of female mice more comprehensively. Additionally, considering the higher expression level of LRRC23 in the oviduct, the author should investigate any potential changes in the oviduct cilia.

Thank you for the reviewer’s comment. As described in line 134, the mother of IV-4, who also carries the homozygous mutant allele like IV-4, was fertile. In addition, Lrrc23Δ/Δ female mice are fertile (now added in lines 173-174). In fact, we maintain the mouse line by crossing Lrrc23Δ/Δ females with heterozygous males. Thus, our initial conclusion that the LRRC23 mutation does not cause female fertility is still valid. However, LRRC23 has a function in the regulation of oviductal cilia requires further study, so we have softened down the corresponding sentence.

1. In the article, the author mentions that there are some morphological differences observed in the sperm, which are not clearly depicted in Fig.1B. It is essential to specify the specific changes in sperm morphology that the author identified.

Thank you for your comment. The morphological variations (e.g., the sperm in the lower left corner of Fig.1B has more a rounded sperm head) meant overall normal morphology with the normal range of occurrence in abnormal sperm morphology in normal fertile men, not necessarily caused by the LRRC23 mutation. To avoid confusion, we have rephrased the sentence (see lines 122-124).

1. In Fig.3F, the previous study confirmed an interaction between LRRC23 and RSPH3 (Zhang et al., 2021), but the current manuscript does not demonstrate such an interaction; the author should explain the text.

We appreciate your point. This could be due to the different interaction condition in vitro, and we described the possibility in main text (See Lines 200-201).

1. In the case of the interaction between LRRC23 and RSPH9, the author utilizes human protein to detect but conducts phenotype verification in mice. Thus, discussing the relevance and potential limitations of extrapolating these findings from human protein interactions to the phenotypic effects

Thank you for the reviewer’s suggestion. We added discussion for that part (lines 336-341).

1. The authors needed to detect changes in LRRC23 protein and mRNA levels at different stages of spermatogenesis.

We agree that expression profiling of LRRC23 protein levels in developing male germ cells will be helpful to further understand LRRC23 function in spermatogenesis, but we do not perceive that it is not critical in this study as LRRC23 mRNA expression profiling from scRNA database (Fig. EV4) hints at the protein profiles.

1. In Figure 4C of the article, the author should provide a clear and detailed explanation in the text of how they distinguish RS1, RS2, and RS3.

We added the information in figure legends (lines 1034-1037).

1. Zoom in on the RS structure in Fig.EV5D for precise observation.

In TEM images with limited resolution, we could not tell which RS (RS1, 2, or 3) we have in the cross-section, and simple zoom-in does not provide a better and/or more accurate observation (the main reason, we moved forward with cryo-ET).

1. By utilizing computational modeling and bioinformatics tools, the authors gain insights into the potential interactions, binding sites, and structural features of LRRC23 within the RS3 complex. This approach provides a deeper understanding of LRRC23's function and role in the assembly and stability of the RS3 complex. To enhance the clarity and visualization of the findings, the authors should generate a schematic diagram that illustrates the proposed interactions and structural organization of LRRC23 within the RS3 complex.

We appreciate the reviewer’s suggestion to speculate the molecular position and interaction of LRRC23 within the RS3 complex. For the level of computational modeling and bioinformatics, we believe that purification of RS3 complex and LRRC23 interactome study is required, which is one of our future directions. Given the limitation of our current data, we choose to stay conservative and not to suggest detailed structural information of LRRC23 in RS3 complex.

Author Response

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

Re: Revised author response for eLife-RP-RA-2023-90135 (“The white-footed deermouse, an infection-tolerant reservoir for several zoonotic agents, tempers interferon responses to endotoxin in comparison to the mouse and rat” by Milovic, Duong, and Barbour”)

The revised manuscript has taken into account all the comments and questions of the two reviewers. Our responses to each of the comments are detailed below. In brief, the modifications or additional materials for the revision each specifically address a reviewer comment. These modifcations or materials include the following….

• a more in-depth consideration of sample sizes

• a better explanation of what p values signify for a GO term analysis

• a more detailed account of the selection of the normalization procedure for cross-species targeted RNA-seq (including a new supplemental figure)

• several more box plots in supplementary materials to complement the scatterplots and linear regressions of the figures of the primary text

• provision in a public access repository of the complete data for the RNA-seq analyses as well as primary data for figures and tables as new supplementary tables

• the expansion of description of the analysis done for the revision of Borrelia hermsii infection of P. leucopus. This included a new table (Table 10 of the revision) • development of the possible relevance of finding for longevity studies by citing similarities of the findings in P. leucopus with those in the naked mole-rat

• what we think is a better assessment of differences between female and male P. leucopus for this particular study, while still keeping focus on DEGs in common for females and males. This included a new figure (Figure 4 of the revision).

• removal of reference to a “inverse” relationship between Nos2 and Arg1 while still retaining ratios of informative value

We note that in the interval between uploading the original bioRxiv preprint and now we learned of the paper of Gozashti, Feschotte, and Hoekstra (reference 32), which supports our conception of the important place of endogenous retroviruses in the biology and ecology of deermice. This is the only addition or modification that was not a direct response to a reviewer comment or question, but it was germane to one of Reviewer #1’s comments (“Regarding..”).

Reviewer #1:

Supplemental Table 1 only lists genes that passed the authors statistical thresholds. The full list of genes detected in their analysis should be included with read counts, statistics, etc. as supplemental information.

We agree that provision of the entire lists of reference transcripts and the RNA-seq results for each of the 40 animals is merited. These datasets are too large for what the journal’s supplementary materials resource was intended for, so we have deposited them at the Dryad public access repository.

While P. leucopus is a critical reservoir for B. burgdorferi, caution should be taken in directly connecting the data presented here and the Lyme disease spirochete. While it's possible that P. leucopus have a universal mechanism for limiting inflammation in response to PAMPs, B. burgdorferi lack LPS and so it is also possible the mechanisms that enable LPS tolerance and B. burgdorferi tolerance may be highly divergent.

The impetus for the study was the phenomenon of tolerance of infection of P. leucopus by a number of different kinds of pathogens, not just B. burgdorferi. We take the reviewer’s point, though. Certainly, the white-footed deermouse is probably most notable at-large for its role as a reservoir for the Lyme disease agent. We doubt that the species responses to LPS and to the principal agonists of B. burgdorferi are “highly divergent”, though. Other than the TLR itself-TLR4 for LPS vs the heterodimer TLR2/TLR1 for the lipoproteins of these spirochetes--the downstream signaling is generally similar for amounts comparable in their agonist potency.

We had thought that we had addressed this distinction for B. burgdorferi and other Borreliaceae members by referring to the earlier study. But we agree with the reviewer that what was provided on this point was insufficient in the context of the present work. Accordingly, for the revision we have added a new analysis of the data on experimental infection of P. leucopus with Borrelia hermsii, which lacks LPS and for which the TLR agonists eliciting inflammation are lipoproteins. We do this in a format (new Table 6) that aids comparison with the LPS experimental data elsewhere in the article. As the manuscript references, B. burgdorferi infection of P. leucopus elicits comparatively little inflammation in blood even at the height of infection. While this phenomenon with the Lyme disease agent was part of the rationale driving these studies, the better comparison with LPS was 5 days into B. hermsii infection when the animals are spirochetemic.

Statistical significance is binary and p-values should not be used as the primary comparator of groups (e.g. once a p-value crosses the deigned threshold for significance, the magnitude of that p-value no longer provides biological information). For instance, in comparing GO-terms, the reason for using of high p-value cutoffs ("None of these were up-regulated gene GO terms with p values < 1011 for M. musculus.") to compare species is unclear. If the authors wish to compare effect sizes, comparing enrichment between terms that pass a cutoff would likely be the better choice. Similarly, comparing DEG expression by p-value cutoff and effect size is more meaningful than analyses based on exclusively on p-value: "Of the top 100 DEGs for each species by ascending FDR p value." Description in later figures (e.g. Figure 4) is favored.

Effect sizes--in this case, fold-changes--were taken into account for GO term analysis and were specified in the settings that are described. So, any gene that was “counted” for consideration for a particular GO term would have passed that threshold and with a falsediscovery corrected p value of a specified minimum. There is no further scoring of the “hit” based upon the magnitude of the p value beyond that point. It is, as the reviewer writes, binary at that point. We are in agreement on those principles.

As we understand the comment above, though, the p-values referred to are in regard to the GO term analysis itself. The objective was discovery followed by inference. The situation was more like a genome-wide association study (GWAS) study. This is not strictly speaking a hypothesis test, because there was no stated hypothesis ahead of time or one driving the design. The “p value” for something like GO term analysis or GWAS provides an estimate of the strength of the association. It is not binary in that sense. The lower the p value, the greater confidence about the association. In a GWAS of a human population an association of a trait with a particular SNP or indel is usually not taken seriously unless the p value is less than 10^-7 or 10^-8. In the case of GO terms, the p value approximates (but is not equivalent to) the number of genes that are differentially expressed that belong to a GO cluster out of the total number of genes that define that cluster. The higher the proportion of the genes in the cluster that are associated with a treatment (LPS vs. saline), the lower the p value. Thus, it provides information beyond the point at which it would be rightly deemed of little additional value in many hypothesis testing circumstances.

That said, we agree that the original manuscript could have been clearer on this point and have for the revision expanded the description of the GO term analysis in the Methods, including some explanation for a reader on what the p value signifies here. We also refrain from specifying a certain p value for special attention and merely list 20 by ascending p value.

The ability to use of CD45 to normalize data is unclear. Authors should elaborate both on the use of the method and provide some data how the data change when they are normalized. For instance, do correlations between untreated Mus and Peromyscus gene expression improve? The authors seem to imply this should be a standard for interspecies comparison and so it would be helpful to either provide data to support that or, if applicable, use of the technique in literature should be referenced.

The reviewer brings up an important point that we considered addressing in more depth for the original manuscript but in the end deferred to considerations about length and left it out.

But we are glad to address this here, as well as in the revised manuscript.

We did not intend to imply either that this particular normalization approach had been done before by others or that it “should” be a standard. We are not aware of another report on this, and it would be up to others whether it would be useful or not for them. We made no claim about its utility in another model or circumstance. The challenge before us was to do a comparative analysis of transcription in the blood not just for animals of one species under different conditions but animals of two different genera under different conditions. A notable difference between the animals was in their white blood cell counts, as this study documents. White cells would be the source of a majority of transcripts of potential relevance here, but there would also be mRNA for globins, from reticulocytes, from megakaryocytes, and likely cell-free RNA with origins in various tissues. If the white cell numbers differed, but the non-white cell sources of RNA did not, then there could be unacknowledged biases.

It would be like comparing two different kinds of tissues and assuming them to be the same in the types and numbers of cells they contained. Four hours after a dose of LPS the liver cells (or brain cells) would differ in their transcriptional profiles from untreated the livers (or brains) of untreated animals for sure, but there would not be much if any change in the numbers of different kinds of cells in the liver (or brain) within 4 hours. The blood can change a lot in composition within that time frame under these same conditions. Some sort of accounting for differing white cell numbers in the blood in different outbred animals of two species seemed to be called for.

The normalization that was done for the genome-wide analysis was not based on a particular transcript, but instead was based on the total number of reads, the lengths of the reference transcripts, and the distributions of reads matching to the tens of thousands of references for each sample. This was done according to what are standard procedures by now for bulk RNAseq analyses. Because the reference transcript sets for P. leucopus and M. musculus differed in their numbers and completeness of annotation, we did not attempt any cross-species comparison for the same set of genes at that point. That would not be possible because they were not entirely commensurate.

The GO term analysis of those results provided the leads for the more targeted approach, which was roughly analogous to RT-qPCR. For a targeted assay of this sort, it is common to have a “housekeeping gene” or some other presumably stably transcribed gene for normalization. A commonly used one is Gapdh, but we had previously found that Gapdh was a DEG itself in the blood in P. leucopus and M. musculus at the four hour mark after LPS. The aim was to provide for some adjustment so datasets for blood samples differing in white blood cell counts could be compared. Two options were the 12S ribosomal RNA of the mitochondria, which would be in white cells but not mature erythrocytes, and CD45, which has served an approximately similar function for flow cytometry of the blood. As described in what has been added for the revision and the supplementary materials, we compared these different approaches to normalization. Ptprc and 12S rRNA were effectively interchangeable as the denominator with identifying DEGs of P. leucopus and M. musculus and cross-species comparisons.

Regarding the ISG data-is a possible conclusion not that Peromyscus don't upregulate the antiviral response because it's already so high in untreated rodents? It seems untreated Peromyscus have ISG expression roughly equivalent to the LPS mice for some of the genes. This could be compared more clearly if genes were displayed as bar plots/box and whisker plots rather than in scatter plots. It is unclear why the linear regression is the key point here rather than normalized differences in expression.

In answer to the question: yes, that is possible. In the interval between uploading of the manuscript and this revision, we became aware of a study by Gozashti and Hoekstra published this year in Molecular Biology and Evolution (reference 32) and reporting on the “massive invasion” of endogenous retroviruses in P. maniculatus and the defenses deployed in response to achieve silencing. We cite this work and discuss it, including related findings for P. leucopus, in the revision.

We had originally intended to include box plots as well as scatterplots with regressions for the data, but thought it would be too much and possibly considered redundant. But with this encouragement from the reviewer we provide additional box plots in supplementary materials for the revision.

Some sections of the discussion are under supported:

The claim that low inflammation contributes to increased lifespan is stated both in the introduction and discussion. Is there justification to support this? Do aged pathogen-free mice show more inflammation than aged Peromyscus?

We respectively point out that there was not a claim of this sort. We stated a fact about P. leucopus’ longevity. We made no statement connecting longevity and inflammation beyond the suggestion in the introduction that the explanation(s) for infection tolerance might have some bearing for studies on determinants of life span.

But the reviewer’s comment prompted further consideration of this aspect of Peromyscus biology. This led eventually to the literature on the naked mole-rat, which seems to be the rodent with the longest known life span and the subject of considerable study. The discussion section of the revision has an added paragraph on some of the similarities of P. leucopus and the naked mole-rat in terms of neutrophils, expression of nitric oxide synthase 2 in response to LPS, and type 1 interferon responses. While this is far from decisive, it does serve to connect some of the dots and, hopefully, is considered at least partially responsive to the reviewer’s question.

The claim that reduced Peromyscus responsiveness could lead to increased susceptibility to infection is prominently proposed but not supported by any of the literature cited.

There was not this claim. In fact, it was framed as a question, not a statement. Nevertheless, we think we understand what the comment is getting at and acknowledge in the revision that there may be unexamined circumstances in which P. leucopus may be more vulnerable.

References to B. burgdorferi, which do not have LPS, in the discussion need to ensure that the reader understands this and the potential that responses could be very different.

We think we addressed this comment in a response above.

Reviewer #2:

1. How were the number of animals for each experiment selected? Was a power analysis conducted?

A power analysis of any meaning for bulk RNA-seq with tens of thousands of reference transcripts, each with their own variance, and a comparison of animals of two different genera is not straight forward. Furthermore, a specific hypothesis was not being tested. This was a broad, forward screen. But the question about sample sizes is one that deserves more attention than the original manuscript provided. This now provided in added text in two places in Methods ( “RNA-seq” and “Genome-wide different gene expression”) in the revision.

1. The authors conducted a cursory evaluation of sex differences of P. leucopus and reported no difference in response except for Il6 and Il10 expression being higher in the males than the females in the exposed group. The data was not presented in the manuscript. Nor was sex considered for the other two species. A further discussion of the role that sex could play and future studies would be appreciated.

We agree that the limited analysis of sex differences and the undocumented remark about Il6 and Il10 expression in females and males warranted correction. For the revision we removed that analysis of targeted RNA-seq of P. leucopus from the two different studies. For this study we were looking for differences that applied to both species. This was the reason that there were equal numbers of females and males in the samples. We agree that further investigation of differences between sexes in their responses is of interest but is probably best left for “future studies”.

But in revision we do not entirely ignore the question of sex of the animal and provide an additional analysis of the bulk RNA-seq for P. leucopus with regard to differences between females and males. This basically demonstarted an overall commensurability between sexes, at least for the purposes of the GO term analysis and subsequent targeted RNA-seq, but did reveal some exceptions that are candidate genes for those future studies.

In the revision, we also add for the discussion and its “study limitations” section a disclaimer about possibly missing sex associated differences because the groups were mixed sexes.

1. The ratio of Nos2 and Arg1 copies for LPS treated and control P. leucopus and M.musculus in Table 3 show that in P. leucopus there is not a significant difference but in M.musculus there is an increase in Nos2 copies with LPS treatment. The authors then used a targeted RNA-seq analysis to show that in P. leucopus the number of Arg1 reads after LPS treatment is significantly higher than the controls. These results are over oversimplified in the text as an inverse relationship for Nos2/Arg1 in the two species.

We agree. In addition to providing box plots for Arg1 and Nos2, as suggested by Reviewer #1, we also replaced “ratio” in commenting on Arg1 and Nos2, with “differences in Nos2 and Arg1 expresssion” replacing “ratio of Nos2 to Arg1 expression” at one place. At another place we have removed “inverse” with regard to Nos2 and Arg1. But we respectfully decline to remove Nos2/Arg1 from Figure 5 (now Figure 6) or inclusion of Nos2/Arg1 ratios elsewhere. According to our understanding there need not be an inverse relationship for a ratio to have informative value.

Recommendations For the Authors

We thank the two reviewers for their constructive recommendations and suggestions, in some case pointing out errors we totally missed. For the great majority, the recommendations were followed. Where we decline or disagree we explain this in the response.

Reviewer #1 (Recommendations For The Authors):

• How was the FDR < 0.003 cutoff chosen for DEG? All cutoffs are arbitrary but there should be some justification.

We agree and have provided the rationale at that point in the paper (before Figure 3) in R2: "For GO term analysis the absolute fold-change criterion was ≥ 2. Because of the ~3-fold greater number of transcripts for the M. musculus reference set than the P. leucopus reference set, application of the same false-discovery rate (FDR) threshold for both datasets would favor the labeling of transcripts as DEGs in P. leucopus. Accordingly, the FDR p values were arbitrarily set at <5 x 10-5 for P. leucopus and <3 x 10-3 for M. musculus to provide approximately the same number of DEGs for P. leucopus (1154 DEGs) and M. musculus (1266 DEGs) for the GO term comparison."

• It would be helpful to include a figure demonstrating the correlation between CD45 and WBC ("Pearson's continuous and Spearman's ranked correlations between log-transformed total white blood cell counts and normalized reads for Ptprc across 40 animals representing both species, sexes, and treatments were 0.40 (p = 0.01) and 0.34 (p = 0.03), respectively.")

In both the first version of the revision (R1) and in R2 we provide a fuller explanation of the choice of CD45 (Ptprc) for normalization as detailed in the response to Reviewer #1's public comment. In the revision only Pearson's correlation and p value is given. We did not think another figure was justified after there was additional space devoted to this in both R1 and R2.

• Unclear what the following paragraph is referring to-is this from the previous paper? Was this experiment introduced somewhere? "Low transcription of Nos2 and high transcription of Arg1 both in controls and LPS-treated P. leucopus was also observed in the experiment where the dose of LPS was 1 µg/g body mass instead of 10 µg/g and the interval between injection and assessment was 12 h instead of 4 h (Table 4)."

This experiment is described in the Methods in the original and subsequent versions, but we agree that it is not clear whether it was from present study or previous one. Here is the revised text for R2: "Low transcription of Nos2 in both in controls and LPS-treated P. leucopus and an increase in Arg1 with LPS was also observed in another experiment for the present study where the dose of LPS was 1 µg/g body mass instead of 10 µg/g and the interval between injection and assessment was 12 h instead of 4 h (Table 4)."

• Regarding the differences in IFNy between outbred and BALB/c mice-are there any other RNA-seq datasets you can mine where other inbred mice (B/6, C3H, etc) have been injected with LPS and probed roughly the same amount of time later? Do they look like BALB/c or the outbreds?

In both the original and R1 and R2 we cite two papers on the difference of BALB/c mice. While this is of interest for follow-up in the future, we did not think additional content on a subject that mainly pertains to M. musculus was warranted here, where the main focus is Peromyscus.

• Figure 8 and its legend are difficult to follow. The top half of the figure is not well explained and it's unclear what species this is. Decreased use of abbreviations would help. Consider marking each R2 value as Mus or Peromyscus (As done in Fig 9). There are some typographical errors in the legend ("gree," incomplete sentence missing the words LPS or treatment AND Mus: "Co-variation between transcripts for selected PRRs (yellow) and ISGs (gree) in the blood of P. leucopus (P) or (M) with (L") or without (C)."

This is now Figure 9 in both R1 and R2. We revised it for R1 to include references to the box plots in supplementary materials, but agree with Reviewer #1's recommendation to correct the typos and make the legend less confusing. We did not think that further labeling of the R2 values in the scatterplots with the species names was necessary. The data points are not just colors but also different symbols, so it should be fairly easy for readers to distinguish the regression lines by species. For R2 this is the revised legend with additions in response to the recommendation underlined:

"Figure 9. Co-variation between transcripts for selected PRRs and ISGs in the blood of P. leucopus (P) or M. musculus (M) with (L) or without (C) LPS treatment. Top panel: matrix of coefficients of determination (R2) for combined P. leucopus and M. musculus data. PRRs are indicated by yellow fill and ISGs by blue fill on horizontal and vertical axes. Shades of green of the matrix cells correspond to R2 values, where cells with values less than 0.30 have white fill and those of 0.90-1.00 have deepest green fill. Bottom panels: scatter plots of log-transformed normalized Mx2 transcripts on Rigi (left), Ifih1 (center), and Gbp4 (right). The linear regression curves are for each species. For the right-lower graph the result from the General Linear Model (GLM) estimate is also given. Values for analysis are in Table S4; box plots for Gbp4, Irf7, Isg15, Mx2, and Oas1 are provided in Figure S6."

• Discussion section could benefit from editing for clarity. Examples listed: o Unclear what effect is described here "The bacterial infection experiment indicated that the observed effect in P. leucopus was not limited to a TLR4 agonist; the lipoproteins of B. hermsii are agonists for TLR2 (Salazar et al. 2009)."

Both R1 and R2 include the new section on the B. hermsii infection model. This was added in response to Reviewer #1 public comment. So the expanded consideration of this aspect should address the reviewer's recommendation for more clarity and context here. For R2 we modified the text in the discussion of R1:

"The analysis here of the B. hermsii infection experiment also indicated that the phenomenon observed in P. leucopus was not limited to a TLR4 agonist."

o Unclear what the takeaway from this paragraph is: "Reducing the differences between P. leucopus and the murids M. musculus and R. norvegicus to a single all-embracing attribute may be fruitless. But from a perspective that also takes in the 2-3x longer life span of the whitefooted deer mouse compared to the house mouse and the capacity of P. leucopus to serve as disease agent reservoir while maintaining if not increasing its distribution (Moscarella et al. 2019), the feature that seems to best distinguish the deer mouse from either the mouse or rat is its predominantly anti-inflammatory quality. The presentation of this trait likely has a complex, polygenic basis, with environmental (including microbiota) and epigenetic influences. An individual's placement is on a spectrum or, more likely, a landscape rather than in one or another binary or Mendelian category."

We agree that modification, simplication, and clarification was called for. In response to a public comment of Reviewer #1 we had changed that section, leaving out reference to longevity here. Here is the revised text in both R1 and R2:

"Reducing differences between P. leucopus and murids M. musculus and R. norvegicus to a single attribute, such as the documented inactivation of the Fcgr1 gene in P. leucopus (7), may be fruitless. But the feature that may best distinguish the deermouse from the mouse and rat is its predominantly anti-inflammatory quality. This characteristic likely has a complex, polygenic basis, with environmental (including microbiota) and epigenetic influences. An individual’s placement is on a spectrum or, more likely, a landscape rather than in one or another binary or Mendelian category."

Minor comments:

• Use of blue and red in figures as the -only- way to easily distinguish between groups is a poor choice-both in terms of how inclusivity of color-blind researchers and enabling grayscale printing. Most detrimental in Figure 2, but also slightly problematic in Figure 1. Use of color and shape (as done in other figures) is a much better alternative.

We agree. Both figures have been modified to include an additional characteristic for denoting the data point. For Figure 1 it is a black filling, and for Figure 2 it is the size of symbol in additon to the color. This should enable accurate visualization by color blind individuals and printing in gray scale. We have added definitions for the symbols within the graph itself, so there is no need to refer to the legend to interpret what they mean.

• Note the typo where it should read P leucopus: "The differences between P. musculus and M. musculus in the ratios of Nos2/Arg1 and IL12/IL10 were reported before (BalderramaGutierrez et al. 2021),"

We thank the reviewer for pointing this typo out, which also carried over to R1. It has been corrected for R2.

• Optional: Can the relationship between the ratios in figure 5 and macrophage "types" be displayed graphically alongside the graphs? It's a little challenging to go back and forth between the text and the figure to try to understand the biological implication.

We considered something like this but in the end decided that we were not yet comfortable assigning “types” in this fashion for Peromyscus.

Reviewer #2 (Recommendations For The Authors):

• Be consistent with nomenclature for your species/treatment groups in the text, figures, and tables. For example, you go back and forth between "P. leucopus" and "deermouse" in the text. And in figures you use "P," "Peromyscus", or "Pero".

In the Methods section of the original and revisions R1 and R2 we indicate that "deermouse" is synonymous with "Peromyscus leucopus" and "mouse" is synonymous with "Mus musculus" in the context of this paper. We think that some alternation in the terms relieves the text of some of its repetitiveness and that readers should not have a problem with equating one with the other. The use of "deermouse" also reinforces for readers that Peromyscus is not a mouse. With regard to the abbreviations for P. leucopus, those were used to accommodate design and space issues of the figures or tables. In all cases, the abbreviations referred to are defined in the legends of the figures. So, we respectfully decline to follow this recommendation.

• Often the sentence structure and/or word choice is irregular and makes quick/easy comprehension difficult. Several examples are:

o The third paragraph of the introduction

We agree that the first and second sentences are unclear. Here is the revision for R2:

“As a species native to North America, P. leucopus is an advantageous alternative to the Eurasian-origin house mouse for study of natural variation in populations that are readily accessible (9, 53). A disadvantage for the study of any Peromyscus species is the limited reagents and genetic tools of the sorts that are applied for mouse studies.”

o The first line after Figure 5 on page 9.

We agree. The long sentence which we think the reviewer is referring to has been in split into two sentences for R2.

“An ortholog of Ly6C (13), a protein used for typing mouse monocytes and other white cells, has not been identified in Peromyscus or other Cricetidae family members. Therefore, for this study the comparison with Cd14 is with Cd16 or Fcgr3, which deermice and other cricetines do have.”

o The sentence that starts "Our attention was drawn to..." on page 14.

We agree that the sentence was awkward and split into two sentences.

“Our attention was drawn to ERVs by finding in the genome-wide RNA-seq of LPS-treated and control rats. Two of the three highest scoring DEGs by FDR p value and fold-change were a gagpol polyprotein of a leukemia virus with 131x fold-change from controls and a mouse leukmia virus (MLV) envelope (Env) protein with 62x fold-change (Dryad Table D5).”

• For figures with multiple panels, use A), B) etc then indicate which panel you are discussing in your text. This is a very data heavy study and your readers can easily get lost.

We agree and have added pointers in the text to the panels we are referring to. But we prefer to use easily understood descriptors like “left” and “upper” over assigned letters.

• For all the figures, where are the stats from the t-tests? Why didn't you do a two-way ANOVA? Instead of multiple t-tests?

Where we are not hypothesis testing and we are able to show all the data points in box-whisker plots with distributions fully revealed, our default position is not to apply significance tests in a post hoc fashion. If a reader or other investigator wants to do this for other purposes, e.g. a meta-analysis, the data is provided in public repository for them to do this. We are not sure what the reviewer means by "multiple t-tests" for "all figures". Where we do 2-tailed t-tests for presentation of data for many genes in a table for the targeted RNA (where individual values cannot shown in the table), there is always correction for multiple testing, as indicated in Methods. The p values shown as "FDR" are after correction.

• Results paragraph "LPS experiment and hematology studies"

o List the two species for the first description to orient the reader since you eventually include rat data.

We agree that this is warranted and followed this recommendation for R2.

o Not all the mice experienced tachypnea, but the text makes it seem like 100% did.

We are not sure what the reviewer is referring to here. This is what is in the text on tachypnea: "By the experiment’s termination at 4 h, 8 of 10 M. musculus treated with LPS had tachypnea, while only one of ten LPS-treated P. leucopus displayed this sign of the sepsis state (p = 0.005)." The only other mention of "tachypnea" was in Methods.

• Figure 1: Why was the M. musculus outlier excluded? Where any other outliers excluded?

That data point for the mouse was not "excluded" from the graph. It is identified (MM17) for reference with Table 1, and there is the graph for all to see where it is. It was only excluded from the regression curve for control mice. There was no significance testing. There were no other outliers excluded.

• Figure 3: explain the colors and make the scales the same for all the panels or at least for the upregulated DEGs and the downregulated DEGs.

We have modified the legend for Figure 3 to include fuller definitions of the x-axes and a description of the color spectrum. We decline to make the x-axis scale the same for all the panels because the horizontal bars in “transcription down” panels would take up only a small fraction of the space. The x-axes are clearly defined and the colors of the bars also indicate the differences in p-values. We doubt that readers will be misled. Here is the revised legend: “Figure 3. Gene Ontology (GO) term clusters associated with up-regulated genes (upper panels) and down-regulated genes (lower panels) of P. leucopus (left panels) and M. musculus (right panels) treated with LPS in comparison with untreated controls of each species. The scale for the x-axes for the panels was determined by the highest -log10 p values in each of the 4 sets. The horizontal bar color, which ranges from white to dark brown through shades of yellow through orange in between, is a schematic representation of the -log10 p values.”

• Results paragraph "Targeted RNA seq analysis"

o In the third paragraph, an R2 of 0.75 is not close enough to 1 to call it "~1"

What the reviewer is referring to is no longer in either R1 and R2, as detailed in the authors' response to public comments.

o In the 4th paragraph, where are your stats?

We have replaced terms like "substantially" and "marginally" with simple descriptions of relationships in the graphs.

"For the LPS-treated animals there was, as expected for this selected set, higher expression of the majority genes and greater heterogeneity among P. leucopus and M. musculus animals in their responses for represented genes. In contrast to the findings with controls, Ifng and Nos2 had higher transcription in treated mice. In deermice the magnitude of difference in the transcription between controls and LPS-treated was less."

• Figure 4: The colors are hard to see, I suggest making all the up regulated reads one color, the down regulated reads a different color, and the reads that aren't different black or gray.

This is now Figure 5 in R1 and R2. The selected genes that are highlighted in the panels are denoted not only by color but also by type of symbol. We do not think that readers will have a problem telling one from another even if color blind. The purpose of this figure was to provide an overview and a visual representation with calling out of selected genes, some of which will be evaluated in more detail later. We thought that this was necessary before diving deeper into the data of Table 2. We do not think further discriminating between transcripts in the categorical way that the reviewer suggests is warranted at this point. So, we respectfully decline to follow this suggestion.

• Results paragraph " Alternatively- activated macrophages...."

o Include a brief description of Nos2 and Arg1

We have defined what enzymes these are genes for in R2.

o How do you explain the lack of a difference in P. leucopus Arg1? Your text says the RT-qPCR confirms the RNA-seq findings.

There was a difference in P. leucopus Arg1 by RT-qPCR between control and LPS treated by about 3-fold. By both RNA-seq and RT-qPCR Arg1 transcription is higher in P. leucopus than in M. musculus under both conditions. But we have modified the sentence so that does not imply more than what the data and analysis of the table reveal.

"While we could not type single cells using protein markers, we could assess relative transcription of established indicators of different white cell subpopulations in whole blood. The present study, which incorporated outbred M. musculus instead of an inbred strain, confirmed the previous finding of differences in Nos2 and Arg1 expression between M. musculus and P. leucopus (Figure 5; Table 2). Results similar to the RNA-seq findings were obtained with specific RT-qPCR assays for Nos2 and Arg1 transcripts for P. musculus and M. musculus (Table 3)."

• Figure 5: reorganize the panels to make the text description and label with letters, where are the stats?

We thought the figure (now Figure 6) was self-explanatory, but agree that further explanation in the legend was indicated. We prefer to use descriptions of locations (“upper left”) over labels, like “panel C”, which do not obviously indicate the location of the panel. Of course, if the journal’s style mandates the other format we will do so. Our response about “stats” for boxplot figures is the same as what we provided above.

• Results paragraph "Interferon-gamma and interleukin-1 beta..."

o Either add the numbers or direct the viewer to where Ifng is in Table 2. The table is very big and Ifng is all the way at the bottom!

We agree that this table is large, but we thought it better to err on the side of inclusiveness by having a single table, rather than have some genes in the main article and other results in a supplementary table. We thought that it would make it easier for reviewers and readers to find a gene of interest, but we also acknowledge the challenge to locate the genes we highlight. We follow for R2 that reviewer's recommendation to provide some guidance for readers trying to locate a featured gene by pointing relative locations. While adding a column of numbers to already complex table seems more than what is called for, we are depositing an Excel spreadsheet of the table at the Dryad repository to facilitate searching by an interested reader for a particular gene.

• Figure 6: stats? The pink and red are hard to easily distinguish from each other. I also suggest not using red and green together for color blind readers.

With regard to the box-plots and significance testing, please see response above to an earlier recommendation. We have removed an interpretative adjective (i.e. "marked") from the description of the graph. Different symbols as well as colors are used, so we do not think that this will pose a problem for readers, even those with complete red-green color blindness. For what it’s worth, with regard to the "red" and "pink" issue, according to the figure on our displays the colors of the two symbols appear to be red and purple. They are also applied to different species and different conditions for those species.

• Figure 8: In the legend it says "... PRRs (yellow) and ISGs (gree)" which is a typo, but don't you mean blue not green anyways?

See response above to Reviewer #1's recommendation. This has been corrected.

Author Response

Reviewer #1 (Public Review):

Summary: The authors investigated the function of Microrchidia (MORC) proteins in the human malaria parasite Plasmodium falciparum. Recognizing MORC's implication in DNA compaction and gene silencing across diverse species, the study aimed to explore the influence of PfMORC on transcriptional regulation, life cycle progression and survival of the malaria parasite. Depletion of PfMORC leads to the collapse of heterochromatin and thus to the killing of the parasite. The potential regulatory role of PfMORC in the survival of the parasite suggests that it may be central to the development of new antimalarial strategies.

Strengths: The application of the cutting-edge CRISPR/Cas9 genome editing tool, combined with other molecular and genomic approaches, provides a robust methodology. Comprehensive ChIP-seq experiments indicate PfMORC's interaction with sub-telomeric areas and genes tied to antigenic variation, suggesting its pivotal role in stage transition. The incorporation of Hi-C studies is noteworthy, enabling the visualization of changes in chromatin conformation in response to PfMORC knockdown.

We greatly appreciate the overall positive feedback . Our application of CRISPR/Cas9 genome editing tools coupled with complementary cellular and functional approaches shed light on the importance ofPfMORC in maintaining chromatin structural integrity in the parasite and highlight this protein as a promising target for novel therapeutic intervention.

Weaknesses: Although disruption of PfMORC affects chromatin architecture and stage-specific gene expression, determining a direct cause-effect relationship requires further investigation.

Our conclusions were made on the basis of multiple, unbiased molecular and functional assays that point to the relevance of the PfMORC protein in maintaining the parasite’s chromatin landscape. Although we do not claim to have precise evidence on the step-by-step pathway to which PfMORC is involved, we bring forth first-hand evidence of its overall function in heterochromatin binding and gene-regulation, its association with major TF regulatory players, and essentiality for parasite survival. We however agree with the comment regarding the lack of direct effects of PfMORC KD and will provide additional evidence by performing ChIP-seq experiments against additional histone marks in WT and PfMORC KD lines.

Furthermore, while numerous interacting partners have been identified, their validation is critical and understanding their role in directing MORC to its targets or in influencing the chromatin compaction activities of MORC is essential for further clarification. In addition, the authors should adjust their conclusions in the manuscript to more accurately represent the multifaceted functions of MORC in the parasite.

We do agree with the reviewer's comment. Validation of the identified interacting partners is critical and most likely essential to understanding their role in directing MORC to its targets. However, our protein pull down experiments have been done using biological replicates. Several of the interacting partners have also been identified and published by other labs. A direct comparison of our work together with previous published work will be incorporated in a revised version of the manuscript to further validate the identified interacting partners and the accuracy of the data we obtained in this manuscript. Molecular validation of all proteins identified in our protein may take a few more years and will be submitted for publication in futur manuscripts.

Reviewer #2 (Public Review):

Summary: This paper, titled "Regulation of Chromatin Accessibility and Transcriptional Repression by PfMORC Protein in Plasmodium falciparum," delves into the PfMORC protein's role during the intra-erythrocytic cycle of the malaria parasite, P. falciparum. Le Roch et al. examined PfMORC's interactions with proteins, its genomic distribution in different parasite life stages (rings, trophozoites, schizonts), and the transcriptome's response to PfMORC depletion. They conducted a chromatin conformation capture on PfMORC-depleted parasites and observed significant alterations. Furthermore, they demonstrated that PfMORC depletion is lethal to the parasite.

Strengths: This study significantly advances our understanding of PfMORC's role in establishing heterochromatin. The direct consequences of the PfMORC depletion are addressed using chromatin conformation capture.

We appreciate the Reviewer’s comments and reflection on the importance of our work.

Weaknesses: The study only partially addressed the direct effects of PfMORC depletion on other heterochromatin markers.

Here again, we agree with the reviewer’s comment and intend to perform additional experiments to delve deeper into the multifaceted roles of PfMORC. We have begun to explore the effects of PfMORC depletion on heterochromatin marks using ChIP-seq experiments at distinct stages of parasite development. We hope our new results will shed light on the direct implications of PfMORC in heterochromatin regulation.

Author Response:

We would like to thank you very much for handling and reviewing our manuscript so carefully and to be so positive about our work. We are indeed grateful about these very concise and constructive reviews as well as about the Editorial Assessment. We basically agree with all reviewers' comments. Besides addressing all formal suggestions, we also decided to do some more experiments.

The main concern, the role of the transcription factor NF-YA1 during rhizobial infections, is indeed an absolut valid one. While the CDEL system has its beauties it certainly has its limitations as well. Thus, we will try to assess the role of NF-YA1 during symbiotic infections in Medicago more specifically. We will place NF-YA1 expression under the control of infection-specific promoters to limit pleiotropic effects of ectopic over-expression and assess rhizobial infections as well as cell cycle patterns in tranformed hairy roots producing the H3.1/H3.3 marker. Infection-inducible promoters will also be used to drive the ectopic expression of CYCD3;1 on the cortical infection thread trajectory to locally increase mitotic cycles, in order to test the functional importance of cell cycle exit on cortical infections.

We hope that we will be able to conclude more firmly on NF-YA1 function prior to locking the version of record and to deliver these experiments in a time frame of about 4-6 months, which is the minimum time we need for cloning the respective constructs, doing all hairy root transformations in sufficient numbers and quantitative microscopy.

Author Response:

Reviewer #1 (Public Review):

[...] Overall the manuscript is well written, and the successful generation of the new endogenous Cac tags (Td-Tomato, Halo) and CaBeta, stj, and stolid genes with V5 tags will be powerful reagents for the field to enable new studies on calcium channels in synaptic structure, function, and plasticity. There are also some interesting, though not entirely unexpected, findings regarding how Brp and homeostatic plasticity modulate calcium channel abundance. However, a major concern is that the conclusions about how "molecular and organization diversity generate functional synaptic heterogeneity" are not really supported by the data presented in this study. In particular, the key fact that frames this study is that Cac levels are similar at Ib and Is active zones, but that Pr is higher at Is over Ib (which was previously known). While Pr can be influenced by myriad processes, the authors should have first assessed presynaptic calcium influx - if they had, they would have better framed the key questions in this study. As the authors reference from previous studies, calcium influx is at least two-fold higher per active zone at Is over Ib, and the authors likely know that this difference is more than sufficient to explain the difference in Pr at Is over Ib. Hence, there is no reason to invoke differences in "molecular and organization diversity" to explain the difference in Pr, and the authors offer no data to support that the differences in active zone structure at Is vs Ib are necessary for the differences in Pr. Indeed, the real question the authors should have investigated is why there are such differences in presynaptic calcium influx at Is over Ib despite having similar levels/abundance of Cac. This seems the real question, and is all that is needed to explain the Pr differences shown in Fig. 1. The other changes in active zone structure and organization at Is vs Ib may very well contribute to additional differences in Pr, but the authors have not shown this in the present study, and rely on other studies (such as calcium-SV coupling at Is vs Ib) to support an argument that is not necessitated by their data. At the end of this manuscript, the authors have found an interesting possibility that Stj levels are reduced at Is vs Ib, that might perhaps contribute to the difference in calcium influx. However, at present this remains speculative.

Overall, the authors have generated powerful reagents for the field to study calcium channels and how they are regulated, but draw conclusions about active zone structure and organization contributing to functional heterogeneity that are not strongly supported by the data presented.

Reviewer 1 raises an interesting question that we agree will form the basis of important studies. Here, we set out to address a different question, which we will work to better frame. While we and others had previously found a strong correlation between calcium channel abundance and synaptic release probability (Pr (Akbergenova et al., 2018; Gratz et al., 2019; Holderith et al., 2012; Nakamura et al., 2015; Sheng et al., 2012)), more recent studies found that calcium channel abundance does not necessarily predict synaptic strength (Aldahabi et al., 2022; Rebola et al., 2019). Our study explores this paradox and presents findings that provide an explanation: calcium channel abundance predicts Pr among individual synapses of either low-Pr type-Ib or high-Pr type-Is inputs where modulating channel number tunes synaptic strength, but does not predict Pr between the two inputs, indicating an inputspecific role for calcium channel abundance in promoting synaptic strength. Thus, we propose that calcium channel abundance predictably modulates synaptic strength among individual synapses of a single input or synapse subtype, which share similar molecular and spatial organization, but not between distinct inputs where the underlying organization of active zones differs. Consistently, in the mouse, calcium channel abundance correlates strongly with release probability specifically when assessed among homogeneous populations of connections (Aldahabi et al., 2022; Holderith et al., 2012; Nakamura et al., 2015; Rebola et al., 2019; Sheng et al., 2012).

As Reviewer 1 notes, the two-fold difference in calcium influx at type-Is synapses is certainly an important difference underlying three-fold higher Pr. However, growing evidence indicates that calcium influx alone, like calcium channel abundance, does not reliably predict synaptic strength between inputs. For example, Rebola et al. (2019) compared cerebellar synapses formed by granule and stellate cells and found that lower Pr granule synapses exhibit both higher calcium channel abundance and calcium influx. In another example, Aldahabi et al. (2023) demonstrate that even when calcium influx is greater at high-Pr synapses, it does not necessarily explain differences in synaptic strength between inputs. Studying excitatory hippocampal CA1 synapses onto distinct interneuronal targets, they found that raising calcium entry at low-Pr inputs to high-Pr synapse levels is not sufficient to increase synaptic strength to high-Pr synapse levels. Similarly, at the Drosophila NMJ, the finding that type-Ib synapses exhibit loose calcium channel-synaptic vesicle coupling whereas type-Is synapses exhibit tight coupling suggests factors beyond calcium influx also contribute to differences in Pr between the two inputs (He et al., 2023). Consistently, a two-fold increase in external calcium does not induce a three-fold increase in release at low-Pr type-Ib synapses (He et al., 2023). Thus, upon finding that calcium channel abundance is similar at type-Ib and -Is synapses, we focused on identifying differences beyond calcium channel abundance and calcium influx that might contribute their distinct synaptic strengths. We agree that these studies, ours included, cannot definitively determine the contribution of identified organizational differences to distinct release probabilities because it is not currently possible to specifically alter subsynaptic organization, and will ensure that our language is tempered accordingly. However, in addition to the studies cited above and our findings, recent work demonstrating that homeostatic potentiation of neurotransmitter release is accompanied by greater spatial compaction of multiple active zone proteins (Dannhauser et al., 2022; Mrestani et al., 2021) and decreased calcium channel mobility (Ghelani et al., 2023) provide support for the interpretation that subsynaptic organization is a key parameter for modulating Pr.

Reviewer #2 (Public Review):

The authors aim to investigate how voltage-gated calcium channel number, organization, and subunit composition lead to changes in synaptic activity at tonic and phasic motor neuron terminals, or type Is and Ib motor neurons in Drosophila. These neuron subtypes generate widely different physiological outputs, and many investigations have sought to understand the molecular underpinnings responsible for these differences. Additionally, these authors explore not only static differences that exist during the third-instar larval stage of development but also use a pharmacological approach to induce homeostatic plasticity to explore how these neuronal subtypes dynamically change the structural composition and organization of key synaptic proteins contributing to physiological plasticity. The Drosophila neuromuscular junction (NMJ) is glutamatergic, the main excitatory neurotransmitter in the human brain, so these findings not only expand our understanding of the molecular and physiological mechanisms responsible for differences in motor neuron subtype activity but also contribute to our understanding of how the human brain and nervous system functions.

The authors employ state-of-the-art tools and techniques such as single-molecule localization microscopy 3D STORM and create several novel transgenic animals using CRISPR to expand the molecular tools available for exploration of synaptic biology that will be of wide interest to the field. Additionally, the authors use a robust set of experimental approaches from active zone level resolution functional imaging from live preparations to electrophysiology and immunohistochemical analyses to explore and test their hypotheses. All data appear to be robustly acquired and analyzed using appropriate methodology. The authors make important advancements to our understanding of how the different motor neuron subtypes, phasic and tonic-like, exhibit widely varying electrical output despite the neuromuscular junctions having similar ultrastructural composition in the proteins of interest, voltage gated calcium channel cacophony (cac) and the scaffold protein Bruchpilot (brp). The authors reveal the ratio of brp:cac appears to be a critical determinant of release probability (Pr), and in particular, the packing density of VGCCs and availability of brp. Importantly, the authors demonstrate a brp-dependent increase in VGCC density following acute philanthotoxin perfusion (glutamate receptor inhibitor). This VGCC increase appears to be largely responsible for the presynaptic homeostatic plasticity (PHP) observable at the Drosophila NMJ. Lastly, the authors created several novel CRISPRtagged transgenic lines to visualize the spatial localization of VGCC subunits in Drosophila. Two of these lines, CaBV5-C and stjV5-N, express in motor neurons and in the nervous system, localize at the NMJ, and most strikingly, strongly correlate with Pr at tonic and phasic-like terminals.

1) The few limitations in this study could be addressed with some commentary, a few minor follow-up analyses, or experiments. The authors use a postsynaptically expressed calcium indicator (mhcGal4>UAS -GCaMP) to calculate Pr, yet do not explore the contribution that glutamate receptors, or other postsynaptic contributors (e.g. components of the postsynaptic density, PSD) may contribute. A previous publication exploring tonic vs phasic-like activity at the drosophila NMJ revealed a dynamic role for GluRII (Aponte-Santiago et al, 2020). Could the speed of GluR accumulation account for differences between neuron subtypes?

We did observe that GCaMP signals are higher at type Is synapses, where synapses tend to form later but GluRs accumulate more rapidly upon innervation (Aponte-Santiago et al., 2020). However, because we are using our GCaMP indicator as a plus/minus readout of synaptic vesicle release at mature synapses, we do not expect differences in GluR accumulation to have a significant effect on our measures. Consistently, the difference in Pr we observe between type-Ib and -Is inputs (Fig. 1C) is similar to that previously reported (He et al., 2023; Lu et al., 2016; Newman et al., 2022).

2) The observation that calcium channel density and brp:cac ratio as a critical determinant of Pr is an important one. However, it is surprising that this was not observed in previous investigations of cac intensity (of which there are many). Is this purely a technical limitation of other investigations, or are other possibilities feasible? Additionally, regarding VGCC-SV coupling, the authors conclude that this packing density increases their proximity to SVs and contributes to the steeper relationship between VGCCs and Pr at phasic type Is. Is it possible that brp or other AZ components could account for these differences. The authors possess the tools to address this directly by labeling vesicles with JanellaFluor646; a stronger signal should be present at Is boutons. Additionally, many different studies have used transmission electron microscopy to explore SVs location to AZs (t-bars) at the Drosophila NMJ.

To date, the molecular underpinnings of heterogeneity in synaptic strength have primarily been investigated among individual type-Ib synapses. However, a recent study investigating differences between type-Ib and -Is synapses also found that the Cac:Brp ratio is higher at type-Is synapses (He et al., 2023).

At this point, we do not know which active zone components are responsible for the organizational (Figs. 1, 2) and coupling (now demonstrated by He et al., 2023) differences between type-Ib and -Is synapses or what establishes the differences in active zone protein levels we observe (Figs. 3,6), although Brp likely plays a local role. We find that Brp is required for dynamically regulating calcium channel levels during homeostatic plasticity and plays distinct roles at type-Ib and -Is synapses (Figs. 3, 4). Brp regulates a number of proteins critical for the distribution of docked synaptic vesicles near T bars of type Ib active zones, including Unc13 (Bohme et al., 2016). Extending these studies to type-Is synapses will be of great interest.

3) In reference to the contradictory observations that VGCC intensity does not always correlate with, or determine Pr. Previous investigations have also observed other AZ proteins or interactors (e.g. synaptotagmin mutants) critically control release, even when the correlation between cac and release remains constant while Pr dramatically precipitates.

This is an important point as a number of molecular and organizational differences between high- and low-Pr synapses certainly contribute to baseline functional differences. The other proteins we (Figs. 3,6) and others (Dannhauser et al., 2022; Ehmann et al., 2014; He et al., 2023; Jetti et al., 2023; Mrestani et al., 2021; Newman et al., 2022) have investigated are less abundant and/or more densely organized at type-Is synapses. Investigating additional active zone proteins, including synaptic proteins, and determining how these factors combine to yield increased synaptic strength are important next steps.

4) To confirm the observations that lower brp levels results in a significantly higher cac:brp ratio at phasic-like synapses by organizing VGCCs; this argument could be made stronger by analyzing their existing data. By selecting a population of AZs in Ib boutons that endogenously express normal cac and lower brp levels, the Pr from these should be higher than those from within that population, but comparable to Is Pr. I believe the authors should also be able to correlate the cac:brp ratio with Pr from their data set generally; to determine if a strong correlation exists beyond their observation for cac correlation.

We do not have simultaneous measures of Pr and Cac and Brp abundance. However, our findings suggest that distinct Cac:Brp ratios at type Ib and Is inputs reflect underlying organizational differences that contribute to distinct release probabilities between the two synaptic subtypes. In contrast, within either synaptic subtype, release probability is positively correlated with both Cac and Brp levels. Thus, the mechanisms driving functional differences between synaptic subtypes are distinct from those driving functional heterogeneity within a subtype, so we do not expect Cac:Brp ratio to correlate with Pr among individual type-Ib synapses. We will work to clarify this point in the revised text.

5) For the philanthotoxin induced changes in cac and brp localization underlying PHP, why do the authors not show cac accumulation after PhTx on live dissected preparations (i.e. in real time)? This also be an excellent opportunity to validate their brp:cac theory. Do the authors observe a dynamic change in brp:cac after 1, or 5 minutes; do Is boutons potentiate stronger due to proportional increases in cac and brp? Also regarding PhTx-induced PHP, their observations that stj and α2δ-3 are more abundant at Is synapses, suggests that they may also play a role in PhTx induced changes in cac. If either/both are overexpressed during PhTx, brp should increase while cac remains constant. These accessory proteins may determine cac incorporation at AZs.

As we have previously followed Cac accumulation in live dissected preparations and found that levels increase proportionally across individual synapses (Gratz et al., 2019), we did not attempt to repeat these challenging experiments at smaller type-Is synapses. We will reanalyze our data to investigate Cac:Brp ratio at individual active zones post PhTx. However, as noted above, we do not expect changes in the Cac:Brp ratio to correlate with Pr among individual synapses of single inputs as this measure reflects organization differences between inputs and PhTx induces an increase in the abundance of both proteins at both inputs.

Determining the effect of PhTx on Stj levels at type-Ib and -Is active zones is an excellent idea and might provide insight into how lower Stj levels correlate with higher Pr at type-Is synapses. While prior studies have demonstrated critical roles for Stj in regulating Cac accumulation during development and in promoting presynaptic homeostatic potentiation (Cunningham et al., 2022; Dickman et al., 2008; Kurshan et al., 2009; Ly et al., 2008; Wang et al., 2016), its regulation during PHP has not been investigated.

Taken together this study generates important data-driven, conceptional, and theoretical advancements in our understanding of the molecular underpinnings of different motor neurons, and our understanding of synaptic biology generally. The data are robust, thoroughly analyzed, appropriately depicted. This study not only generates novel findings but also generated novel molecular tools which will aid future investigations and investigators progress in this field.

References

Akbergenova, Y., K.L. Cunningham, Y.V. Zhang, S. Weiss, and J.T. Littleton. 2018. Characterization of developmental and molecular factors underlying release heterogeneity at Drosophila synapses. eLife. 7.

Aldahabi, M., F. Balint, N. Holderith, A. Lorincz, M. Reva, and Z. Nusser. 2022. Different priming states of synaptic vesicles underlie distinct release probabilities at hippocampal excitatory synapses. Neuron. 110:4144-4161 e4147.

Aponte-Santiago, N.A., K.G. Ormerod, Y. Akbergenova, and J.T. Littleton. 2020. Synaptic Plasticity Induced by Differential Manipulation of Tonic and Phasic Motoneurons in Drosophila. The Journal of neuroscience : the official journal of the Society for Neuroscience. 40:6270-6288.

Bohme, M.A., C. Beis, S. Reddy-Alla, E. Reynolds, M.M. Mampell, A.T. Grasskamp, J. Lutzkendorf, D.D. Bergeron, J.H. Driller, H. Babikir, F. Gottfert, I.M. Robinson, C.J. O'Kane, S.W. Hell, M.C. Wahl, U. Stelzl, B. Loll, A.M. Walter, and S.J. Sigrist. 2016. Active zone scaffolds differentially accumulate Unc13 isoforms to tune Ca(2+) channel-vesicle coupling. Nature neuroscience. 19:1311-1320.

Cunningham, K.L., C.W. Sauvola, S. Tavana, and J.T. Littleton. 2022. Regulation of presynaptic Ca(2+) channel abundance at active zones through a balance of delivery and turnover. Elife. 11.

Dannhauser, S., A. Mrestani, F. Gundelach, M. Pauli, F. Komma, P. Kollmannsberger, M. Sauer, M. Heckmann, and M.M. Paul. 2022. Endogenous tagging of Unc-13 reveals nanoscale reorganization at active zones during presynaptic homeostatic potentiation. Front Cell Neurosci. 16:1074304.

Dickman, D.K., P.T. Kurshan, and T.L. Schwarz. 2008. Mutations in a Drosophila alpha2delta voltagegated calcium channel subunit reveal a crucial synaptic function. The Journal of neuroscience : the official journal of the Society for Neuroscience. 28:31-38.

Ehmann, N., S. Van De Linde, A. Alon, D. Ljaschenko, X.Z. Keung, T. Holm, A. Rings, A. Diantonio, S. Hallermann, U. Ashery, M. Heckmann, M. Sauer, and R.J. Kittel. 2014. Quantitative super-resolution imaging of Bruchpilot distinguishes active zone states. Nature Communications. 5.

Ghelani, T., M. Escher, U. Thomas, K. Esch, J. Lützkendorf, H. Depner, M. Maglione, P. Parutto, S. Gratz, T. Matkovic-Rachid, S. Ryglewski, A.M. Walter, D. Holcman, K. O‘Connor Giles, M. Heine, and S.J. Sigrist. 2023. Interactive nanocluster compaction of the ELKS scaffold and Cacophony Ca²⁺ channels drives sustained active zone potentiation. Science Advances. 9:eade7804.

Gratz, S.J., P. Goel, J.J. Bruckner, R.X. Hernandez, K. Khateeb, G.T. Macleod, D. Dickman, and K.M. O'Connor-Giles. 2019. Endogenous tagging reveals differential regulation of Ca²⁺ channels at single AZs during presynaptic homeostatic potentiation and depression. The Journal of Neuroscience:3068-3018.

He, K., Y. Han, X. Li, R.X. Hernandez, D.V. Riboul, T. Feghhi, K.A. Justs, O. Mahneva, S. Perry, G.T. Macleod, and D. Dickman. 2023. Physiologic and Nanoscale Distinctions Define Glutamatergic Synapses in Tonic vs Phasic Neurons. The Journal of neuroscience : the official journal of the Society for Neuroscience. 43:4598-4611.

Holderith, N., A. Lorincz, G. Katona, B. Rózsa, A. Kulik, M. Watanabe, and Z. Nusser. 2012. Release probability of hippocampal glutamatergic terminals scales with the size of the active zone. Nature neuroscience. 15:988-997.

Jetti, S.K., A.B. Crane, Y. Akbergenova, N.A. Aponte-Santiago, K.L. Cunningham, C.A. Whittaker, and J.T. Littleton. 2023. Molecular Logic of Synaptic Diversity Between Drosophila Tonic and Phasic Motoneurons. bioRxiv:2023.2001.2017.524447.

Kurshan, P.T., A. Oztan, and T.L. Schwarz. 2009. Presynaptic alpha2delta-3 is required for synaptic morphogenesis independent of its Ca2+-channel functions. Nature neuroscience. 12:1415-1423.

Lu, Z., A.K. Chouhan, J.A. Borycz, Z. Lu, A.J. Rossano, K.L. Brain, Y. Zhou, I.A. Meinertzhagen, and G.T. Macleod. 2016. High-Probability Neurotransmitter Release Sites Represent an Energy-Efficient Design. Current biology : CB. 26:2562-2571.

Ly , C.V., C.-K. Yao , P. Verstreken , T. Ohyama , and H.J. Bellen 2008. straightjacket is required for the synaptic stabilization of cacophony, a voltage-gated calcium channel α1 subunit. Journal of Cell Biology. 181:157-170.

Mrestani, A., M. Pauli, P. Kollmannsberger, F. Repp, R.J. Kittel, J. Eilers, S. Doose, M. Sauer, A.-L. Sirén, M. Heckmann, and M.M. Paul. 2021. Active zone compaction correlates with presynaptic homeostatic potentiation. Cell Reports. 37:109770.

Nakamura, Y., H. Harada, N. Kamasawa, K. Matsui, Jason S. Rothman, R. Shigemoto, R.A. Silver, David A. DiGregorio, and T. Takahashi. 2015. Nanoscale Distribution of Presynaptic Ca2+ Channels and Its Impact on Vesicular Release during Development. Neuron. 85:145-158.

Newman, Z.L., D. Bakshinskaya, R. Schultz, S.J. Kenny, S. Moon, K. Aghi, C. Stanley, N. Marnani, R. Li, J. Bleier, K. Xu, and E.Y. Isacoff. 2022. Determinants of synapse diversity revealed by superresolution quantal transmission and active zone imaging. Nature Communications. 13:229.

Rebola, N., M. Reva, T. Kirizs, M. Szoboszlay, A. Lőrincz, G. Moneron, Z. Nusser, and D.A. Digregorio. 2019. Distinct Nanoscale Calcium Channel and Synaptic Vesicle Topographies Contribute to the Diversity of Synaptic Function. Neuron. 104:693-710.e699.

Sheng, J., L. He, H. Zheng, L. Xue, F. Luo, W. Shin, T. Sun, T. Kuner, D.T. Yue, and L.-G. Wu. 2012. Calcium-channel number critically influences synaptic strength and plasticity at the active zone. Nature neuroscience. 15:998-1006.

Wang, T., R.T. Jones, J.M. Whippen, and G.W. Davis. 2016. alpha2delta-3 Is Required for Rapid Transsynaptic Homeostatic Signaling. Cell Rep. 16:2875-2888.

Author Response:

We sincerely appreciate the recognition from both reviewers regarding the innovative gradual activity-blocking design employing NBQX, as well as the robustness of our approach that integrates experimental and computational approaches to investigate the interplay between homeostatic functional and structural plasticity in response to activity deprivation.

Acknowledging the raised concerns and insightful advice shared by the reviewers, we provide the the following provisional response:

Why did we focus on activity silencing? Our decision to focus on chronic activity deprivation stems from a robust body of evidence—summarised in the recent review by Moulin and colleagues (2022)—that highlights the consistent occurrence of homeostatic spine loss alongside synaptic downscaling in response to prolonged excitation. In contrast, chronic silencing studies, as outlined in the same review, exhibit inconsistencies and contradictions, with spine loss often manifesting as non-homeostatic. After carefully reviewing the available data, we formulated two hypotheses to account for this heterogeneity: (i) the non-linear nature of activity-dependent structural plasticity, and (ii) the intricate interplay between homeostatic synaptic scaling and structural plasticity influenced by factors such as the extend of activity deprivation, specific dendritic segments, cell phenotypes, brain regions, and even across species. The intricate exploration of these hypotheses necessitated a systematic approach through computational simulations (and suitable experiments). The present manuscript intentionally confines the discussion of heightened activity to a proof-of-concept computer simulation, underscoring our deliberate emphasis on the central theme of activity silencing. Nevertheless, we do concur with the reviewers that an intriguing avenue for future exploration lies in extending the model to encompass homeostatic synaptic downscaling triggered by augmented activity.

Why did we choose NBQX and why didn't we extensively characterise it? We utilised NBQX, a competitive antagonist targeting AMPA receptors, enabling us to finely modulate network activity via dosages (as elucidated by Wrathall et al., 2007), surpassing the control attainable with TTX. Despite its atypical role in studying homeostatic synaptic plasticity, NBQX boasts commendable efficacy in regulating network activity, substantiated by our electrophysiological recordings as well as in vivo and in vitro studies (Follett et al., 2000; Wrathall et al., 2007). However, it's worth noting that NBQX selectively binds to GluA2-containing AMPA receptors, pivotal for TTX-triggered synaptic scaling (Gainey et al., 2009) and glutamate-induced spine protrusion in the presence of TTX (Richards et al., 2005). Importantly, there's no conclusive evidence suggesting that NBQX, when applied in isolation (without TTX), hinders the synthesis or insertion of AMPA receptors. While we acknowledge the interest and value in characterising NBQX separately, such an endeavour extends beyond the immediate scope of our current study.

It's pertinent to also note that the models we employed—activity (calcium) dependent homeostatic synaptic scaling and structural plasticity—are inherently phenomenological in nature. In essence, these models refrain from delving into intricate molecular mechanisms beyond the regulation of calcium concentration by firing rates. Given the highly phenomenological nature of our models, introducing a detailed molecular characterization of NBQX, or expanding into a chronic increase in network activity scenarios targeting different molecular pathways, could potentially create misleading expectations among our readers, implying a level of molecular pathway implementation that is not our immediate focus.

Did the model successfully replicate the experimental findings? Achieving a strong agreement between computer simulations and empirical data is often a sought-after outcome, particularly when both aspects are integrated within a single study. However, this congruence is not always the primary intent. In our present investigation, we introduced three distinct ways in which experimental data merged with computational studies: to provide informative input, to validate hypotheses, and to stimulate novel ideas.

Our experiments primarily aimed to inform the computational model through an analysis of spine density. The computational framework was envisioned to yield insights that could be broadly applicable, extending beyond the mere replication of conducted experiments. In this context, our modelling outcomes effectively mirrored the heterogeneous alterations in synapse numbers observed in various in vivo and in vitro studies following activity deprivation—ranging from homeostatic increases to non-homeostatic synapse loss.

Our model also proposed a plausible mechanism illustrating how synaptic scaling might propel the transition from non-homeostatic synapse loss to the restoration of synapse levels, achieved by maximising inputs from active spines. This supposition found partial confirmation when considering both our experimentally obtained spine sizes and those detailed in the existing literature—pointing to a reduction in spine numbers but a conservation of larger spine sizes during complete activity blockade.

Moreover, our experimental observations unveiled certain aspects that, while not entirely encompassed by our model, have the potential to inspire future modelling studies. For instance, we observed size-dependent changes in spine sizes under complete activity blockade; we also observed inconsistent combinations of spine density and size changes across dendritic segments upon activity deprivation. The prospect of reconfiguring the interplay between structural plasticity and synaptic scaling rules to elucidate the observed heterogeneity in outcomes stands as an intriguing avenue worth revisiting, particularly as the modelling of structural plasticity within a network of intricately detailed neurons becomes feasible.

In summary, while the aspiration to faithfully replicate experimental outcomes exists, achieving an exact correspondence between a purposefully simplified system, like the point neural network we employed in our study, and real-world data should be approached with caution. Striving for such a match carries the risk of overfitting and prematurely advancing conclusions that might not stand the test of broader applications.

Why did we establish strict definitions for functional and structural plasticity? The rationale behind this strategic decision lies in the historical breadth of the term "structural plasticity," encompassing a wide array of high-dimensional alterations in neural morphology throughout development and adulthood. This expansive interpretation contributed to the delayed development of computational models specifically targeting structural plasticity. Moreover, certain elements, like spine sizes, blur the boundaries with the functional facet of synapses as also mentioned by the reviewers. We hope the reviewers and readers concur with our perspective that implementing structural plasticity through the manipulation of synapse numbers—effectively enabling dynamic (re)wiring—provides a high degree of freedom and robustness. Synaptic size seamlessly translates into synaptic weights within the modelling framework. While the distinction between synaptic weight and synapse number may seem stringent, it meticulously prepares the groundwork for addressing a fundamental question: How does the gradual modification of synapse numbers, juxtaposed with the swift modulation of synaptic weights, interact within a perpetually evolving dynamic system? In this respect our study serves as a panoramic vista, unveiling possibilities wherein distinct combinations of these two governing principles can engender divergent outcomes. This contribution not only stands as a benchmark but also extends a welcoming embrace to forthcoming structural plasticity models that embrace the concept of continuous size and number alterations.

Author Response

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

Reviewer #1 (Public Review):

The manuscript describes an interesting experiment in which an animal had to judge a duration of an interval and press one of two levers depending on the duration. The Authors recorded activity of neurons in key areas of the basal ganglia (SNr and striatum), and noticed that they can be divided into 4 types.

The data presented in the manuscript is very rich and interesting, however, I am not convinced by the interpretation of these data proposed in the paper. The Authors focus on neurons of types 1 & 2 and propose that their difference encodes the choice the animal makes. However, I would like to offer an alternative interpretation of the data. Looking at the description of task and animal movements seen in Figure 1, it seems to me that there are 4 main "actions" the animals may do in the task: press right lever, press left lever, move left, and move right. It seems to me that the 4 neurons authors observed may correspond to these actions, i.e. Figure 1 shows that Type 1 neurons decrease when right level becomes more likely to be correct, so their decrease may correspond to preparation of pressing right lever - they may be releasing this action from inhibition (analogously Type 2 neurons may be related to pressing left lever). Furthermore, comparing animal movements and timing of activity of neurons of type 3 and 4, it seems to me that type 3 neurons decrease when the animal moves left, while type 4 when the animal moves right.

I suggest Authors analyse if this interpretation is valid, and if so, revise the interpretation in the paper and the model accordingly.

We thank the reviewer for the general appreciation of the study. Regarding to the interpretation of each SNr subtypes, we have compared firing activities of the same SNr neurons in both standard 2-8 s task and reversed 2-8 s task (Figure 2G-R, Figure S4). Type 1 and Type 2 neurons are related to right and left choices respectively in the standard task (Figure 2G, M, N), and this is even more evident in the reversed 2-8 s task (Figure 2J), because when the movement trajectories of the same mice in 8-s trials were reversed from left-then-right in the control task (Figure 2I) to right-then-left in the reversed task (Figure 2L), the Type 1 SNr neurons which showed monotonic decreasing dynamics in the control 2-8 s task (Figure 2M) reversed their neuronal dynamics to a monotonic increase in the reversed 2-8 s task (Figure 2P). The same reversal of neuronal dynamics was also observed in Type 2 SNr neurons in the reversed version of standard task (Figure 2N vs Figure 2Q). Therefore, Type 1 and Type 2 neurons are related to the action selection. Furthermore, Type 3 and Type 4 SNr neurons exhibiting transient change when mice switching either from left to right, or from left to right maintained the same neuronal dynamics in both standard 2-8 s task and reversed 2-8 s task (Figure S4C-F), indicating that Type 3 and Type 4 neurons are related to the switch between choices but not the specific upcoming choice to be made.

Reviewer #1 (Recommendations For The Authors):

Suggest to clarify if SNr neurons recorded just from a single hemisphere or bilaterally.

We have described the recording hemisphere in our Methods (page 46, lines 974-976) as follows “For striatum recording, we implanted 11 mice in the left hemisphere and 8 mice in the right hemisphere. For the SNr recording, we implanted 5 mice in the left hemisphere and 4 mice in the right hemisphere.”

Suggest to analyse if type 1/2/3/4 neurons are preferrably located in hemispheres contra/ipsi lateral to a particular lever or movement.

We have addressed this issue in Figure S3 and Figure S6. In fact, we have implanted electrodes in both left and right hemispheres with mirror M-L coordinates. For striatum recording, we implanted 11 mice in the left hemisphere and 8 mice in the right hemisphere. For the SNr recording, we implanted 5 mice in the left hemisphere and 4 mice in the right hemisphere. We have analyzed the striatal and SNr neuronal activity in left vs. right hemisphere respectively, in relation to action selection. We found that SNr neurons recorded in either left or right hemisphere exhibited the same four types of neural dynamics with similar proportions (Fig. S3). Specially, the Type 1 neurons are dominant in both hemispheres. Similar in striatum, SPNs from left and right hemispheres showed the same four types of neural dynamics with similar proportions (Fig. S6). Therefore, there is no significant difference between hemispheres regarding to the proportion of neuron subtypes.

Suggest to investigate if type 1/2 neurons are involved in preparation for lever press, please investigate if these neurons are also changing their activity during the lever press.

In Figure S1L, we have showed the neuronal activities of example Type 1 and Type 2 SNr neurons to rewarded and non-rewarded lever presses. Type 1 SNr neuron shows higher firing activities when pressing the left lever than pressing the right lever, whereas Type 2 SNr neuron shows higher firing activities when pressing the right lever than pressing the left lever, indicating that Type 1 and Type 2 neurons firing activities are action choice dependent.

Suggest investigating if Type 3/4 neurons are controlling movement from one location to another, please analyse if their activity is correlated with the movement on trial by trial bases.

In Figure S2C-D, we showed firing activities of example Type 3 and Type 4 neurons on trial-by-trial bases. Type 3 neuron showed increased firing activities between 3-4 s during the 8s lever retraction period when the animal switched from left side to right side, whereas Type 4 neuron showed decreased firing activities between 3-4 s during as the animal switching from left to right. We further showed in Figure S4C-F, Type 3 and Type 4 neurons Type 3 and Type 4 neurons are related to the switch between choices but not the specific upcoming choice to be made.

Suggest also performing analogous analyses for striatal neurons.

We showed 4 types of SPNs on the on trial-by-trial bases as follows. Due to the limitation of the number of figures, these data were not included in the manuscript. We have now included these results in Fig. S2(E-H).

Typo: l. 68: "can bidirectionally regulates" -> "can bidirectionally regulate"

Thanks, we have now corrected the typos.

Reviewer #2 (Public Review):

In this valuable manuscript Li & Jin record from the substantial nigra and dorsal striatum to identify subpopulations of neurons with activity that reflects different dynamics during action selection, and then use optogenetics in transgenic mice to selectively inhibit or excite D1- and D2- expressing spiny projection neurons in the striatum, demonstrating a causal role for each in action selection in an opposing manner. They argue that their findings cannot be explained by current models and propose a new 'triple control' model instead, with one direct and two indirect pathways. These findings will be of broad interest to neuroscientists, but lacks some direct evidence for the proposal of the new model.

Overall there are many strengths to this manuscript including the fact that the empirical data in this manuscript is thorough and the experiments are well-designed. The model is well thought through, but I do have some remaining questions and issues with it.

Weaknesses:

1) The nature of 'action selection' as described in this manuscript is a bit ambiguous and implies a level of cognition or choice which I'm not sure is there. It's not integral to the understanding of the paper really, but I would have liked to know whether the actions are under goal-directed/habitual or even Pavlovian control. This is not really possible to differentiate with this task as there are a number of Pavlovian cues (e.g. lever retraction interval, house light offset) that could be used to guide behavior.

Sorry for the confusion of task description in the manuscript. We appreciate reviewer’s deep understanding about the complexity of the 2-8 s task we designed. Indeed, the 2-8 s task can’t be simply categorized as goal-directed/habitual or Pavlovian task. There are several behavioral aspects in this task. Lever retraction is served as a Pavlovian cue for mice to start performing the left-then-right sequential movement, but once levers are retracted, there is no cue available to mice during the lever retraction period, and mice have to make a decision to switch choice solely based on its internal estimation of the passage of time, which is considered as a cognitive process. The house light stays on for the entire training session (2 – 3 hours), and will be turned off when the task is done, so house light will not be used as a guidance for choice behavior. The behavior and neural activities during the lever retraction period is our main focus in this manuscript. The main advantage of such task design is that the animal is engaged in a self-determined, dynamic switch of action selection process, which offers a unique opportunity for investigating the role of various neuronal populations in the basal ganglia pathways during action selection.

2) In a similar manner, the part of the striatum that is being targeted (e.g. Figures 4E,I, and N) is dorsal, but is central with regards to the mediolateral extent. We know that the function of different striatal compartments is highly heterogeneous with regards to action selection (e.g. PMID: 16045504, 16153716, 11312310) so it would have been nice to have some data showing how specific these findings are to this particular part of dorsal striatum.

We thank the reviewer for bringing up this point. We are targeting dorsal-central part of striatum. In Figure S5G-L, we showed the specific location we targeted in striatum. Also as specified in Methods (lines 965-970), the craniotomies for electrode implantation were made at the following coordinates: 0.5 mm rostral to bregma and 1.5 mm laterally, and ~ 2.2 mm from the surface of the brain for dorsal striatum. For the virus injection and optic fiber implantation (lines 997-998), the craniotomies was made bilaterally at 0.5 mm rostral to bregma, 2 mm laterally and ~ 2.2 mm from the surface of the brain.

3) I'm not sure how I feel about the diagrams in Figure 4S. In particular, the co-activation model is shown with D2-SPNs represented as a + sign (which is described as "having a facilitatory effect to selection" in the caption), but the co-activation model still suggests that D2-SPNs are largely inhibitory - just of competing actions rather than directly inhibiting actions. Moreover, I am not sure about these diagrams because they appear to show that D2-SPNs far outnumbers D1-SPNs and we know that this isn't the case. I realize the diagrams are not proportionate, but it still looks a bit misrepresented to me.

We appreciate the reviewer’s comments about the diagram. We borrowed and extended the “center-surround” layout from the receptive field of neurons in the early visual system, as an intuitive analogy in describing the functional interaction among striatal pathways (also see Mink 2003 Archives of Neurology). In the co-activation model, if D2-SPNs inhibit the competing action, then the target action will be more likely to be selected due to the reduced competition, which means D2-SPNs actually facilitate the target action in an indirect way. And this is why we define the effect of D2-SPNs in the co-activation model as facilitatory. The area of each region does not represent the amount of cells but mainly qualitative functional role. To make it clearer, we have now added more explanation in the manuscript (page 17, lines 338-341).

4). There are a number of grammatical and syntax errors that made the manuscript difficult to understand in places.

We have now gone through the text carefully and corrected the typos.

5) I wondered if the authors had read PMID: 32001651 and 33215609 which propose a quite different interpretation of direct/indirect pathway neurons in striatum in action selection. I wonder if the authors considered how their findings might fit within this framework.

We appreciate the reviewer’s comments and suggestion. Miriam Matamales et al. (2020, PMID: 32001651) found that dynamic D2- to D1-SPNs transmodulation across the striatum that is necessary for updating previously learned behavior, which highlights the importance of collateral modulations between D1- and D2-SPNs as an additional layer of behavior control besides the classic direct and indirect pathways. This finding is compatible with our “Triple control” model emphasizing the influence of collateral modulations within striatum on behavior choice. James Peak et al. (2020, PMID: 33215609) demonstrated that D2-SPNs are critical to maintain the flexibility of behavior, which is reflected in our “Triple-control” model that activation of D2-SPNs could trigger the behavioral switch from the current action to another action. Although the two studies mentioned above mainly investigate the roles of striatal D1- and D2-SPNs in action learning and behavioral strategies, their functions in general fit within our new ‘Triple-control’ model of basal ganglia pathways for action selection.

6) There is no direct evidence of two indirect pathways, although perhaps this is beyond the scope of the current manuscript and is a prediction for future studies to test.

As accumulating RNA-seq and physiological data implying the heterogeneity of D2-SPNs, the further investigation of the subtypes of D1- and D2-SPNs and their functionality are likely a direction the field will continue to explore. On the other hand, we have discussed other possible anatomical circuits within basal ganglia circuitry that could fulfill the functional role of a third pathway in our new ‘Triple-control’ model, together with or independent of the second indirect pathway (page 32-33, lines 689-700). We certainly hope that our new model will inspire future work to identify and dissect the additional functional pathways in the basal ganglia circuits for action control.

Reviewer #2 (Recommendations For The Authors):

Suggestions for authors:

1) Consider how specific to the dorso-central striatum these findings are, possibly in the discussion.

We have specified in the Discussion that the study is targeting dorsal-central part of striatum (page 29, lines 609-612).

2) Modify the diagrams in 4S to make them more representative of the model's features.

We have responded this comment above.

3) Consider whether the findings here might fit within the role for direct pathway in excitatory action-outcome learning and the indirect pathway in response flexibility more generally.

The current study is mainly focus on selection and execution of actions. It will definitely be important to continue exploring the functionality of direct vs. indirect pathways in the action learning process.

4) Correct typos and grammatical errors including (but not limited to):

a) Line 62-64 - explain why this is controversial? Is it because we don't know which one applies?

In the “Go/No-go” model, indirect pathway inhibits the desired action and function as gain modulation, while in the “Co-activation” model, indirect pathway inhibits the competing action and in turn facilitates the desired action in an indirect manner, therefore these two existing models disagree with each other on the explanation the function of indirect pathway in its targeting action and the net outcome of behavior.

b) Line 68 - Regulates should be regulate.

This has been corrected in the revised manuscript.

c) Line 86 - should read "there are neuronal populations in either the direct or indirect pathway that are activated..."

This has been corrected in the revised manuscript.

d) Line 146-147 - "these types of neuronal dynamics in Snr only appeared in the correct but not incorrect trials" - It seems the authors are suggesting this only for Types 1 and 2 neurons, but this confused me the first time I read it and I suggest it is made clearer.

Line 146-147 now reads “These four types of neuronal dynamics in SNr only appeared…”

e) Line 346 - significant should be significantly.

This has been corrected in the revised manuscript.

f) Line 360 "contrast" should be "contrasting".

This has been corrected in the revised manuscript.

Author Response

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

We thank the reviewers for their positive remarks. We have addressed the reviewers’ recommendations in the point-by-point response below to improve our revised manuscript.

Reviewer #1 (Recommendations For The Authors):

1. The authors carry out their HDX-MS work on Prestin (and SLC26A9) solubilized in glycol-diosgenin. The authors should carefully rationalize their choice of detergent and discuss how their key findings are also pertinent to the native state of Prestin when residing in an actual phospholipid bilayer. More native membrane mimetic models are available, for instance, nano-discs etc. While I am not insisting that the authors have to repeat their measurements in a more native membrane system, it would be a very nice control experiment, and in any case, a detailed discussion of the limitations of the approach taken and possible caveats should be included - possibly with additional references to other studies.

Response: We have added a paragraph rationalizing the choice of detergent in lines 174-176. We have also added requested HDX data comparing prestin reconstituted in nanodisc to prestin solubilized in micelle (Fig 5). The HDX for prestin under these two membrane mimetics were indistinguishable, including the anion-binding site, suggesting that our major findings are likely pertinent to prestin residing in a lipid bilayer. The only major HDX difference we observed was that a lipid-facing helix TM6 is more dynamic for prestin in nanodisc compared to in micelles. In our previous structural studies, we identified TM6 as the “eletromotile elbow” that is important for prestin’s mechanical expansion (Bavi et al., Nature, 2021). We are currently conducting a more thorough investigation to understand the role of TM6 in prestin’s electromotility.

1. As far as I understand, the HEPES state represents the apo-state and thus assumes that HEPES does not bind to Prestin - the authors should support this assumption or include a discussion of the possible effect of HEPES on Prestin. Also, the HEPES state has fewer time-points - this should also be discussed.

Response: We have included a discussion of the possible effects of HEPES in lines 331-345. In fact, in an attempt to support our assumption that HEPES does not bind to prestin, we set out to determine the structure of prestin in the HEPES-based buffer using single particle cryo-EM. However, we did not find evidence that HEPES binds to prestin. Details are discussed in lines 331-345 and Supporting Information Text 3.

We employed a denser sampling of HDX labeling times for prestin in Cl- because it is critical for fitting and ∆G calculation. The earlier time points are used mainly to evaluate the dynamics of the less stable cytosolic domain. Since the cytosolic domain does not directly participate in prestin’s voltage-sensing mechanism and electromotility, we only measured the HEPES states with longer time points which mainly probe the dynamics of the transmembrane domain.

1. Overall, the HDX-MS data provided and the statistical analysis done is in my view sufficiently detailed and well done - the authors are advised to make reference to and include a HDX Summary table and HDX Data Table according to the HDX-MS community-guidelines (Masson et al. Nature Methods 2019).

Response: An HDX summary table was provided in Table S1 and referred in lines 81 and 388. We have included a reference to Masson et al., Nature Methods, 2019, in line 389.

1. Figure 5 - I like the detailed analysis of the helix folding - but in my experience, one can provide a great fit of many HDX curves to a 4 -term exponential function - I think the authors would need more time-points to provide a more convincing case. But it does provide a compelling theory - even if the data strictly does not prove it. The authors should discuss this in more detail - including limitations etc.

Response: We presented a statistical analysis describing the accuracy of the fitting in Fig 6A. We acknowledge that the values of the exponentials may not be precisely determined, but the fundamental result is robust – TM3 exchanges through fraying from the N-terminal end of the helix while TM6 exchanges much more cooperatively. Collecting additional time points may reduce the error on the rates but would not contribute to additional mechanistic insights.

Reviewer #2 (Recommendations For The Authors):

1. I suggest toning down more speculative/ hypothetical aspects. Specifically, I believe that the following sentence should not be in the abstract in its present form: "This event shortens the TM3-TM10 electrostatic gap, thereby connecting the two helices such that TM3-anion-TM10 is pushed upwards by forces from the electric field, resulting in reduced cross-sectional area."

Response: The sentence has been rephrased.

1. The "nuance" between helix fraying and helix unfolding is an important aspect of the author's hypothesis but this should be explained better. In that regard, have the authors performed HDX-MS analysis of the mutant P136T? That would nicely support their claim regarding the importance of helix fraying as being foundational to allow electromotility.

Response: More explanation for helix fraying and unfolding has been provided in the main text. We have not performed HDX-MS analysis of the mutant P136T. However, we performed molecular dynamics simulations using Upside, and consistently, showed that a P136T mutation in prestin results in a highly stabilized TM3 (Fig. S4B).

1. Why do measurements at two pDs? Did the authors observe any differences?

Response: The purpose of two pDs is to increase the effective dynamic range of the HDX measurement by two orders of magnitude because the intrinsic exchange rate scales with pD & Temp. This allows us to determine the stability of both the highly and minimally stable regions within the protein. We have rephrased lines 83-87 to better rationalize this choice of pDs. With the time points performed in this study, we did not observe noticeable differences for HDX performed under the two pDs when corrected for the changes in the intrinsic rates (Fig. S7A).

1. I can't help but wonder what is the interest in doing HDX-MS measurements after 27h of incubation. Membrane proteins are known for their instability once purified and a few odd HDX profiles at that specific timepoint (especially in the 80-100 residues area) make one question whether local unfolding preceding aggregation could happen. This actually weakens the author's claims about cooperative unfolding and localized and directional helix fraying. Could they provide some evidence (CD, thermostability measurements such as trp fluorescence quenching, or SEC analysis) that the prestin is still folded after 27h in GDN.

Response: We appreciate reviewer’s comments on membrane proteins can be unstable once purified. In our system, we did not observe evidence of unfolding or aggregation caused by long-term incubation after purification. This is mostly supported by the fact that our HDX reactions were initiated and injected to MS in random order, yet are still highly reproducible among biological and technical replicates. A specific example included HDX on freshly purified SLC26A9 gave the same deuteration levels as SLC26A9 purified in GDN after 4 days. For prestin, although we don’t have direct comparison between fresh samples and old samples (24-27h post-purification) due to the lack of samples, 30s HDX in SO42- performed 24h post-purification gave a %D that fell between 10s and 90s of labeling done on fresh sample. Additionally, HDX on prestin in Cl- performed on freshly purified sample gave the sample %D as prestin in the presence of 1M urea labeled after 24~48h of purification, suggesting that prestin is relatively resistant to aggregation at least within 48h after purification even in the presence of 1 M urea (data not shown).

Furthermore, the HDX for prestin in nanodisc are essentially identical to prestin in micelles except for a functionally important helix (TM6), suggesting minimal aggregation or misfolding.

We think the “a few odd HDX profiles” at 27h time points for residues 80-100 are caused by two reasons. Firstly, TM1 unfolds cooperatively and its stability in HEPES falls within the detection range when long labeling time points were employed (within one log unit of 27h). Secondly, we observed two non-interconverting and structurally distinct populations for TM1 (Supporting Information Text 1 & Fig. S8), and in long labeling times, the two isotope distributions merge and sometimes can skew the %D calculations. Nevertheless, the HDX differences we observed comparing across conditions are clear and such %D calculation skewing, if present, should be minimal and does not change our main conclusions.

Author Response

Reviewer #1 (Public Review):

Summary:

This work describes the mechanism of protein disaggregation by the ClpL AAA+ protein of Listeria monocytogenes. Using several model substrate proteins the authors first show that ClpL possesses a robust disaggregase activity that does not further require the endogenous DnaK chaperone in vitro. In addition, they found that ClpL is more thermostable than the endogenous L. monocytogenes DnaK and has the capacity to unfold tightly folded protein domains. The mechanistic basis for the robust disaggregase activity of ClpL was also dissected in vitro and in some cases, supported by in vivo data performed in chaperone-deficient E. coli strains. The data presented show that the two AAA domains, the pore-2 site and the N-terminal domain (NTD) of ClpL are critical for its disaggregase activity. Remarkably, grafting the NTD of ClpL to ClpB converted ClpB into an autonomous disaggregase, highlighting the importance of such a domain in the DnaK-independent disaggregation of proteins. The role of the ClpL NTD domain was further dissected, identifying key residues and positions necessary for aggregate recognition and disaggregation. Finally, using sets of SEC and negative staining EM experiments combined with conditional covalent linkages and disaggregation assays the authors found that ClpL shows significant structural plasticity, forming dynamic hexameric and heptameric active single rings that can further form higher assembly states via their middle domains.

Strengths:

The manuscript is well-written and the experimental work is well executed. It contains a robust and complete set of in vitro data that push further our knowledge of such important disaggregases. It shows the importance of the atypical ClpL N-terminal domain in the disaggregation process as well as the structural malleability of such AAA+ proteins. More generally, this work expands our knowledge of heat resistance in bacterial pathogens.

Weaknesses:

There is no specific weakness in this work, although it would have helped to have a drawing model showing how ClpL performs protein disaggregation based on their new findings. The function of the higher assembly states of ClpL remains unresolved and will need further extensive research. Similarly, it will be interesting in the future to see whether the sole function of the plasmid-encoded ClpL is to cope with general protein aggregates under heat stress.

We thank the reviewer for the positive evaluation. We agree with the reviewer that it will be important to test whether ClpL can bind to and process non-aggregated protein substrates. Our preliminary analysis suggests that the disaggregation activity of ClpL is most relevant in vivo, pointing to protein aggregates as main target.

We also agree that the role of dimers or tetramers of ClpL rings needs to be further explored. Our initial analysis suggests a function of ring dimers as a resting state. It will now be important to study the dynamics of ClpL assembly formation and test whether substrate presence shifts ClpL assemblies towards an active, single ring state.

Reviewer #2 (Public Review):

The manuscript by Bohl et al. is an interesting and carefully done study on the biochemical properties and mode of action of potent autonomous AAA+ disaggregase ClpL from Listeria monocytogenes. ClpL is encoded on plasmids. It shows high thermal stability and provides Listeria monocytogenes food-pathogen substantial increase in resistance to heat. The authors show that ClpL interacts with aggregated proteins through the aromatic residues present in its N-terminal domain and subsequently unfolds proteins from aggregates translocating polypeptide chains through the central pore in its oligomeric ring structure. The structure of ClpL oligomers was also investigated in the manuscript. The results suggest that mono-ring structure and not dimer or trimer of rings, observed in addition to mono-ring structures under EM, is an active species of disaggregase.

Presented experiments are conclusive and well-controlled. Several mutants were created to analyze the importance of a particular ClpL domain.

The study's strength lies in the direct comparison of ClpL biochemical properties with autonomous ClpG disaggregase present in selected Gram-negative bacteria and well-studied E. coli system consisting of ClpB disaggregase and DnaK and its cochaperones. This puts the obtained results in a broader context.

We thank the reviewer for the detailed comments. There are no specific weaknesses indicated in the public review.

Reviewer #3 (Public Review):

Summary:

This manuscript details the characterization of ClpL from L. monocytogenes as a potent and autonomous AAA+ disaggregase. The authors demonstrate that ClpL has potent and DnaK-independent disaggregase activity towards a variety of aggregated model substrates and that this disaggregase activity appears to be greater than that observed with the canonical DnaK/ClpB co-chaperone. Furthermore, Lm ClpL appears to have greater thermostability as compared to Lm DnaK, suggesting that ClpL-expressing cells may be able to withstand more severe heat stress conditions. Interestingly, Lm ClpP can provide thermotolerance to E. coli that have been genetically depleted of either ClpB or in cells expressing a mutant DnaK103. The authors further characterized the mechanisms by which ClpL interacts with protein aggregates, identifying that the N-terminal domain of ClpL is essential for disaggregase function. Lastly, by EM and mutagenesis analysis, the authors report that ClpL can exist in a variety of larger macromolecular complexes, including dimer or trimers of hexamers/heptamers, and they provide evidence that the N-terminal domains of ClpL prevent dimer ring formation, thus promoting an active and substrate-binding ClpL complex. Throughout this manuscript the authors compare Lm ClpL to ClpG, another potent and autonomous disaggregase found in gram-negative bacteria that have been reported on previously, demonstrating that these two enzymes share homologous activity and qualities. Taken together this report clearly establishes ClpL as a novel and autonomous disaggregase.

Strengths:

The work presented in this report amounts to a significant body of novel and significant work that will be of interest to the protein chaperone community. Furthermore, by providing examples of how ClpL can provide in vivo thermotolerance to both E. coli and L. gasseri the authors have expanded the significance of this work and provided novel insight into potential mechanisms responsible for thermotolerance in food-borne pathogens.

Weaknesses:

The figures are clearly depicted and easy to understand, though some of the axis labeling is a bit misleading or confusing and may warrant revision. While I do feel that the results and discussion as presented support the authors' hypothesis and overall goal of demonstrating ClpL as a novel disaggregase, interpretation of the data is hindered as no statistical tests are provided throughout the manuscript. Because of this only qualitative analysis can be made, and as such many of the concluding statements involving pairwise comparisons need to be revisited or quantitative data with stats needs to be provided. The addition of statistical analysis is critical and should not be difficult, nor do I anticipate that it will change the conclusions of this report.

We thank the reviewer for the valid criticism. We addressed the major concern of the reviewer and added the requested statistical analysis to all relevant figures. The analysis confirms our conclusions. We also followed the advice of the reviewer and revised axis labeling to increase clarity.

Author Response

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

Public Reviews:

Reviewer #1 (Public Review):

Anderson, Henikoff, Ahmad et al. performed a series of genomics assays to study Drosophila spermatogenesis. Their main approaches include (1) Using two different genetic mutants that arrest male germ cell differentiation at distinct stages, bam and aly mutant, they performed CUT&TAG using H3K4me2, a histone modification for active promoters and enhancers; (2) Using FACS sorted pure spermatocytes, they performed CUT&TAG using antibodies against RNA PolII phosphorylated Ser 2, H4K16ac, H3K9me2, H3K27me3, and ubH2AK118. They also compare these chromatin profiling results with the published single-cell and single-nucleus RNA-seq data. Their analyses are across the genome but the major conclusions are about the chromatin features of the sex chromosomes. For example, the X chromosome is lack of dosage compensation as well as inactivation in spermatocytes, while Y chromosome is activated but enriched with ubH2A in spermatocytes. Overall, this work provides high-quality epigenome data in testes and in purified germ cells. The analyses are very informative to understand and appreciate the dramatic chromatin structure change during spermatogenesis in Drosophila. Some new analyses and a few new experiments are suggested here, which hopefully further take advantage of these data sets and make some results more conclusive.

Major comments: 1. The step-wise accumulation of H3K4me2 in bam, aly and wt testes are interesting. Is it possible to analyse the cis-acting sequences of different groups of genes with distinct H3K4me2 features, in order to examine whether there is any shared motif(s), suggesting common trans-factors that potentially set up the chromatin state for activating gene expression in a sequential manner?

While the histone H3K4me2 mark is low and more widespread at genes active in late spermatocytes and in spermatids (shown in Figure 2C and some examples in Figure 1C-D), we suggest that this may be due to a general decrease in the importance of this modification in late spermatogenesis rather than a specific feature of those genes. We point this out in lines 146-152. This idea is supported by the widespread change in RNAPII distribution in all genes in the germline, shown in Figure 3F and supplementary Figure 2.

1. Pg. 4, line 141-142: "we cannot measure H3K4me2 modification at the bam promoter in bam mutant testes or at the aly promoter in aly mutant testes", what are the allelic features of the bam mutant and aly mutant? Are the molecular features of these mutations preventing the detection of H3K4me2 at the endogenous genes' promoters? Also, the references cited (Chen et al., 2011) and (Laktionov et al., 2018) are not the original research papers where these two mutants were characterized.

We have corrected these citations to the original papers. We clarified in the text that the bamΔ86 allele is a deletion of almost all of the coding sequence (reported in Bopp, D., Horabin, J.I., Lersch, R.A., Cline, T.W., Schedl, P. (1993). Expression of the Sex-lethal gene is controlled at multiple levels during Drosophila oogenesis. Development 118(3): 797--812.). The aly1 allele is also a P element-induced mutation; it is not molecularly characterized (it was first described here: Lin, T.Y., Viswanathan, S., Wood, C., Wilson, P.G., Wolf, N., Fuller, M.T. (1996). Coordinate developmental control of the meiotic cell cycle and spermatid differentiation in Drosophila males. Development 122(4): 1331--1341.) We noticed a lack of reads for various histone modifications in aly mutants in part of the gene, suggesting that the deletion is limited to the promoter and the first exon. Signal for the H3K4me2 modification is at background levels for the distal portion of aly, suggesting that the deletion inactivates the gene.

1. The original paper that reported the Pc-GFP line and its localization is: Chromosoma 108, 83 (1999).

We are citing the first published description of this marker in the male germline (lines 291-293).

The Pc-GFP is ubiquitously expressed and almost present in all cell types. In Figure 6B, there is no Pc-GFP signals in bam and aly mutant cells.

We apologize, our labeling of the figure was easily overlooked - the bam and aly genotypes do not carry the PcGFP marker, since we didn’t need it for staging the germline nuclei. We have clarified this in the figure.

According to the Method "one testis was dissected", does it mean that only one testis was prepared for immunostaining and imaging? If so, definitely more samples should be used for a more confident conclusion.

We corrected the text to make it clear that all cytological examinations were repeated at least times (lines 438-439).

Also, why use 3rd instar larval testes instead of adult testes?

Generally, we find that immunostaining of the larval testes is cleaner, and we now mention this in the Methods (lines 439-440). We have immunostained both larval and adult testes for these markers with consistent results.

Finally, it is better to compare fixed tissue and live tissue, as the Pc-GFP signal could be lost during fixation and washing steps. Please refer to the above paper [Chromosoma 108, 83 (1999)] for Pc-GFP in spermatogonial cells and Development 138, 2441-2450 (2011) for Pc-GFP localization in aly mutant.

We are using PcGFP staining for staging with antibody detection of other chromatin features, which requires fixed material, although we have compared PcGFP signal in both live and fixed tissue. We have added the 1999 reference for nuclear staging in the male germline.

1. Ubiquitinylation of histone H2A is typically associated with gene silencing, here it has been hypothesized that ubH2A contributes to the activation of Y chromosome. This conclusion is strenuous, as it entirely depends on correlative results.

We agree that this is a correlation. We cite in the text examples where uH2A is associated with gene activation. We have added a comment to clarify that this is a correlation (lines 318-320), and now present an alternative that uH2A on the Y chromosome may be moderating expression from these highly active genes (lines 405-407).

For example, the lack of co-localization of ubH2A immunostaining and Pc-GFP are not convincing evidence that ubH2A is not resulting from PRC1 dRing activity. It would be a lot stronger conclusion by using genetic tools to show this. For example, if dRing is knocked down (using RNAi driven by a late-stage germline driver such as bam-Gal4) or mutated in spermatocytes (using mitotic clonal analysis), would they detect changes of ubH2A levels?

We have tested multiple constructs to knockdown dRING using the bam-GAL4 driver although we have not reported it in the manuscript. These knockdowns have no effect on uH2A staining in the testis, on motile sperm production, or on male fertility, although these RNAi constructs do produce Polycomb phenotypes when expressed in somatic cells from an en-GAL4 driver. This is the reason why we point out in the text that there are multiple alternative candidates for an H2A ubiquitin ligase in the Drosophila genome and that in other species RING1 is not responsible for sex body uH2A in the male germline (lines 394-396).

1. Regarding "X chromosome of males is thought to be upregulated in early germline cells", it has been shown that male-biased genes are deprived on the X chromosome [Science 299:697-700 (2003); Genome Biol 5:R40 (2004); Nature 450:238-241 (2007)], so are the differentiation genes of spermatogenesis [Cell Research 20:763-783 (2010)]. It would be informative to discuss the X chromatin features identified in this work with these previous findings.

We now mention that the Drosophila X chromosome is moderately depleted of male germline-expressed genes (lines 362-363).

For example, the lack of RNAPII on X chromosome in spermatocytes could be due to a few differentiation genes expressed in spermatocytes located on the X chromosome.

We show in Figure 3B that there is a minor non-significant reduction in RNAPII on the X chromosome in spermatocytes. This small reduction might be due to the moderate paucity of male germline-expressed genes on this chromosome, but since it is non-significant we have not discussed it.

Reviewer #2 (Public Review):

Anderson et al profiled chromatin features, including active chromatin marks, RNA polymerase II distribution, and histone modifications in the sex chromosomes of spermatogenic cells in Drosophila. The results are new and the experiments and analyses look well done, including with appropriate numbers of replicates. Results were parsed by comparing them among two arrest mutants and wildtype, as well as in FACS-sorted spermatocytes. The authors also profiled larval wing discs to serve as reference-somatic cells, which allowed them to focus only on features in their testis data that were associated with germ cells. Their results were further refined by categorizing the genes of interest based on available single nucleus RNA seq expression profiles. The authors document interesting phenomena, such as differences in the distribution of RNAPIIS2p on some genes in germ cells vs somatic cells, the presence of a uH2A body beginning in early spermatocytes, and high levels of uH2A on the Y chromosome and little or none on the X. The former is intriguing because this modification is usually associated with silencing, yet the Y chromosome is active in spermatogenic cells. The authors interpret some of their data as implying a lack of dosage compensation of the X chromosome in spermatocytes.

The data are believable and new, but it is not fully clear how to interpret them. The paper's interpretations rely on subtractive logic to parse results from mixtures of cells down to cell type, extracting spermatogonia, spermatocyte, etc. features by comparing bam mutants (only spermatogonia) to aly mutants (spermatogonia and early spermatocytes but no later stages) to wildtype (all spermatogenic stages), and extracting testis germline data by comparison to wing disc soma; their FACS sorted spermatocytes also have heterogeneity. I recognize that the present paper was a lot of work and am not suggesting that the authors redo their study using methods that give more purity and precision of stage (https://doi.org/10.1126/science.aal3096, https://doi.org/10.1101/gad.335331.119), but they should be aware of them and of their results.

The pulse-release system that the reviewer points to is an interesting system, but more limited in material and in useable markers than the systems we used here. We have added to our discussion of the the limitations of subtractive comparisons between arrest genotypes, both in regards to using mutants that may alter gene expression programs, and to how subtractive comparisons may limit our detection of differences between cell types (lines 143-147).

The conclusions about dosage compensation are indirect, but are consistent with the current model documented in the studies cited by the authors, as well as earlier studies (doi: 10.1186/jbiol30).

We disagree; our data directly speaks to the molecular mechanisms at play. Our profiling of the H4K16acetylation mark and RNAPII in isolated spermatocytes (Figure 4) demonstrates that current models are correct, and so are useful for settling this point in the literature.

Reviewer #1 (Recommendations For The Authors):

Throughout the manuscript, it is better to cite the original research papers.

We have added citations for the original characterizations of bam and aly alleles used, for the descriptions of PCGFP in spermatocytes, and for issues raised by reviewer comments.

Minor comments:

Pg.2, line 70-71: "Germline stem cells at the apical tip of the testis asymmetrically divide to birth spermatogonia", should be gonialblast.

Fixed (line 71).

Pg.2, line 71: "four rapid mitotic divisions", the spermatogonial cell cycle lasts several hours-- "rapid" is subjective and relative, better to leave this word out.

Fixed (line 71).

Reviewer #2 (Recommendations For The Authors):

Other than the major issue raised in the public review this paper only needs a few minor modifications, listed by line number below. The first one would be considered essential by this reviewer.

27: In the sentence that ends on this line, please add the word testis after Drosophila.

Fixed (line 27).

119: It must be known from the Fly Cell Atlas data whether these genes do begin to express in spermatogonia.

Collated expression values from the FCA are provided in Supplementary Table 2. In many cases there is detectable expression of these genes in spermatogonia, although transcript abundance peaks in early spermatocytes.

198: remove "distribution of".

Fixed (line 200).

311: enrichment relative to what?

Fixed (line 313). It is relative to signal in wing discs.

344: other aspects could be regulated such as elongation, termination.

We have added caveats to our speculations in this sentence (lines 340-356). The increased signal we see in gene bodies could be due to slower RNAPII elongation, but we don’t see a way that changes in termination would produce this pattern.

369: This part of the paper seems overly speculative, given the many molecular differences between dosage compensation mechanisms of Drosophila vs mammals, and studies that indicate that MSCI does occur in Drosophila (DOI: 10.3390/genes12111796).

We disagree, and this is a central point in our manuscript. The paper referred to here does not directly assess MSCI in Drosophila, instead they argue that MSCI could be the force driving the evolutionary depletion of male-germline-expressed genes they describe. These and many studies in the literature have conflated the effects of a lack of X dosage compensation and of MSCI in the male germline. Our direct measurements of RNAPII in spermatocytes demonstrates that there is no dosage compensation nor is there MSCI. Further, profiling of histone modifications associated with Drosophila somatic dosage compensation (H4K16ac) or with mammalian MSCI (uH2A, H3K9me2) show that the molecular mechanisms found in these other settings are not in play in the Drosophila male germline. As we have established these biological differences between mammals and Drosophila, it is appropriate to now speculate on why these differences may be, which we do on lines 374-384.

(several lines): Can the authors justify their assumption that chromatin features of larval wing disc cells will match those of somatic cells of adult testes?

We don’t only compare germline features to somatic cells of the wing disc, but also to genes with somatic expression in the testes annotated by FCA expression data (H3K4me2 in Figure 2C, RNAPII in Figure 3F). Note in Supplementary Figure 2 the distribution of RNAPII in whole testes (which includes somatic cells) is similar to that of larval wing discs, confirming that the differences we describe are specific to germline cells.

Author Response

The following is the authors’ response to the previous reviews

Point-to-Point Responses to Reviewers’ Comments

We are a bit surprised by the comments of Reviewer 1, but that our further responses can help communications with Reviewer 1. We have also responded to comments of Reviewers 2 and 3.

Public Reviews:

*Reviewer #1 (Public Review):

The overall tone of the rebuttal and lack of responses on several questions was surprising. Clearly, the authors took umbrage at the phrase 'no smoking gun' and provided a lengthy repetition of the fair argument about 'ticking boxes' on the classic list of criteria. They also make repeated historical references that descriptions of neurotransmitters include many papers, typically over decades, e.g. in the case of ACh and its discovery by Sir Henry Dale. While I empathize with the authors' apparent frustration (I quote: '...accept the reality that Rome was not built in a single day and that no transmitter was proven by a one single paper') I am a bit surprised at the complete brushing away of the argument, and in fact the discussion. In the original paper, the notion of a receptor was mentioned only in a single sentence and all three reviewers brought up this rather obvious question. The historical comparisons are difficult: Of course many papers contribute to the identification of a neurotransmitter, but there is a much higher burden of proof in 2023 compared to the work by Otto Loewi and Sir Henry Dale: most, if not all, currently accepted neurotransmitter have a clear biological function at the level of the brain and animal behavior or function - and were in fact first proposed to exist based on a functional biological experiment (e.g. Loewi's heart rate change). This, and the isolation of the chemical that does the job, were clear, unquestionable 'smoking guns' a hundred years ago. Fast forward 2023: Creatine has been carefully studied by the authors to tick many of the boxes for neurotransmitters, but there is no clear role for its function in an animal. The authors show convincing effects upon K+ stimulation and electrophysiological recordings that show altered neuronal activity using the slc6a8 and agat mutants as well as Cr application - but, as has been pointed out by other reviewers, these effects are not a clear-cut demonstration of a chemical transmitter function, however many boxes are ticked. The identification of a role of a neurotransmitter for brain function and animal behavior has reasonably more advanced possibilities in 2023 than a hundred years ago - and e.g. a discussion of approaches for possible receptor candidates should be possible.

Again, I reviewed this positively and agree that a lot of cumulative data are great to be put out there and allow the discovery to be more broadly discussed and tested. But I have to note, that the authors simply respond with the 'Rome was not built in a single day' statement to my suggestions on at least 'have some lead' how to approach the question of a receptor e.g. through agonists or antagonists (while clearly stating 'I do not think the publication of this manuscript should not be made dependent' on this). Similarly, in response to reviewer 2's concerns about a missing receptor, the authors' only (may I say snarky) response is ' We have deleted this sentence, though what could mediate postsynaptic responses other than receptors?' The bullet point by reviewer 3 ' • No candidate receptor for creatine has been identified postsynaptically.' is the one point by that reviewer that is simply ignored by the authors completely. Finally, I note that my reivew question on the K stimulation issues (e.g. 35 neurons that simply did not respond at all) was: ' Response: To avoid the disadvantage of K stimulation, we also performed optogenetic experiments recently and obtained encouraging preliminary results.' No details, not data - no response really.

In sum, I find this all a bit strange and the rebuttal surprising - all three reviewers were supportive and have carefully listed points of discussion that I found all valid and thoughtful. In response, the authors selectively responded scientifically to some experimental questions, but otherwise simply rather non-scientifically dismissed questions with 'Rome was not built in a day'-type answers, or less. I my view, the authors have disregarded the review process and the effort of three supportive reviewers, which should be part of the permanent record of this paper.

Response:

We were very surprised by the tone of Reviewer 1 in the second round of reviewing. The corresponding author has spent some time including a long holiday to cool down and re-read our earlier responses. The following is entirely by the correspond author.

I have finally checked the term “smoking gun”, and found out that I interpreted it wrongly while I had thought that Reviewer 1 was wrong. This came from a long story in that I was lectured by a native speaker for my English when submitting the first paper from my own paper. In that case, the Reviewer was wrong (in arguing that only adjectives but not nouns can be used to define nouns), I was quite offended and remembered it vividly. In the case of “smoking gun”, I wrongly believed that it meant a hint (while the definite evidence would be “the final nail in the coffin”). By interpreting is as a hint, I was then rebutting Reviewer 1 for negating all our experimental results as “not a single piece of suggestive evidence”.

For the above, I apologize.

I have another disagreement about “smoking gun”. For a transmitter, multiple criteria have to be met. For example, finding a receptor for a small molecule would not be definitive for a transmitter because if it is not present in the SVs, it is unlikely to be a typical transmitter. If a molecule has a receptor but they are not even in the nervous system, it is definitely no a transmitter.

The title of our paper is “Evidence suggesting creatine as a new central neurotransmitter”, not “Evidence proving creatine as a new central neurotransmitter”. In the Abstract, after “Our biochemical, chemical, genetic and electrophysiological results are consistent with the possibility of Cr as a neurotransmitter”, we are adding “though not yet reaching the level of proof for the now classic transmitters”. In the last sentence of the introduction, we have now added “though the discovery of a receptor for Cr would prove it”.

I do, however, believe that, however strong the wordings are, criticisms and rebuttals in science are normal and should be conducted even when emotions are involved.

One of my major point of differences with at least two of the reviewers is that the criteria for neurotransmitters should be those listed in major textbooks. While everyone can have one’s own opinions, the textbooks, especially those accepted by readers of the field for more than 40 years, should be the standards. Kandel has listed the 4 criteria not only 40 years ago but also just 2 years ago in their latest 6th edition. The reviewers have asked for more, while discounting Kandel et al. (2021). So, in essence, the Reviewer is not shy in scientific criticisms when stating “The identification of a role of a neurotransmitter for brain function and animal behavior has reasonably more advanced possibilities in 2023 than a hundred years ago”.

Reviewer 1 raised another new criterion: brain function and behavior, while this is not in any textbook lists. However, lack of Cr caused behavioral problems, as cited by us in the introduction: both humans and mice were defective in brain function with loss of function mutations in the gene for the specific Cr transporter SLC6A8. If the reviewer meant behavioral abnormalities caused by Cr injection, that was unclear. But that criterion may not be met by other transmitters which is the likely reason that it was not a criterion in any textbook.

Reviewer #2 (Public Review):

Summary:

Bian et al studied creatine (Cr) in the context of central nervous system (CNS) function. They detected Cr in synaptic vesicles purified from mouse brains with anti-Synaptophysin using capillary electrophoresis-mass spectrometry. Cr levels in the synaptic vesicle fraction was reduced in mice lacking the Cr synthetase AGAT, or the Cr transporter SLC6A8. They provide evidence for Cr release within several minutes after treating brain slices with KCl. This KCl-induced Cr release was partially calcium dependent and was attenuated in slices obtained from AGAT and SLC6A8 mutant mice. Cr application also decreased the excitability of cortical pyramidal cells in one third of the cells tested. Finally, they provide evidence for SLC6A8-dependent Cr uptake into synaptosomes, and ATP-dependent Cr loading into synaptic vesicles. Based on these data, the authors propose that Cr may act as neurotransmitter in the CNS.

Strengths: 1. A major strength of the paper is the broad spectrum of tools used to investigate Cr. 2. The study provides evidence that Cr is present in/loaded into synaptic vesicles.

Weaknesses: 1. There is no significant decrease in Cr content pulled down by anti-Syp in AGAT-/- mice when normalized to IgG controls. Hence, blocking AGAT activity/Cr synthesis does not affect Cr levels in the synaptic vesicle fraction, arguing against a Cr enrichment.

Response: Evidence for Cr enrichment in the SVS was obtained robustly with wild type mice. When brain Cr is very low in AGAT-/- mutant mice, because there is little Cr, there is also little Cr in the SVs. One does not require that as a criterion: it does not argue against the normal levels of Cr could be transported into the SVs even if when the much reduced levels of AGAT-/- Cr in mutant mice could be enriched in SVs.

1. There is no difference in KCl-induced Cr release between SLC6A8-/Y and SLC6A8+/Y when normalizing the data to the respective controls. Thus, the data are not consistent with the idea that depolarization-induced Cr release requires SLC6A8.

Response: This comment of Reviewer 2 was based on Figure 5D. But if one carefully examines Figure 5G, it was clear that the Ca++ dependent component of KCl -induced Cr release was lower in SLC6A8-/Y than that in SLC6A8+/Y.

1. The rationale of grouping the excitability data into responders and non-responders is not convincing because the threshold of 10% decrease in AP rate is arbitrary. The data do therefore not support the conclusion that Cr reduces neuronal excitability.

Response: Comparison of the same neuron, before and after Cr did show effects on neuronal excitability though that would have no statistics if one does not group multiple cells into the same categories.

Reviewer #3 (Public Review):

SUMMARY:

The manuscript by Bian et al. promotes the idea that creatine is a new neurotransmitter. The authors conduct an impressive combination of mass spectrometry (Fig. 1), genetics (Figs. 2, 3, 6), biochemistry (Figs. 2, 3, 8), immunostaining (Fig. 4), electrophysiology (Figs. 5, 6, 7), and EM (Fig. 8) in order to offer support for the hypothesis that creatine is a CNS neurotransmitter.

STRENGTHS:

There are many strengths to this study. • The combinatorial approach is a strength. There is no shortage of data in this study. • The careful consideration of specific criteria that creatine would need to meet in order to be considered a neurotransmitter is a strength. • The comparison studies that the authors have done in parallel with classical neurotransmitters is helpful. • Demonstration that creatine has inhibitory effects is another strength. • The new genetic mutations for Slc6a8 and AGAT are strengths and potentially incredibly helpful for downstream work.

WEAKNESSES: • Some data are indirect. Even though Slc6a8 and AGAT are helpful sentinels for the presence of creatine, they are not creatine themselves. Of note, these molecules themselves are not essential for making the case that creatine is a neurotransmitter.

Response: We agree, but those data are not inconsistent with the possibility.

• Regarding Slc6a8, it seems to work only as a reuptake transporter - not as a transporter into SVs. Therefore, we do not know what the transporter into the TVs is.

Response: SLC6A8 is not the transporter on the SVs, but is an excellent candidate for the transporter on the presynaptic cytoplasmic membrane for uptake of Cr into the presynaptic structure.

• Puzzlingly, Slc6a8 and AGAT are in different cells, setting up the complicated model that creatine is created in one cell type and then processed as a neurotransmitter in another. This matter will likely need to be resolved in future studies.

Response: We agree.

• No candidate receptor for creatine has been identified postsynaptically. This will likely need to be resolved in future studies.

Response: We agree.

• Because no candidate receptor has been identified, it is important to fully consider other possibilities for roles of creatine that would explain these observations other than it being a neurotransmitter? There is some attention to this in the Discussion.

Response: We agree.

There are several criteria that define a neurotransmitter. The authors nicely delineated many criteria in their discussion, but it is worth it for readers to do the same with their own understanding of the data.

By this reviewer's understanding (and combining some textbook definitions together) a neurotransmitter: 1) must be present within the presynaptic neuron and stored in vesicles; 2) must be released by depolarization of the presynaptic terminal; 3) must require Ca2+ influx upon depolarization prior to release; 4) must bind specific receptors present on the postsynaptic cell; 5) exogenous transmitter can mimic presynaptic release; 6) there exists a mechanism of removal of the neurotransmitter from the synaptic cleft.

Response: While any of us can come up with a list according to our own understanding, the paper copies lists from textbooks, especially from Kandel et al. (2021), which lists the same 4 criteria as Kandel et al. (1983), providing consistency and consensus.

For a paper to claim that the published work has identified a new neurotransmitter, several of these criteria would be met - and the paper would acknowledge in the discussion which ones have not been met. For this particular paper, this reviewer finds that condition 1 is clearly met.

Conditions 2 and 3 seem to be met by electrophysiology, but there are caveats here. High KCl stimulation is a blunt instrument that will depolarize absolutely everything in the prep all at once and could result in any number of non-specific biological reactions as a result of K+ rushing into all neurons in the prep. Moreover, the results in 0 Ca2+ are puzzling. For creatine (and for the other neurotransmitters), why is there such a massive uptick in release, even when the extracellular saline is devoid of calcium?

Response: Classic transmitters are released in a Ca++ dependent manner when stimulated by KCl, though they also had a Ca++ independent component as also shown in our Figure 5 E and F.

Condition 4 is not discussed in detail at all. In the discussion, the authors elide the criterion of receptors specified by Purves by inferring that the existence of postsynaptic responses implies the existence of receptors. True, but does it specifically imply the existence of creatinergic receptors? This reviewer does not think that is necessarily the case. The authors should be appropriately circumspect and consider other modes of inhibition that are induced by activation or potentiation of other receptors (e.g., GABAergic or glycinergic).

Response: Kandel et al. did not list this.

Condition 5 may be met, because authors applied exogenous creatine and observed inhibition. However, this is tough to know without understanding the effects of endogenous release of creatine. if they were to test if the absence of creatine caused excess excitation (at putative creatinergic synapses), then that would be supportive of the same. Nicely, Ghirardini et al., 2023 study cited by the reviewers does provide support for this exact notion in pyramidal neurons.

Response: For most commonly accepted transmitters, this criterion has never been met. For example, the simplest case would be ACh at the neuromuscular junction. Howver, we have now found that choline is clearly present in SVs. So, how does anyone be sure that only ACh is released only, or how does anyone rule out effects of choline on postsynaptic cells when cholinergic neurons are stimulated?

Many synapses are now known to release more than one transmitter, making it difficult to define the effect of one transmitter released endogenously.

These are perhaps reasons why some textbooks do not emphasize similarities of endogenously released vs exogenously applied molecules.

For condition 6, the authors made a great effort with Slc6a8. This is a very tough criterion to understand or prove for many synapses and neurotransmitters.

Response: SLC6A8 is a transporter on the cytoplasmic membrane, thus a good candidate for removal of Cr from the synaptic cleft.

In terms of fundamental neuroscience, the story should be impactful. There are certainly more neurotransmitters out there than currently identified and by textbook criteria, creatine seems to be one of them taking all of the data in this study and others into account.

Response: We hope that more will join our lonely efforts in trying to discover more transmitters.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Since the authors largely disregarded questions in the review process, I do not see a point in listing recommendation for the authors again.

Reviewer #2 (Recommendations For The Authors):

1. The different sections of the manuscript are not separated by headers.

Response: We do have separate subheadings.

1. The beginning of the results section either does not reference the underlying literature or refers to unpublished data.

Response: We have a very long introduction which was criticized for being too long and with too much historical citations. We therefore refrained from citation again in the beginning part of the Results section.

1. The text contains many opinions and historical information that are not required (e.g., "It has never been easy to discover a new neurotransmitter, especially one in the central nervous system (CNS). We have been searching for new neurotransmitters for 12 years."; l. 17).

Response: We would like to keep these because most readers are young and do not know the history and difficulties of discovering transmitters.

1. Almeida et al. (2008; doi: 10.1002/syn.20280) provided evidence for electrical activity-, and Ca2+-dependent Cr release from rat brain slices. This paper should be introduced in the introduction.

Response: Done.

1. Fig. 7: A Y-scale for the stimulation protocol is missing.

Response: Done.

Reviewer #3 (Recommendations For The Authors):

The main suggestion by this reviewer (beyond the details in the public review) was to consider the full spectrum of biology that is consistent with these results. By my reading, creatine could be a neurotransmitter, but other possibilities also exist. The authors have highlighted some of those for their Discussion.

Author Response

The following is the authors’ response to the previous reviews

eLife assessment

The manuscript offers important findings on the potential influence of maternally derived extracellular vesicles on embryo metabolism. However, while the content is convincing, the title appears to overstate the study's conclusions due to its speculative nature on the DNA transmission and embryo bioenergetics connection. A more measured title would better represent the evidence presented.

We want to extend our heartfelt appreciation to the editors and reviewers for their invaluable comments on our research. Their feedback has played a crucial role in improving the quality of our manuscript.

We acknowledge the concern regarding the manuscript's title and are fully open to making modifications. Following the recommendation of Reviewer 2, the proposed new title of the manuscript will be “Vertical transmission of maternal DNA through extracellular vesicles associates with altered embryo bioenergetics during the periconception period.”

Reviewer #1 (Public Review):

Q1. Bolumar et al. isolated and characterized EV subpopulations, apoptotic bodies (AB), Microvesicles (MV), and Exosomes (EXO), from endometrial fluid through the female menstrual cycle. By performing DNA sequencing, they found the MVs contain more specific DNA sequences than other EVs, and specifically, more mtDNA were encapsulated in MVs. They also found a reduction of mtDNA content in the human endometrium at the receptive and post-receptive period that is associated with an increase in mitophagy activity in the cells, and a higher mtDNA content in the secreted MVs was found at the same time. Last, they demonstrated that the endometrial Ishikawa cell-derived EVs could be taken by the mouse embryos and resulted in altered embryo metabolism.

This is a very interesting study and is the first one demonstrating the direct transmission of maternal mtDNA to embryos through EVs.

A1. Thank you for your kind comments.

Reviewer #2 (Public Review):

Q2. In Bolumar, Moncayo-Arlandi et al. the authors explore whether endometrium-derived extracellular vesicles contribute DNA to embryos and therefore influence embryo metabolism and respiration. The manuscript combines techniques for isolating different populations of extracellular vesicles, DNA sequencing, embryo culture, and respiration assays performed on human endometrial samples and mouse embryos.

Vesicle isolation is technically difficult and therefore collection from human samples is commendable. Also, the influence of maternally derived DNA on the bioenergetics of embryos is unknown and therefore novel. However, several experiments presented in the manuscript fail to reach statistical significance, likely due to the small sample sizes. This manuscript is a good but incomplete start as to the potential function of maternal DNA transfer via vesicles.

In my opinion the manuscript supports the following of the authors' claims:

1. Different amounts of nDNA and mtDNA are shed in human endometrial extracellular vesicles during different phases of the menstrual cycle.
2. Endometrial microvesicles are more enriched for mitochondrial DNA sequences compared to other types of vesicles present in the human samples.
3. Fluorescently labelled DNA from extracellular vesicles derived from an endometrial adenocarcinoma cell line can be incorporated into hatched mouse embryos.
4. Culture of mouse embryos with endometrial extracellular vesicles can influence embryo respiration and the effect is greater when cultured with isolated exosomes compared to other isolated microvesicles.

My main concerns with the manuscript:

1. Several experiments presented fail to reach statistical significance or are qualitative.
2. The definitive experiments presented in the manuscript are limited to the transfer of DNA in general not mtDNA. Therefore a strong connection with metabolism is missing, diminishing the significance of the findings.

A2. We thank you for your detailed feedback. While we acknowledge the reviewer's concerns regarding sample sizes, we emphasize that this study was intentionally designed as a pilot study and was approved by the IRB with a specific sample size to serve as proof of concept. We fully agree that further research is essential for a more comprehensive understanding of the novel biological process described in this manuscript. When this manuscript is finally accepted, we can submit a new IRB application to obtain a larger sample size, allowing us to delve deeper into demonstrating the connection with metabolism

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Q3. The authors have made significant improvements, and the manuscript now is appropriate for eLife.

A3. Thank you for your consideration.

Reviewer #2 (Recommendations For The Authors):

The authors have made several changes that have improved the manuscript. However, I still have some concerns.

Q4. The title is still too definitive. Something like "Vertical transmission of maternal DNA through extracellular vesicles is associated with changes in embryo bioenergetics during the periconception period" would be more appropriate.

A4. As mentioned earlier in the response to the editors, we acknowledge the concerns regarding the manuscript's title.

Following your recommendation, the proposed new title of the manuscript is “Vertical transmission of maternal DNA through extracellular vesicles associates with altered embryo bioenergetics during the periconception period.”

Q5. I am confused by the incorporation of the new experiment (supplementary figure 7) where embryos are cultured in free-floating synthesized mtDNA. If these sequences were not encapsulated in vesicles I don't think the experiment is relevant. If they were similarly prepared as in the section "Tagged-DNA production and EV internalization by murine embryos" I stand corrected but please clarify or omit. Otherwise, the new data/figure in response to Q11 showing co-localization of mitochondria and EdU-tagged DNA from MVs from Ishikawa cells is more compelling. However, this doesn't separate the uptake of mtDNA alone from the potential uptake of mitochondria, which this manuscript is not focused on.

A5. We apologize for any confusion that may have arisen for the reviewer. We conducted this experiment in response to question Q4 posed by the same reviewer, which specifically inquired about the detection of internalized mtDNA by the embryos.

As previously stated in the revised manuscript, the EdU system does not selectively label mtDNA; instead, it labels any newly synthesized DNA, both nuclear and mitochondrial. We have not found a system that specifically labels mtDNA for subsequent tracing inside EVs or for encapsulation within artificial EVs (which falls outside our expertise). Therefore, we employed labeled mtDNA that we could trace after the embryos' internalization.

While we acknowledge that this approach is not perfect, it does demonstrate the internalization of mtDNA sequences within the embryo. We have revised the manuscript to eliminate any potential sources of confusion. If the reviewer or editors still have concerns about the experiment's suitability, we are open to removing it from the final version of the manuscript. Please refer to page 9 and lines 234-238 for more details."

Author Response

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

General comments:

To reviewer 1 and 3: The following sentences below were added at the beginning of the result section to clarify that the Gr gene expression analysis was performed using bimodal expression systems and to provide a reference that these expression profiles can generally be expected to represent endogenous Gr expression.

"Note that this and all previous Gr expression studies were performed using bimodal expression systems, mostly GAL4/UAS, whereby Gr promotors driving GAL4 are assumed to faithfully reproduce expression of the respective Gr genes. Importantly, we analyzed two or more Gr28-GAL4 insertion lines for each transgene, and at least two generated the same expression profiles (Mishra et al., 2018; Thorne and Amrein, 2008) providing evidence that the drivers reflect a fairly accurate expression profile of respective endogenous genes."

Specific comments:

Reviewer #1 (Recommendations For The Authors):

The important chemogenetic behavioral data would benefit from a clearer presentation including a cartoon to explain what the behavior is and how it is scored. Figure 2 is the key figure in this paper and it would be helpful if the figure were reorganized to guide the non-expert reader to the key result. I recommend labeling the positive controls Gr43a as "sweet" and Gr66a as "bitter" and perhaps organize the presentation to have the negative control at the left, then Gr28ba that had no effect, then group Gr28a with Gr43a for positive valence and Gr28bc with Gr66a for negative valence. I'm not sure what the value is of showing both 0.1 mM and 0.5 mM capsaicin, the text does not explain. The experiment in Figure 2B is important but non-experts will not understand what is being done here - can the authors please provide a cartoon like those in Figure 1 showing what cells are being subjected to chemogenetics and how this differs from Figure 2A?

The reviewer is correct that much can be improved, which we hope to have accomplished with the modifications in Figure 2. We re-organized it to deliver the key result to non-expert readers in an easy way. We added cartoons both explaining how the two-choice preference assays were conducted and indicating which cells express UAS-VR1. The cartoon in Figure 1E and Figure 2A are now directly relatable and should clarify what cells express VR1 (in Figure 2). Positive and negative control experiments using Gr43aGAL4 (a GAL4 knock-in; Miyamoto et al., 2013) and Gr66a-GAL4 are highlighted in the Figure and mentioned upfront in the text to make clear to what the experimental larvae can be compared. We also excluded larvae responses to 0.5 mM capsaicin.

1. The AlphaFold ligand docking in Figure 8 is conducted with Gr28bc monomers, which are unlikely to be the in vivo relevant structure, given that the related OR/ORCO ancestor structures are tetramers. I recommend that this component of the paper either be removed entirely or that the authors redo the in silico work using the AlphaFold-Multimer package reported by Hassabis and Jumper in 2022 https://www.biorxiv.org/content/10.1101/2021.10.04.463034v2. It will be interesting to see what a tetramer structure looks like with the ligand.

We tried but were able to use the recommended package. Even if it were, the problem is that we do not know the partner of Gr28b.c. And while it is not clear whether and how extensive changes in the ligand binding pockets occur when using the monomer prediciton vs a multimer package, we followed the reviewer’s suggestion and removed the modeling from the manuscript.

Minor points:

1. Line 80: I do not think it is biophysically or biochemically plausible that GRs and IRs would assemble into functional heteromeric channels and suggest that the authors either explain how that would work or remove this speculative comment.

We have removed this sentence.

1. Line 246-248: I would tone down the speculation about GR subunit composition - it's still too early days to understand the stoichiometry or the extent that any of the broadly expressed GRs is a co-receptor.

We did not indulge in the possible stoichiometry of Gr complexes, but merely mention that they are composed in general of two or more Gr subunits, for which clear genetic evidence exists: Up to three different putative bitter Gr genes are necessary to elicit responses to bitter compounds, and at least two putative sugar Gr genes are necessary to restore behavioral responses to any sweet tasting chemicals (sugars). Regardless, we have toned down the language, stating now:

“Given the multimeric nature of bitter taste receptors (Sung et al., 2017), one possibility is that the absence of a Gr subunit not required for the detection of denatonium (Gr66a) could favor formation of multimeric complexes containing Gr subunits that recognize this compound (Gr28b.a and/or Gr28b.c).”

1. Line 284: I don't think that co-expression necessarily means that GRs form heteromultimeric channels. It's equally possible that the cell controls subunit assembly to avoid mixing and matching ligand-selective subunits at will. I would tone this down - it's still speculative at this stage. We don't even know yet how this works for OR-Orco, where we do have structures. There is not yet an OR-Orco Cryo-EM structure, so we do not know what the subunit stoichiometry is.

We are not sure what the reviewer’s concern is. While direct biochemical or biophysical evidence is currently lacking, there is strong genetic evidence for heteromeric composition of Gr complexes, both from studies of bitter and sweet receptors/neurons (see response above). It is likely that intrinsic properties facilitate assembly of certain Grs within a taste receptor complex. We have refrained from any speculation about stoichiometry, though given the relatedness of Grs and Ors, it would not be far-fetched to propose that taste receptor complexes are also tetrameric in nature, which was recently proposed for a homomeric channel of the bombyx mori homolog of Gr43a, BmGr9 (Morinaga et al., 2022).

1. Line 305: the work of Emily Troemel and Cori Bargmann PMID: 9346234 should be cited in the Discussion. Theirs was the first experiment to show that valence was a feature of the neuron and not the receptor(s) it expresses.

We have now cited this work in the discussion to acknowledge this important discovery.

1. Figure 1 - the clarity of the organization of the figure could be improved for non-experts. For instance, can the key for the abbreviations be written out at the right of Figure 1A? Second, it is confusing to talk about DOG/TOG neurons "projecting" to the DO/TO - I think the authors mean dendritic innervation, not axons projecting. Maybe having a diagram that cartoons a closeup of the DOG/TOG neurons and how they innervate the cuticular structures would make this clearer. I struggled to go from the pretty staining at the left of B and C to the schematics at the right that colored in which neurons express which receptors.

We appreciate these comments regarding clarity and have amended Figure 1 and made necessary changes in the text and the Figure legend.

1. Figure 3 would benefit from a summary cartoon relating back to the cartoons in Figure 1 to summarize what neurons the authors think are necessary for bitter avoidance.

We very much appreciate this suggestion and have increased clarity by referring to the carton in Figures 1 and 2.

1. Figure 4B - the lowercase letters indicating Gr28 subunits that are being expressed under UAS control (bottom row of table "UAS-Gr28") are easily confused for the lowercase letters a, b used throughout to signify significant differences. I recommend that the authors write out the gene names in this figure to clarify the genes in the rescue experiment.

We changed the text in the Figure accordingly.

1. For non-experts it would be helpful to have a map of the Gr28 gene locus so that people understand the arrangement of the genes and how the Gal4 driver lines map onto the locus.

We have now included such a map in Figure 1B.

Reviewer #2 (Recommendations For The Authors):

1. In the title and multiple times in the text (e.g. lines 121-122), the authors make the claim that different Gr28 genes mediate opposing behaviors. At first, I was not convinced of this claim, but I now believe it may be warranted if integrating the present results with results from Mishra et al., 2018. In the present study, the authors show that different neurons drive opposing behaviors, but they did not show that the genes themselves mediate opposing behaviors. They show evidence for the role of Gr28bc and Gr28ba in aversion, but not the role of Gr28a in attraction. I was thinking that there could be other receptors in Gr28a-expressing neurons that mediate attraction. However, Mishra et al. showed that mutation of all Gr28 genes abolishes preference for RNA/ribose as well as detection of these compounds by Gr28a+ neurons of the terminal organ, an impairment that could be rescued by expressing Gr28a (although Gr28b genes seem to have similar functions), and the present study shows that the other Gr28 genes are not co-expressed with Gr28a in the terminal organ. Is this the line of reasoning that we must take to come to the conclusion in the title? If so, I don't believe it comes through clearly in the paper.

We appreciate this observation. We have modified language in the abstract and the introduction to reflect previous reports of Gr28a as an RNA/ribose receptor (Mishra et al., 2018) and its conversation across dipteran insects (Fujii et al., 2023) where we showed that appetitive behavior for RNA can be mediated via the mosquito homologs in transgenic Drosophila larvae. The reviewer is correct in that there are other appetitive neurons, namely those expressing Gr43a, which defines a set distinct from and non-overlapping with Gr28a neurons (Mishra 2018). This additional information is included in the Figure 1, summarizing expression of the Gr28 genes, Gr66a and Gr43a.

1. The Figure 6 schematic does not show Gr66a+ Gr28- cells as being connected to avoidance behavior. This seems misleading because it seems likely that these cells do promote avoidance (based on known functions of other Gr66a cells). Also, it is not clear what the red dashed line represents.

The Gr66a neurons are indeed also avoidance mediating, but it is not clear which subgroup of these neurons is necessary. Our analysis in Figure 2 using Gr28b.c driving Kir2.1 suggests that a small subset of Gr66a neurons is sufficient to mediate avoidance. It is, however, possible that other subsets not including Gr28b.c can also mediate avoidance. The figure has been modified accordingly, as has the model in Figure 7.

1. I would suggest including the description of Figures 7-8 in the Results instead of the Discussion. In Figure 8, it would be helpful to superimpose labels for the transmembrane domains and extracellular/intracellular sides to better interpret the models.

The modeling was removed from the manuscript (see response above to reviewer 1).

1. The finding that Gr66a mutants show increased denatonium and quinine avoidance (Figure 4 - figure supplement 1) seems like a non sequitur, as it does not relate to the analysis of Gr28 genes. I support the inclusion of these interesting results, but perhaps it could be stated why this experiment was conducted (e.g. as a positive control).

We have reworded this section to make clear why Gr66a mutants were tested (possibly being part of a denatonium receptor complex).

1. An introduction to the nomenclature and gene structure for the Gr28 genes would be helpful. It's not clear how they're all related, e.g. that the Gr28b genes share some exons whereas Gr28a is separate. The Results section alludes to "the high level of similarity between these receptors", and some sort of reference or quantification for this statement would be useful. I also think naming the Gr28b genes with a period (e.g. "Gr28b.c") may be more consistent with the literature.

We have added the structure of the Gr28 genes in the Figure 1B, which was also a suggestion by reviewer 1, and we have amended the naming of the genes.

1. Lines 79-80 state "some GRNs express members of both families", but no citation is provided.

As this sentence was deleted, based on a comment by reviewer 1, this point becomes mute.

1. There are several typos or grammatical mistakes that the authors may wish to correct (e.g. lines 73, 75, 91, 232, 334, 780, 788).

We appreciate the reviewer pointing these errors out to us. The mistakes were corrected.

Reviewer #3 (Recommendations For The Authors):

• Silencing experiments suggest a role for Gr28bc in the avoidance of quinine (Figure 3), while imaging experiments do not support this role (Figure 5G). An explanation is needed to reconcile these findings.

The imaging experiments do support a role for Gr28b proteins in quinine detection in the specific TOG GRN used for all live imaging (Figure 5). This GRN in DGr28 larvae has a significantly lower Ca2+ responses to quinine compared to controls. However, the Ca2+ response could not be rescued to wild type levels by supplementing single Gr28b subunits, suggesting multiple Gr28b proteins are present in a quinine specific receptor complex in this GRN. Also note that Ca2+ responses of DGr28 larvae to quinine is not completely abolished, suggesting some redundancy, possible via Gr33a (Apostolopoulou et al., 2014), also supported by DGr28 larvae, which have still a robust avoidance to quinine. We are confident we have been clearer in arguing this point, both the result and especially the discussion section.

• Silencing experiments specifically targeted neurons expressing Gr28bc and Gr28be (Figure 3). It is important to note why other neurons expressing different members of the Gr28 family were not included in this analysis.

• Inconsistency is observed in the use of different reagents across the experiments. Specifically, all six Gal4 lines were utilized in the Chemical Activation experiments, while only two lines were employed in the silencing experiments.

The silencing experiments asked the specific questions as to what neurons are necessary for avoidance of bitter chemicals. Gr28a-GAL4 and Gr28b.a-GAL4 neurons were omitted because the former mediate feeding preference and not avoidance, and the latter is expressed in the same neurons as Gr28b.e (Figure 1). The remaining two Gr28b genes, Gr28b.b-GAL4 and Gr28b.d-GAL4 are not expressed in the larval taste system (Mishra et al., 2018) as we stated in the introduction/result section, and they were therefore not included in the chemogenetic or Kir2.1 inactivation experiments. We included these genes in rescue experiments, simply to test whether or not they can restore function for sensing denatonium.

As for the chemogenetic activation experiments: two of the GAL4 lines are controls (Gr66a-GAL4 and Gr43GAL4), that were needed to show what can be expected from these experiments.

• The authors did not acknowledge that neurons expressing members of the GR28 family also express other Gr family members, which could potentially contribute to the detection and behavioral responses to the tested bitter compounds.

We believe we did, but we have made that much more explicit in the revised manuscript.

• Gal4 lines from various studies exhibit varying expression patterns, highlighting the necessity for improved reagents. These findings also suggest the importance of employing different Gal4 lines for each receptor to validate the results of the current study.

See response at the beginning of our rebuttal.

• Activating or silencing neurons pertains to the function of the neurons rather than the receptors.

We agree and nothing in the manuscript states otherwise.

Author Response

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

REPLIES TO REVIEWERS

For instance, The DynaMut2 and thermal shift assays point towards less stable variants than wild type, with Tm values slightly lower. On the other hand, the Kd value of variants reported stronger binding of NSP10 with NSP16. How do authors explain this, as the change due to point mutation may not fall within error range?

Concerning the lower Tm values for the mutants compared to wild type NSP10, the errors of the measurements conducted in triplicate are very low (0.1 degrees) indicating that they do not fall into the error range, in particular as the changes in Tm are significant with changes of up to 4 degrees. This is consistent with the DynaMut23 calculations. Furthermore, the differences in Kd values between wild type and mutants are partially significant. Whereas one of the mutants did not display any changes in Kd value. Compared to wild-type NSP10 for both NSP14 and NSP16, the other show a 2 to 3 fold better Kd, with reasonable errors and we consider those as small but significant, and not within error range.

For instance, the conformational ensemble could be utilized for docking with NSP16 and NSP14. There could be a potential alternative pathway for explaining the above changes in Kd. This should be attempted for understanding the role in its functional activity.

We agree with the reviewer. We are working on a follow up manuscript exclusively looking into the NSP10-NSP14/16 interfacial interactions. Our preliminary results from biophysical and biochemical analysis suggests a range of Kd values observed between the mutants and the NSP14/NSP16. We are also investigating changes in the interfacial interactions via crystallography.

Therefore, more quantitative analysis is required to explain structural changes. The free energy landscape reported in the paper may not capture rare transition events or slight rearrangements in side chain dynamics, both these could offer better understanding of mutations.

We agree with the point raised by the reviewer. As mentioned above, we are exclusively looking into these interfacial interactions and binding between different partners, which will be reported in a follow up manuscript.

Recommendations for the authors: please note that you control which, if any, revisions, to undertake

1. Line 206, V104 need to be corrected to A104.

done

1. Line333, does it mean the Kd value of NSP10 binding to NSP16 similar to the Kd value of binding to NSP14?

Yes. Overall, they are in about the same range with a Kd value of around 1 µM for the NSP10-NSP16 complex and 4 µM for the NSP10-NSP14 complex.

1. Figure 3, the colors corresponding to different variants or native NSP10 could be consistent for easier reading and understanding.

The colors have been edited.

1. The data presented in Figure 3d are not clear enough to draw conclusions about the Kd Value in the main text.（Values of variants are smaller than that of wild-type NSP10, indicating a slightly stronger binding to NSP16）

The measured differences are small with 2 to 3 fold differences, but significant and are not within the error range as can be derived from the data and calculated Kd values and their errors.

1. Are there other mutations in the sequence with the top 3 mutations? If yes, is it possible to do the same experiments with that protein? Why not choose the NSP10 of the popular strain for the determination of the binding ability to NSP14 and NSP16.

No, the top three were single point mutations.

1. Enzyme activity assays like ExoN activity detection of NSP14 and vitro activity detection of NSP16 2′-O-MTase could be performed to characterize the effect of these three mutations on biological function.

Yes, it would be good to consider these. We are considering these assays in the follow up manuscript as mentioned above.

1. More details on image acquisition and writing errors need to be clarified and corrected.

Done.

1. Typo in Results section T12, T102, V104 should be A104

Done.

1. DynaMut analysis is extrapolated to explain that "Mutation to a hydrophobic side chain such as Ile, results in a loss of this interaction." There is no data to support this as complexes have not been studied. Perhaps this is speculative at best.

We have changed this sentence to “Mutation to a hydrophobic side chain such as Ile, is predicted to result in the loss of this interaction”, since this was a prediction

Author Response

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

Public Reviews:

Reviewer #1 (Public Review):

Summary: Hansen et al. dissect the molecular mechanisms of bacterial ice nucleating proteins mutating the protein systematically. They assay the ice nucleating ability for variants changing the R-coils as well as the coil capping motifs. The ice nucleation mechanism depends on the integrity of the R-coils, without which the multimerization and formation of fibrils are disrupted.

Strengths: The effects of mutations are really dramatic, so there is no doubt about the effect. The variants tested are logical and progressively advance the story. The authors identify an underlying mechanism involving multimerization, which is plausible and compatible with EM data. The model is further shown to work in cells by tomography.

Weaknesses: The theoretical model presented for how the proteins assemble into fibrils is simple, but not supported by much data.

Agreed. This theoretical INP multimer model was introduced to promote discussion and elicit ideas on how to prove or disprove it. The length and width of the fibres are defined by cryo-ET results, in which the narrow width is just sufficient to accommodate a dimer of the INPs, and the long length requires that several INPs are joined end to end. Their antiparallel arrangement produces identical ends to the dimer and avoids steric clash of the C-terminal cap structures as well as the C-terminal GFP tag. This model can accommodate the wide range of INPs lengths seen in nature (due to different numbers of water-organizing coils) and introduced in mutagenesis experiments (Forbes et al. 2022). It defines a critical role for the R-coil subdomain in joining the dimers together and explains why this region cannot be shortened by more than a few coils either in nature or by experimentation.

In response to specific criticisms of the model (Fig. 9), we have redesigned this to be less schematic and to incorporate several copies of the AlphaFold-predicted structure.

Reviewer #2 (Public Review):

Summary:

This paper further investigates the role of self-assembly of ice-binding bacterial proteins in promoting ice-nucleation. For the P. borealis Ice Nucleating Protein (PbINP) studied here, earlier work had already determined clearly distinct roles for different subdomains of the protein in determining activity. Key players are the water-organizing loops (WO-loops) of the central beta-solenoid structure and a set of non-water-organizing C-terminal loops, called the R-loops in view of characteristically located arginines. Previous mutation studies (using nucleation activity as a read-out) had already suggested the R-loops interact with the WO loops, to cause self-assembly of PbINP, which in turn was thought to lead to enhanced ice-nucleating activity. In this paper, the activities of additional mutants are studied, and a bioinformatics analysis on the statistics of the number of WO- and R-loops is presented for a wide range of bacterial ice-nucleating proteins, and additional electron-microscopy results are presented on fibrils formed by the non-mutated PbINP in E coli lysates.

Strengths:

-A very complete set of additional mutants is investigated to further strengthen the earlier hypothesis.

-A nice bioinformatics analysis that underscores that the hypothesis should apply not only to PbINP but to a wide range of (related) bacterial ice-nucleating proteins.

-Convincing data that PbINP overexpressed in E coli forms fibrils (electron microscopy on E coli lysates).

Weaknesses:

-The new data is interesting and further strengthens the hypotheses put forward in the earlier work. However, just as in the earlier work, the proof for the link between self-assembly and ice-nucleation remains indirect. Assembly into fibrils is shown for E coli lysates expressing non-mutated pbINP, hence it is indeed clear that pbINP self-associates. It is not shown however that the mutations that lead to loss of ice-nucleating activity also lead to loss of self-assembly. A more quantitative or additional self-assembly assay could shine light on this, either in the present or in future studies.

The control cryo-ET experiment where the R-coils were deleted and INP fibres were not seen is consistent with a link between the loss of ice-nucleating activity and the loss of self-assembly. However, we agree that a more direct measurement of the physical state of INP molecules is needed to prove the link.

-Also the "working model" for the self-assembly of the fibers remains not more than that, just as in the earlier papers, since the mutation-activity relationship does not contain enough information to build a good structural model. Again, a better model would require different kinds of experiments, that yield more detailed structural data on the fibrils.

Reviewer #1 also raised these criticisms of the model, which we have responded to (above). Testing the model is a focus of our continuing experiments on INPs.

Reviewer #3 (Public Review):

Summary: in this manuscript, Hansen and co-authors investigated the role of R-coils in the multimerization and ice nucleation activity of PbINP, an ice nucleation protein identified in Pseudomonas borealis. The results of this work suggest that the length, localization, and amino acid composition of R-coils are crucial for the formation of PbINP multimers.

Strengths: The authors use a rational mutagenesis approach to identify the role of the length, localisation, and amino acid composition of R-coils in ice nucleation activity. Based on these results, the authors hypothesize a multimerization model. Overall, this is a multidisciplinary work that provides new insights into the molecular mechanisms underlying ice nucleation activity.

Weaknesses: Several parts of the work appear cryptic and unsuitable for non-expert readers. The results of this work should be better described and presented.

In revising the manuscript for reposting we have rewritten sections to make it more accessible to the non-expert. Incorporating the detailed recommendations of the reviewers has been helpful in this effort.

Recommendations for the authors: please note that you control which revisions to undertake from the public reviews and recommendations for the authors

Reviewer #1 (Recommendations For The Authors):

Introduction: Curiously, there is no mention at all in the introduction of what the biological function of these ice-nucleating proteins is.

We added the following text to the first paragraph of the Introduction: ”INP-producing bacteria are widespread in the environment where they are responsible for initiating frost (4) and atmospheric precipitation (5). As such, these bacteria play a significant role in the Earth’s hydrological cycle and in agricultural productivity.”

Line 70: TXT, SLT, and Y motifs are mentioned, but only the first is described. Also, TXT name alternates between TXT and TxT in the manuscript. (I think the latter is more correct).

These putative water-organizing motifs are introduced in the preceding paper (new ref 8). We now use TxT consistently throughout the manuscript and have converted SLT to SxT because L is an inward-pointing residue that is not directly involved in water organization.

Line 236: A construct with repeats deleted is tested for thermostability, but it is not really explained what hypothesis this experiment is supposed to test.

This is an observation that adds information about the stability of the INP multimers and will need to be explained by the structure.

Line 267: The authors test a mutant where the N-terminal coil is disrupted and find a big effect. Nevertheless, no conclusion is drawn. What does this result mean?

On the contrary, INP activity is not appreciably affected by N-terminal deletion.

Line 269: The CryoEM begins rather abruptly with technical details. Consider introducing the paragraph with a brief statement about what you want to investigate. Also, the analysis seems a little half-hearted.

Given that the authors describe other EM studies of fibrils of the same protein it would be nice with a clear statement about what is new in their study and how it compares to previous studies.

We have added this statement about why we used Cryo-EM: “The idea that INPs must assemble into larger structures to be effective at ice nucleation has persisted since their discovery (6). In the interim the resolving power of cryo-EM has immensely improved. Here we elected to use cryo-electron tomography to view the INP multimers in situ and avoid any perturbation of their superstructure during isolation.”

Fig. 7B: Single-letter amino acid codes are always capitalized.

We have revised this figure to use capital letters for the amino acids.

Fig. 9: This figure is really hard to read even though it is very simplistic. I would consider making a figure with several copies of the AlphaFold model instead. Especially panel D, I do not know what is supposed to show.

We have followed this advice and have completely revised the figure using copies of the AlphaFold model. Panel D (now C) shows two cross-sections through the AlphaFold model.

Line 355 onwards: The model of the INP is the weakest part of the manuscript. This reviewer considers that the model is crude and it is unclear what information the model is supported by. The authors might want to consider running an AlphaFold multimer to get a better model of at least the dimer.

Our objective now is to validate or disprove the model by experimentation using protein-protein cross-linking in conjunction with mass spectrometry, and higher resolution cryo-EM methods.

Reviewer #2 (Recommendations For The Authors):

I would suggest more frankly discussing the weaknesses mentioned in my public review, as well as approaches that could be used in the future to address these.

In the cryo-ET analysis, INP mutations of the R-coils that lead to loss of ice-nucleating activity fail to show fibres in the bacteria (Fig. S4), which is consistent with the loss of self-assembly. We are working on physical methods that can assess the degree of assembly of the different INP constructs and mutations. We are working to validate and improve the working model of INP multimers.

Reviewer #3 (Recommendations For The Authors):

Abstract

Line 18. Below 0 Celsius should be < 0 {degree sign}C.

Done

Line 25. E. coli should be Escherichia coli

Done

Line 29. E. coli should be in italics.

Done

Introduction

The introduction is weak and not suitable for non-expert readers. Moreover, in some parts it is cryptic and it is not clear whether the authors are describing INP in general or PbINP. The introduction should be reorganized to highlight the novelty of this paper compared to Forbes et al. 2022.

The changes we have made to the Introduction can be seen in the ‘documents compared’ version where the changes are tracked.

Line 45. It is unclear whether this paragraph is a result reported in the literature or the result of this work. Please clarify.

These are results reported in the literature as indicated by the references cited in the paragraph.

Line 54. It is not clear whether this paragraph describes PbINP or INP in general.

This paragraph begins with INPs in general and then focuses on PbINP.

Results

Line 109. This section would benefit from a paragraph in which the authors describe the rationale for this bioinformatic analysis.

We added the following Statement: “A bioinformatic analysis of bacterial INPs was undertaken to identify their variations in size and sequence to understand what is common to all that could guide experiments to probe higher order structure and help develop a collective model of the INP multimer.”

Some information is needed on the selected sequences such as sequence identity, what do the authors mean by nr database?

The abbreviation nr has been replaced by ‘non-redundant’. As explained in that same paragraph the sequences selected were those from long-read sequences that could be relied on to accurately count the number of solenoid coils.

Line 144. The standard deviation is necessary to understand whether these differences are statistically significant.

These have been added as p values.

Figure 2. I noticed that the authors used GFP-tagged PbINP. Why? In addition, panel C is never mentioned in the manuscript.

The GFP tag was used to confirm expression of the PbINP in E. coli. We have added this sentence: “As previously described these constructs were tagged with GFP as an internal control for INP production, and its addition had no measured effect on ice nucleation activity (8).”The GFP tag was also useful as in internal control for the heat denaturation experiments featured in Fig. 6, where it lost its fluorescence between 65 and 75 °C.

Fig. 2C is now cited alongside Fig. 2B.

Figure 3. In my opinion, the results of the R-coil deletion should also be shown in Figure 2. Line 171. This section is cryptic. A logo sequence or an alignment of WO-coils and R-coils of PbINP could be helpful for the reader. Instead of the architecture of the whole protein, it would be useful to have the sequence of the R-coils with the residues that the authors mutagenised.

The logo sequences are available in Fig. 1.

Line 202. Here, the authors describe a new experimental setup. As the Materials and Methods section follows the Discussion, the authors should state in the first paragraph of the Results section that IN activity was measured on whole cells.

We have now modified the introductory sentence to read: “Ice nucleation assays were performed on intact E. coli expressing PbINP to assess the activity of the incremental replacement mutants.”

Line 202. The authors investigated the effects of pH and temperature (Line 223) on the IN activity. The authors should better introduce the rationale for these experiments and how they fit within the work.

We have now modified the following sentence to provide the rationale: “To see how important electrostatic interactions were in the multimerization of PbINP as reflected by its ice nucleation activity, it was necessary to lyse the E. coli to change the pH surrounding the INP multimers.”

Line 245. This work is supported by a model provided by Alphafold. I wonder how reliable this model is; the authors should indicate the quality of the model and provide the accuracy values of the residuals.

This information is now provided in Figure S1.

Line 259. Typically in mutagenesis studies, a key residue is substituted with alanine to create a loss of function variant. In this case, the authors have made the following substitutions F1204D, D1208L, and Y1230D, it is not clear to me why the authors have replaced an aromatic residue with one of aspartic acid that is negatively charged.

We have justified these more extreme changes as follows: “For an enhanced effect of the mutations hydrophobic residues were replaced with charged ones and vice versa.”

Line 269. This paragraph seems completely unrelated to the section entitled: The β-solenoid of INPs is stabilized by a capping structure at the C terminus, but not at the N terminus.

We had omitted the sub-heading “Cryo-electron tomography reveals INPs multimers form bundled fibres in recombinant cells”, which is now in place.

Discussion

Overall, the discussion is too long and some parts appear cryptic, this section should be reorganized.

The changes we have made to the Discussion can be seen in the ‘documents compared’ version where the changes are tracked.

Line 354. It is not clear what experimental evidence supports this model. In the results, this model is never mentioned and it is not clear whether it was obtained by computational analysis or not.

The model is presented in the Discussion because it was not arrived at by experimentation but is an attempt to integrate the observations made in the Results section. The experimental evidence that supports this model is reviewed in the Discussion section: “Working model of the INP multimer is consistent with the properties of INPs and their multimers.”

Line 354. The authors used GFP-tagged PbINP. The Authors should discuss the role of GFP in this model and IN activity. A measurement of IN activity on PbINP without GFP would be useful.

We have previously shown in Ref 8 that the GFP tag has no detrimental effect on ice nucleation activity. Our model for the INP multimer can accommodate this C-terminal tag without any steric hindrance.

Line 364. The Authors hypothesize that electrostatic interactions stabilize end-to-end dimer associations. To test this hypothesis, the authors should measure the activity of IN at increasing concentrations of NaCl. It is known that high salt concentrations shield charges by preventing the formation of electrostatic intermolecular interactions.

We have added this sentence to the Discussion: “Another useful test of the electrostatic component to the multimer model would be to study the effects of increasing salt concentration on ice nucleation activity of the E. coli extracts.”

Line 439. Conclusions should be useful for the reader.

Material and Methods

In several sections, the authors refer to what has already been published in Forbes et al. However, the minimum information should also be described in this work. In addition, the Authors should indicate the number of replicates.

The ice nucleation assays on whole cells were done on the WISDOM apparatus, which integrates 100’s of individual measurements to obtain a T50 value. These T50 values were confirmed by assays on the nanoliter osmometer apparatus. The numbers of replicates used on the nanoliter osmometer apparatus are indicated by box and whisker plots in Figs. 5 & 6 with boxes and bars showing quartiles, with medians indicated by a centre line.

Line 500. This paragraph should be removed as the results are not described in the manuscript.

This is a Methods section that describes how that INPs were expression in E. coli. It has details that are important for researchers who want to repeat our findings, such as the use of the Arctic Express strain for producing INP.

Author Response

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

Thank you for the e-mail of 27th September that includes the eLife assessment and reviewers comments on manuscript eLife-RP-RA-2023-91861. We have considered these, added additional data and made various changes to the text as detailed below. We now submit a modified version that we would be happy to view as the ‘Version of Record’.

We are very pleased to note the highly positive reports from the reviewers. The major change we have made is to alter the Introduction to include further consideration of the development of the ‘bar-code’ hypothesis. As highlighted by reviewer 2 the Lefkowitz/Duke University Group have been major proponents of this concept. However, as with many topics their views did not emerge in isolation. Indeed we (specifically Tobin) were developing similar ideas in the same period (see Tobin et al., (2008) Trends Pharmacol Sci 29, 413-420). Moreover, other groups, particularly that of Clark and collaborators at University of Texas, were developing similar ideas using the beta2-adrenoceptor as a model at least as early as this (e.g. Tran et al., (2004) Mol Pharmacol 65, 196-206). As such we have re-written parts of the Introduction to reflect these early studies whilst retaining information on more recent studies that have greatly expanded such early work. This has resulted in the addition of extra references and re-numbering of the Reference section. We have also provided statistical analysis of agonist-induced arrestin interactions with the receptor as requested by a reviewer and performed additional studies to assess the effect of the GRK2/3 inhibitor in agonist-regulation of phosphorylation of the hFFA2-DREADD receptor. This has led to an additional author (Aisha M. Abdelmalik) being added to the paper.

To address first the ‘public reviews’

Reviewer 1

1. We agree that we do not at this point explore the implications of the tissue specific barcoding we observe and report. However, as noted by the reviewer these will be studies for the future.

2. The question of why these are only 2 widely expressed arrestins and very many GPCRs is not one we attempt to address here and groups using various arrestin ‘conformation’ sensors are probably much better placed to do so than we are.

Reviewer 2

1. It is difficult to address the potential low level of ‘background’ staining in some of the immunocytochemical images versus the ‘cleaner’ background in some of the immunoblotting images. The methods and techniques used are very distinct. However, it should be apparent that the immunoblotting studies are performed (both using cell lines and tissues) post-immunoprecipitation and this is likely to reduce such background to a minimum. This is obviously not the case in the immunocytochemical studies. It is also likely, even though the antisera are immune-selected against the peptide target, there may be some level of immune-recognition this is not limited to the phosphorylated residues.

2. Whilst this reviewer has commented in detail in the ‘recommendations’ section on the use of English, the other reviewers have not, and we do not find the manuscript challenging to follow or read.

Reviewer 3

1. We agree that the mass-spectrometry presented is not quantitative. The intention was for the mass spec to be a guide for the development of the antisera used in the study. We have re-written the initial part of the Results section (page 7) to state that phosphorylation of Ser297 was evident in the basal and agonist-stimulated receptor whilst phosphorylation of Ser296 was only evident following agonist addition.

2. Immunoblotting is intrinsically variable as parameters of antiserum titre in re-used samples is not assessed and although we are aware that FFA2 displays a degree of constitutive activity (see for example Hudson et al., (2012) J Biol Chem. 287(49):41195-209) we did not make any specific effort to supress this by, for example, including an inverse agonist ligand. Agonist-regulation of phosphorylation of the receptor, as detected in cell lines by the anti- pThr306/pThr310antiserum, is exceptionally clear cut in all the images displayed, and as we note for the pSer296/pSer297 antiserum this was always, in part, agonist-independent.

The point about compound 101 not being tested directly in the immunoblotting studies performed on the cell line-expressed receptor is a good one. We have now performed such studies which are shown as Figure 2E. These illustrate that the GRK2/3 inhibitor compound 101 does not reduce substantially agonist-induced phosphorylation of the receptor at least as detected by the pThr306/pThr310antiserum or by the pSer296/pSer297 antiserum. Equally this compound had little effect on recognition of the receptor. As the PD2 mutations which correspond to the targets for the pThr306/pThr310antiserum have no significant effect on recruitment of arrestin 3 in response to MOMBA (please see additional statistical analysis in modified Figure 2C) this is perhaps not surprising. Moreover, the PD1 mutations that correspond to the pSer296/pSer297antiserum also, in isolation, only have a partial effect of MOMBA-induced interactions with arrestin 3.

1. The use of phosphatase inhibitors is an integral part of these studies. As noted in Materials we used PhosSTOP (Roche, 4906837001). However, we failed to make it sufficiently clear that this reagent was present throughput sample preparation for both cell lines and tissue studies. This had been specified previously by two of us (SS, FN, see Fritzwanker S, Nagel F, Kliewer A, Stammer V, Schulz S. In situ visualization of opioid and cannabinoid drug effects using phosphosite-specific GPCR antibodies. Commun Biol. 6, 419 (2023)) but we agree this was insufficient and we now correct this oversight by making this explicit in Results.

Recommendations

Reviewer 1

Competing interest: We apologise for this typographic error. It is now corrected.

Figures: We have upgraded the figure images to 300dpi and this markedly improves readability

Reviewer 2

Revisiting writing: We thank the reviewer for their assessment of the text. However, we do not feel that ‘every sentence in the entire manuscript could be clarified’ is a reasonable statement. Neither of the other reviewers commented on this. Each of the authors read and approved the manuscript.

Figures: see response to Reviewer 1. We have greatly enhanced image quality at this part of the process.

Statistics on Figure 2: We apologise for this oversight. Although there were no significant differences in potency for MOMBA to promote interactions with arrestin-3 to each of the PD mutants versus wild type receptor, there were in terms of maximal effect. Statistical analysis was performed via one-way ANOVA followed by Dunnett’s multiple comparisons test. This is now detailed directly in Figure 2C and its associated legend. As noted by the reviewer there was indeed a highly significant effect of the GRK2/3 inhibitor compound 101 and this is now also noted in Figure 2D and its associated legend.

Units on page 9: pEC50 is considered as Molar by default but we have now specified this. PD1-4: It would be cumbersome to write out (and to read) 8 mutations that make up PD1-4 and hence we think this is specified appropriately in the Figure.

Reviewer 3

1. Mass spec: Please see comment point 1 to reviewer 3.

2. Immunoblotting and compound 101: We have done so.

3. Phosphatase inhibition: see public comments, reviewer 3.

Author Response

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

We are grateful to all the reviewers for their thoughtful comments and the efforts they put into reviewing our manuscript. These are highly positive and constructive reviews. Thank you! We have updated our manuscript to include further discussion of several important points (as suggested by reviewers) and addressed reviewer suggestions individually below.

Reviewer #1 (Public Review):

This remarkable and creative study from the Asbury lab examines the extent to which mechanical coupling can coordinate the growth of two microtubules attached to isolated kinetochores. The concept of mechanical coupling in kinetochores was proposed in the mid-1990s and makes sense intuitively (as shown in Fig. 1B). But intuitive concepts still need experimental validation, which this study at long last provides. The experiments described in this paper will serve as a foundation for the transition of an intuitive concept into a robust, quantitative, and validated model.

The introduction cites at least 5 papers that proposed mechanical coupling in kinetochores, as well as 5 theoretical studies on mechanical coupling within microtubule bundles, so it's clear that this manuscript will be of considerable interest to the field. The intro is very well written (as is the manuscript in general), but I recommend that the authors include a brief review of the variable size of k-fibers across species, to help the reader contextualize the problem.

We agree with the reviewer’s suggestion and have added a brief review of variable k-fiber sizes to the Introduction section (lines 30-35).

For example, budding yeast kinetochores are built around a single microtubule (Winey 1995), so mechanical coupling is not relevant for this species.

Indeed, the use of yeast kinetochores to study mechanical coupling is an odd fit, because these structures did not evolve to support such coupling. There is no doubt that yeast kinetochores are useful for demonstrating mechanical coupling and for measuring the stiffnesses necessary to achieve coupling, but I recommend that the authors include a caveat somewhere in the manuscript, perhaps in the place where they discuss their use of simple elastic coupling as compared to viscoelastic coupling or strain-stiffening. It's easy to imagine that kinetochores with large k-fibers might require complex coupling mechanisms, for example.

Even though yeast kinetochores are built around single microtubules, mechanical coupling has still been proposed to help coordinate the dynamics of sister kinetochores in yeast (Gardner et al. 2005, see main text for full reference). We have added this important point to the Introduction section of the manuscript (lines 33-35). The microtubules attached to sister kinetochores are oriented oppositely to one another, in an anti-parallel arrangement that differs from the parallel arrangement we studied here. Nevertheless, it seems likely to us that coordination of anti-parallel microtubule growth between the single microtubules attached to sister kinetochores in yeast relies at least partly on mechanical coupling. One of the many ways we foresee our dual-trap assay being useful in the future is to test how anti-parallel microtubule growth and shortening can be coordinated via mechanical coupling. Of course, since kinetochores can change the dynamics of their attached microtubules (Umbreit et al., 2012, “The Ndc80 kinetochore complex directly modulates microtubule dynamics”), the kinetochores from different species may have also evolved unique mechanisms of modifying microtubule tension-dependent dynamics to achieve coordination of their attached microtubules. Thus far, in vitro reconstitutions using kinetochore assemblies from metazoans have not yet achieved the coupling stability that we routinely achieve with isolated yeast kinetochores. As reconstitutions with kinetochores from other species improve, it will be very interesting to test for species-specific differences in how the kinetochores influence microtubule dynamics and in how effectively they can coordinate microtubules via mechanical coupling.

We note that the (visco)elastic properties of yeast kinetochores, and their relative simplicity compared to other kinetochores, shouldn’t significantly affect our primary experimental results. Yeast kinetochores are relatively small and the force on each bead changes very slowly in our experiments (see Figure S3-1 for examples), so the kinetochore’s change in length over time is very slow and very small. We have added this point to the Methods section of the manuscript (lines 479-484). We agree that mechanical coupling in species with large k-fibers might rely on more complex material properties, such as viscoelasticity or strain-stiffening. In principle, that type of complexity could be incorporated into our dual-trap experiments by altering the simulated linker. We view this as an interesting area for future study.

And is mechanical coupling relevant for holocentric kinetochores like those found in C. elegans?

This is a very interesting question. While holocentric kinetochores do not form k-fiber bundles (O’Toole et al., 2003, “Morphologically distinct microtubule ends in the mitotic centrosome of Caenorhabditis elegans” and Redemann et al., 2017, C. elegans chromosomes connect to centrosomes by anchoring into the spindle network), mechanical coupling could be even more important for them compared to monocentric kinetochores because tip-attached microtubules both near each other AND at opposite ends of the same chromosome must grow at similar enough rates to stay attached to the same chromosome. In C. elegans prometaphase, opposite chromosome ends move towards the same pole as the chromosome itself oscillates, suggesting that microtubule plus ends attached to the same chromosome are growing in the same direction at the same time (Maddox et al., 2004, ““Holo”er than thou: Chromosome segregation and kinetochore function in C. elegans”). Microtubules appear to stop growing or shortening after chromosome alignment is complete (Redemann et al., 2017), at which time the plus ends of kinetochore microtubules are in close proximity to the chromosome surface (O’Toole et al., 2003, Redemann et al., 2017). The tight clustering of kinetochore microtubule tips near the chromosome at metaphase, as well as the coordinated movement of chromosome arms preceding metaphase, suggests a high level of inter-microtubule coordination in the congression leading up to metaphase. We propose this coordination could be achieved by mechanical coupling through the kinetochore proteins on the surface of holocentric chromosomes and through the underlying chromosome itself.

The paper shows considerable rigour in terms of experimental design, statistical analysis, and presentation of results. My only comment on this topic relates to the bandwidth of the dual-trap assay, which I recommend describing in the main text in addition to the methods. For example, the authors note that the stage position is updated at 50 Hz. The authors should clearly explain that this bandwidth is sufficiently fast relative to microtubule growth speeds.

Thank you for this suggestion. We have added to the Results section (lines 131-133) that updating the stage position at 50 Hz is sufficient to maintain the desired force. We also modified the Methods section (lines 488-491) to clarify that the stage position is sampled at 200 Hz, which is more than sufficient to accurately show the growth variability present in dual-trap experiments.

After describing their measurements, the authors use Monte Carlo simulations to show that pauses are essential to a quantitative explanation of their coupling data. Apparently, there is a history of theoretical approaches to coupling, as the introduction cites 5 theoretical studies. I would have appreciated it if the authors had engaged with this literature in the Results section, e.g. by describing which previous study most closely resembles their own and/or comparing and contrasting their approach with the previous work.

Thank you for this excellent suggestion. We have added a brief comparison of our work to previous theoretical studies examining the role of mechanical coupling in k-fiber coordination to the Results section (lines 179-185).

Overall, this paper is rigorous, creative, and thought-provoking. The unique experimental approach developed by the Asbury lab shows great promise, and I very much look forward to future iterations.

Reviewer #2 (Public Review):

Leeds et al. investigated the role of mechanical coupling in coordinating the growth kinetics of microtubules in kinetochore-fibers (k-fibers). The authors developed a dual optical-trap system to explore how constant load redistributed between a pair of microtubules depending on their growth state coordinates their growth.

The main finding of the paper is that the duration and frequency of pausing events during individual microtubule growth are decreased when tension is applied at their tips via kinetochore particles coupled to optically trapped beads. However, the study does not offer any insight into the possible mechanism behind this dependency. For example, it is not clear whether this is a specific property of the kinetochore particles that were used in this experiment, whether it could be attributed to specific proteins in these particles, or if this could potentially be an inherent property of the microtubules themselves.

We agree that the experiments described in our work do not distinguish between tension-dependence inherent to the microtubule itself and tension-dependence conferred by the kinetochore. We speculate about reasons why tension might disfavor pausing in paragraph 5 of the discussion (lines 356-366). Given that microtubule growth is suppressed by compression without the presence of kinetochores or other microtubule-associated proteins (Dogterom & Yurke, 1997, Janson et al., 2003, see main text for full reference), it seems plausible to us that tension-dependent dynamics, including pausing behaviors, might be inherent to microtubules. However, experiments with different tension-bearing plus-end couplers will be required to test this idea rigorously. We view this as an interesting area for future study.

The authors simulate the coordination between two microtubules and show that by using the parameters of pausing and variability in growth rates both measured experimentally they can explain coordination between two microtubules measured in their experiments. This is a convincing result, but k-fibers typically have many more microtubules, and it seems important to understand how the ability to coordinate growth by this mechanism scales with the number of microtubules. It is not obvious whether this mechanism could explain the coordination of more than two microtubules.

We wholeheartedly agree, it is of vital importance to understand how the coordination of growth via mechanical coupling scales with the number of microtubules. Indeed, we have already begun studying simulations of bundles of ten to twenty microtubules based on the pausing model developed in this paper. Simulated microtubule tips appear significantly limited when linked by mechanical couplers of similar stiffnesses to those used in the dual-trap assay, supporting the idea that mechanical coupling may be able to explain much of the coordination between microtubules in growing k-fiber bundles. We hope to use these simulations to continue exploring the degree to which mechanical coupling can coordinate k-fiber microtubules in future publications.

The range of stiffnesses chosen to simulate the microtubule coupling allows linkers to stretch hundreds of nanometers linearly. However, most proteins including those at kinetochore must have finite size and therefore should behave more like worm-like chains rather than linear springs. This means they may appear soft for small elongations, but the force would increase rapidly once the length gets close to the contour length. How this more realistic description of mechanics might affect the conclusions of the work is not clear.

While the worm-like chain is likely a better model for individual linker molecules, deformation of the underlying centromeric chromatin is also likely to be important, with viscoelastic properties that are still poorly understood. Rather than using a complicated (viscoelastic or worm-like-chain-based) model with many unconstrained parameters, we felt a simple model with a single stiffness parameter to characterize the coupling material was a better starting point, allowing a straightforward comparison between stiffer and softer coupling. In future work, simulations could be used to study the effects of strain-stiffening and viscoelasticity and ask if these effects might further improve (or degrade) the efficacy of mechanical coupling for coordinating kinetochore microtubules.

The novel dual-bead assay is interesting. However, it only provides virtual coupling between two otherwise independently growing microtubules. Since the growth of one affects the growth of the other only via software, it is unclear whether the same insight can be gained from the single-bead setup, for example, by moving the bead at a constant speed and monitoring how microtubule growth adjusts to the fixed speed. The advantages of the double-bead setup could have been demonstrated better.

Thank you for your suggestion to clarify the advantages of our dual-trap approach compared to single-trap experiments. We have added a paragraph to the Discussion section (lines 315-327) to explain the following points: In a real k-fiber bundle, each microtubule can dynamically adjust its growth speed to the current force being applied. In the same way, the dual-trap assay allows us to examine how both leading and lagging tips dynamically adjust to the other’s growth speed simultaneously. In addition, in our dual-trap assay each microtubule in the pair is grown at the same time relative to preparing the slide and comes from an identical batch of kinetochore-bead and tubulin-containing growth buffer. Any differences in growth speeds between paired microtubules can be attributed to intrinsic microtubule variability, rather than prep-to-prep or sample-to-sample differences in microtubule dynamics.

Reviewer #3 (Public Review):

Leeds et al. employ elegant in vitro experiments and sophisticated numerical modeling to investigate the ability of mechanical coupling to coordinate the growth of individual microtubules within microtubule bundles, specifically k-fibers. While individual microtubules naturally polymerize at varying rates, their growth must be tightly regulated to function as a cohesive unit during chromosome segregation. Although this coordination could potentially be achieved biochemically through selective binding of polymerases and depolymerases, the authors demonstrate, using a novel dual laser trap assay, that mechanical coupling alone can also coordinate the growth of in vitro microtubule pairs.

By reanalyzing recordings of single microtubules growing under constant force (data from their own previous work), the authors investigate the stochastic kinetics of pausing and show that pausing is suppressed by tension. Using a constant shared load, the authors then show that filament growth is tightly coordinated when pairs of microtubules are mechanically coupled by a material with sufficient stiffness. In addition, the authors develop a theoretical model to describe both the natural variability and force dependence of growth, using no freely adjustable parameters. Simulations based on this model, which accounts for stochastic force-dependent pausing and intrinsic variability in microtubule growth rate, fit the dual-trap data well.

Overall, this study illuminates the potential of mechanical coupling in coordinating microtubule growth and offers a framework for modeling k-fibers under shared loads. The research exhibits meticulous technical rigor and is presented with exceptional clarity. It provides compelling evidence that a minimal, reconstituted biological system can exhibit complex behavior. As it currently stands, the paper is highly informative and valuable to the field.

To provide further clarity regarding the implications of their study, the authors may wish to address the following points in more detail:

• Considering the authors' understanding of the quantitative relationship between forces, microtubule growth, and coordination, is the dual trap assay necessary to demonstrate this coordination? What advantages does the (semi)experimental system offer compared to a purely in silico treatment?

Thank you for your suggestion to explain the advantages of our dual-trap approach compared to simulations based on previous recordings of individual microtubules growing under tension. We have added a paragraph about this to the Discussion section (lines 315-327). Previously we knew that a shared load should theoretically tend to coordinate a growing microtubule pair, but we did not know how well, nor did we know the degree of variability that would need to be overcome to achieve coordination. Moreover, there are myriad ways one could model the variability and force dependence in microtubule growth, but not all of them can successfully explain the tip separations we now measure between real microtubule pairs. For instance, our non-pausing model, although entirely derived from force-clamp data, had too much variability and too little coordination between microtubule pairs when we compared simulation results to our dual-trap measurements. Thus, the dual-trap assay allows us to test our assumptions about how variability in microtubule growth arises and how mechanical coupling affects it using real microtubules. Reviewer 2 likewise asked about the advantages of the dual-trap approach relative to single-trap experiments, and we suggest also examining our response to their comment above.

• What are the limitations of studying a system comprising only two individual microtubules? How might the presence of crosslinkers, which are typically present in vivo between microtubules, influence their behavior in this context?

This is a very interesting question. K-fiber microtubules in many organisms are subject to forces along their lattices from crosslinkers that attach them to each other and to other microtubules outside the k-fiber. Bridging fibers, for example, are pushed apart at the spindle equator by kinesin motors like Eg5, and are thought to maintain tension on k-fiber microtubule tips by sliding them towards the pole (Vukusic et al., 2017, “Microtubule Sliding within the Bridging Fiber Pushes Kinetochore Fibers Apart to Segregate Chromosomes"). Passive crosslinkers can also produce diffusion-like forces that drive microtubules to move relative to one another (although to our knowledge this has only been demonstrated with antiparallel microtubules—see Braun et al., 2017, “Changes in microtubule overlap length regulate kinesin-14-driven microtubule sliding”). Testing how these various lattice-based forces might affect k-fiber coordination is of great interest to us, but it is not easy to envision how it could be done in our dual-trap setup, where the two coupled microtubules only interact through mechanical forces and are biochemically isolated from one another (in separate assay chambers). Perhaps a clever new assay could be devised in the future to study the role of crosslinkers in combination with mechanical coupling on the coordination of growing microtubules in parallel.

• How dependent are the results on the chosen segmentation algorithm? Can the distributions of pause and run durations truly be fitted by "simple" Gaussians, as indicated in Figure S5-2? Given the inherent limitations in accurately measuring short durations and the application of threshold durations, it is likely that the first bins in the histograms underestimate events. Cumulative plots could potentially address this issue.

The qualitative trends of tension suppressing pause entrance and promoting pause exit seemed to be insensitive to the choices we made in our segmentation algorithm. We have added a paragraph to the Methods section (lines 558-569) to explain how other choices we tried (a smoothing window of 5 s compared to 2 s and a minimum event duration of 0.01 s compared to 1 s) had only mild effects on the measured force sensitivities but did not affect their signs. This suggests that while imposing a threshold duration almost certainly underestimates the number of shorter events, it does not substantially affect our overall conclusion that tension reduces the rate of pause entry, accelerates pause exit, and speeds assembly during the ‘runs’ between pauses.

For segmenting each position-vs-time record into pause and run intervals, we fit the velocity distribution for each individual recording with a mixture of Gaussians. The distributions from some recordings fit quite well to a sum of Gaussians, while others did not fit as well. However, we found that the exact threshold used to separate runs from pauses (typically between 2 and 4 nm/s) had a surprisingly small effect on what the algorithm differentiated as a pause or a run. The segmentation algorithm and its performance on every record we analyzed can be directly viewed by downloading and running our force-clamp viewer, publicly available at https://doi.org/10.5061/dryad.6djh9w16v.

Reviewer #2 (Recommendations For The Authors):

In Figure 3a it would be helpful to see the traces of forces applied to individual microtubules. This would help to understand both, how the force is distributed between individual microtubules depending on their dynamic state and also to see the fluctuations of individual forces.

We completely agree that understanding how force is distributed between microtubules in our dual-trap assay is both interesting and of great value. Although we decided not to include force vs time traces in the main figures, please refer to Figure S3-1, which shows the force-vs-time curves corresponding to the example position-vs-time traces displayed in Figure 3a, plus examples from two additional microtubule pairs.

Author Response

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

Reviewer #1 (Public Review):

The paper offers some potentially interesting insight into the allosteric communication pathways of the CTFR protein. A mutation to this protein can cause cystic fibrosis and both synthetic and endogenous ligands exert allosteric control of the function of this pivotal enzyme. The current study utilizes Gaussian Network Models (GNMs) of various substrate and mutational states of CFTR to quantify and characterize the role of individual residues in contributing to two main quantities that the authors deem important for allostery: transfer entropy (TE) and cross correlation. I found the TE of the Apo system and the corresponding statistical analysis particularly compelling. I found it difficult, however, to assess the limitations of the chosen model (GNM) and thus the degree of confidence I should have in the results. This mainly stems from a lack of a proposed mechanism by which allostery is achieved in the protein. Proposing a mechanism and presenting logical alternatives in the introduction would greatly benefit this manuscript. It would also allow the authors to place the allosteric mechanism of this protein in the broader context of protein allostery.

As detailed below, we went to great lengths to address these concerns, with an emphasis on the limitations of the model and a proposed mechanism. These revisions should hopefully warrant a re-evaluation of our manuscript.

Reviewer #1 (Recommendations For The Authors):

1. It would greatly benefit the paper to state a proposed mechanism by which allostery is achieved in this protein. Is this through ensemble selection, ensemble induction, or a purely dynamic mechanism? What is the rationale for choosing the proposed mechanism and what are reasonable alternative mechanisms? How does this mechanism fit in the broader context of protein allostery?

Following this comment, we added a VERY extensive description of the proposed mechanism by which allostery is achieved in CFTR and present the rationale for choosing this mechanism (lines 445-97 and Figure 7). Briefly, based on previous experimental results and our results we propose that no single model can explain allostery in CFTR, and that its allosteric mechanism is a combination of induced fit, ensemble selection, and a dynamic mechanism.

1. With a proposed mechanism in place, the choice of a GNM to investigate the mechanism and eliminate alternative mechanisms should be rationalized.

The rational for choosing GNM (and ANM-LD) to study the proposed mechanism is now given in lines 498-510. Please note however, that as mentioned in the response to point 1 (and detailed in lines 445-97), the choice of allosteric mechanism, and ruling out other alternatives was not based solely on GNM and ANM-LD, but also on previous experimental results.

1. A discussion of the strengths and limitations of the GNM are pivotal to understanding the limitations of the results shown. How sensitive are the results to specific details of the model(s)?

a. A discussion of the strengths and limitations of the GNM have been added to the introduction. Please see lines 107-122.

b. Sensitivity of the results to the specific details of GNM:

GNM uses two parameters: the force constant of harmonic interactions and the cutoff distance within which the existence of the interactions is considered. The force constant is uniform for all interactions and is taken as unity. Its value affects only the absolute values of the fluctuations (i.e., their scale) but not their distribution. As we are only looking at fluctuations in relative terms our results are insensitive to its value. GNM uses a cutoff distance of 7-10 Å in which interactions are considered (10 Å used in this study). To test the sensitivity of the results to the cutoff distance we repeated the calculations using 7 Å. As now discussed in lines 170-73 and shown in Figure S2 the results remained largely unchanged.

c. Sensitivity of the results to the specific details of TE: To identify cause-and-effect relations TE introduces a time delay (τ) between the movement of residues. The choice of τ is important: when τ is too small, only local cause-and-effect relations (between adjacent amino acids) will be revealed. if τ is too big, few (if any) cause-and-effect relations will manifest. This is analogous to the effects of a stone throne into a lake: look too soon, before the stone hits the water, and you’ll see no ripples. Look too late, the ripples will have already subsided. In a previous work (PMID 32320672), we studied in detail the effects of choosing different τ values and found that an optimal value of τ which maximizes the degree of collectivities of net TE values is in most cases 3× τopt (τopt is the time window in which the total TE of residues is maximized). Details of how τ was chosen were added to the methods section.

In general, the limitations of the chosen model(s) is difficult to determine from the current manuscript because it is devoid of details of the model. While I understand that GNMs have been widely used to study protein systems, the specifics of the model are central to the current work and thus should be provided somewhere in the manuscript.

a. As mentioned in our response above, the limitations of GNM are now presented (lines 107-122).

b. The specifics of the model are now given in more detail in the methods section.

c. In addition, as mentioned above, the results are largely independent of the values of the model’s parameters.

b. Would changing the force constants to a more anisotropic model qualitatively change the results?

a. GNM assumes isotropic fluctuations, and the calculations are based on this assumption. Therefore, GNM is inherently an isotropic model.

b. Importantly, we complement the GNM-TE calculations with ANM-LD simulations, which predict the normal modes in 3D using an anisotropic network model.

1. How repeatable is the difference between no ATP bound and ATP bound CFTR? I worry that the differences in TE in Figures 1 and 3A are mainly due to two different crystallization conditions. Is there evidence that two different structures of the same protein in the same ligand state lead to small changes in TE?

To address this concern, we repeated the calculations using the structures of the ATP-free and bound forms of zebrafish CFTR. As now explained in text (lines 298-303) and shown in Figure S8 the effects of ATP are highly repeatable.

1. Collective modes - why should we expect allostery to be in the most collective modes? Let alone the 10 most? Why not do a mode by mode analysis? Why, for example, were two modes removed page 9 first full paragraph?

a. Collective modes: We have erroneously referred to the slow modes as collective modes. This has now been corrected throughout the manuscript.

b. Let alone the 10 most?

c. why should we expect allostery to be in the most collective modes? Residues that are allosterically coupled are expected to display correlated motions. The slow modes (formerly referred to as “collective modes”) are generally the most collective ones, i.e., display the greatest degree of concerted motions. We therefore expect these modes to contain the allosteric information.

d. Furthermore, as now explained in the text (lines 163-69) and in Figure S1 the Eigenvalue decays of ATP-free and -bound CFTR demonstrate that the 10 slowest GNM modes sufficiently represent the entire dynamic spectrum (the distribution converges after the 10th slow mode).

e. Why not do a mode by mode analysis? It is entirely possible to do a mode-by-mode analysis. However, our view is that the allosteric dynamics of a protein is best represented by an ensemble of modes, rather than by individual ones. We found (as detailed here PMID 32320672) that it is more informative to first use the complete set of modes that encompasses the dynamics (the 10 slowest modes in our case) and then gradually remove the dominant modes.

f. As explained in text (lines 254-7) and more elaborately in our previous work (PMID 35644497), the large amplitude of the slowest modes may hide the presence of “faster” modes that may nevertheless be of functional importance. Removal of the 1-2 slowest modes often helps reveal such modes.

g. Why, for example, were two modes removed page 9 first full paragraph? As explained for the ATP-free form (lines 257-60), removal of these two slowest modes allowed the “surfacing” of dynamic features which were hidden before. We propose that these dynamic features are functionally relevant (see lines 304-19). Removal of other modes did not provide additional insight.

Minor issues:<br /> 1. Statements like "see shortly below" should be made more specific (or removed completely).

Corrected as suggested

1. "interfered" should be "inferred" page 10 middle of the first full paragraph

Corrected as suggested

1. End parenthesis after "(for an excellent explanation about the correlation between TE and allostery see (41)." Page 4 middle of first full paragraph

Corrected as suggested

Reviewer #2 (Public Review):

In this study, the authors used ANM-LD and GNM-based Transfer Entropy to investigate the allosteric communications network of CFTR. The modeling results are validated with experimental observations. Key residues were identified as pivotal allosteric sources and transducers and may account for disease mutations.

The paper is well written and the results are significant for understanding CFTR biology.

Reviewer #2 (Recommendations For The Authors):

Technical comments:

p4 Please explain how is the time delay parameter tau chosen (ie. three times the optimum tau value...)? It seems this unknown time should depend on the separation between i and j. Is the TE result sensitive to the choice of tau? How does the choice of cutoff distance of GNM affect the TE result?

a. The choice of τ is important: when τ is too small, only local cause-and-effect relations (between adjacent amino acids) will be revealed. if τ is too big, few (if any) cause-and-effect relations will manifest. This is analogous to the effects of a stone throne into a lake: look too soon, before the stone hits the water, and you’ll see no ripples. Look too late, the ripples will have already subsided. In a previous work (PMID 32320672), we studied in detail the effects of choosing different τ values and found that an optimal value of τ which maximizes the degree of collectivities of net TE values is in most cases 3× τopt (τopt is the time window in which the total TE of residues is maximized). Details of how τ was chosen were added to the methods section.

b. To test the sensitivity of the results to the cutoff distance we repeated the calculations using 7 Å. As now discussed in lines 170-173 and shown in Figure S2 the results remained largely unchanged.

It would be nice to directly validate the causal prediction by GNM-based TE. For example, is it in agreement with direct causal observation of MD simulation? If the dimer is too big for MD, perhaps MD is more feasible for the monomer (NBD1+TMD1).

a. The causality we determined using GNM-based TE is in good agreement with conclusions drawn from single channel electrophysiological recordings and rate-equilibrium free-energy relationship analysis (Sorum et al; Cell 2015, and see lines 8691, and 364-70).

b. To the best of our knowledge, causality relations in CFTR are yet to be determined by MD simulations (This is likely because the protein is too big and the conformational changes are very slow). We cannot therefore compare the causality.

c. Conducting MD simulations on half of CFTR (NBD1+TMD1) is not likely to be very informative: the ATP binding sites are formed at the interface of NBD1 and NBD2, and the ion translocation pathway at the interface of the TMDs.

p5 How are the TE peak positions different from other key positions as predicted by GNM, such as the hinge positions with minimal mobility of the dominant GNM modes?

Following this comment, we compared the positions of the GNM-TE peaks and the hinge positions as determined by GNM. As now discussed in lines 173-178 and shown in Figure S3 we observed partial overlap which was nevertheless statistically significant (Figure S3).

p7 How to select the 10 most collective GNM modes? Why not use the 10 slowest GNM modes?

We have actually used the 10 slowest GNM modes, but in an attempt to cater for the non-specialist reader, we referred to them as the most collective ones. This has now been corrected throughout the manuscript and the terminology that is now used is “10 slowest modes”

p9 There exist other ANM-based methods for conformational transition modeling. So it would be nice to discuss their similarity and differences from ANM-LD, and compare their predictions.

Alternative ANM (and other elastic network models) -based methods are now mentioned and referenced in lines 144-50. These methods are different from ANM-LD in the details of the all atom simulations and in their integration with the elastic network model. It is not trivial to reanalyze CFTR’s allostery using these methods and is beyond the scope of this work.

Regarding the prediction of order of residue motions, can one directly observe such order by superimposing some intermediate conformation of ANM-LD with the initial and end structure?

This would indeed be very attractive approach to visualize the order of events and following this comment we have tried to do just so. Unfortunately, we failed: Superimposing pairs of frames provided little insight, and we therefore compiled a video comprising all frames, or videos based on averages of several time delayed frames. We found that it is next to impossible to discern (using the naked eye) the directionality of the fluctuations and follow the order of conformational changes. Therefore, at this point, we have abandoned this endeavor.

Reviewer #3 (Public Review):

This study of CFTR, its mutants, dynamics, and effects of ATP binding, and drug binding is well written and highly informative. They have employed coarse-grained dynamics that help to interpret the dynamics in useful and highly informative ways. Overall the paper is highly informative and a pleasure to read.

The investigation of the effects of drugs is particularly interesting, but perhaps not fully formed.

This is a remarkably thorough computational investigation of the mechanics of CFTR, its mutants, and ATP binding and drug binding. It applies some novel appropriate methods to learn much about structure's allostery and the effects of drug bindings. It is, overall, an interesting and well written paper.

There are only two main questions I would like to ask about this quite thorough study.

Reviewer #3 (Recommendations For The Authors):

1. Is it possible that the relatively large exothermic ATP hydrolysis itself exerts a force that causes the observed transitions? Jernigan and others have explored this effect for GroEL and some other structures. The effects of ATP binding and hydrolysis are likely often confused, and both are likely to be important.

It is well established by many studies that ATP hydrolysis is not required to drive the conformational changes or to open the channel, and that ATP binding per-se is sufficient (e.g., We have clarified this point in lines 521-30.

1. For the case of ivacaftor, would a comparison of the motion's directions show that ivacaftor might be compensating simply by its mass being located in a site to compensate for the mass changes from the mutations (ENMs with masses needed to address this). We have observed such cases on opposite sides of a hinge.

We do not think that this is the case, from the following reasons:

a. Ivacaftor corrects many gating mutations (e.g., G551D, G178R, S549N, S549R, G551S, G970R, G1244E, S1251N, S1255P, G1349D) which are spread all over the protein. Ivacaftor binds to a single site in CFTR, and it is therefore unlikely that its mass contribution corrects all these diverse mass changes.

b. The residues that comprise the Ivacaftor binding were identified as allosteric “hotspots” in both the ATP-free and -bound forms (Figures 2B, 3B, and 6A), also in the absence of the drug. This indicates that the dynamic traits of this site is intrinsic to it, and that once bound, the drug acts by modulating these dynamics

The Abstract does not repeat some of the more interesting points made in the paper and would benefit from a substantial revision.

Corrected as suggested

There are just a few minor points (just words):

P 3 line 2 of first full ¶: "effects" should be "affects"

Corrected as suggested

P 6 first lilne "per-se" should be "per se"

Corrected as suggested

Further down that page "two set" should be "two sets"

Corrected as suggested

Even further down that same page "testimony" should be "support"

Corrected as suggested

P 10, 5 lines from the bottom "impose that" is awkward

Changed to “define”

Author Response

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

Public Reviews:

Reviewer #1 (Public Review):

The authors have previously employed micrococcal nuclease tethered to various Mcm subunits to the cut DNA to which the Mcm2-7 double hexamers (DH) bind. Using this assay, they found that Mcm2-7 DH are located on many more sites in the S. cerevisiae genome than previously shown. They then demonstrated that these sites have characteristics consistent with origins of DNA replication, including the presence of ARS consensus sequences, location of very inefficient sites of initiation of DNA replication in vivo, are free of nucleosomes, they contain a G-C skew and they locate to intergenic regions of the genome. The authors suggest, consistent with published single molecule results, that there are many more potential origins in the S. cerevisiae genome than previously annotated.

The results are convincing and are consistent with prior observations. The analysis of the origin associated features is informative.

Reviewer #2 (Public Review):

By mapping the sites of the Mcm2-7 replicative helicase loading across the budding yeast genome using high-resolution chromatin endogenous cleavage or ChEC, Bedalov and colleagues find that these markers for origins of DNA replication are much more broadly distributed than previously appreciated. Interestingly, this is consistent with early reconstituted biochemical studies that showed that the ACS was not essential for helicase loading in vitro (e.g. Remus et al., 2009, PMID: 19896182). To accomplish this, they combined the results of 12 independent assays to gain exceptionally deep coverage of Mcm2-7 binding sites. By comparing these sites to previous studies mapping ssDNA generated during replication initiation, they provide evidence that at least a fraction of the 1600 most robustly Mcm2-7-bound sequences act as origins. A weakness of the paper is that the group-based (as opposed to analyzing individual Mcm2-7 binding sites) nature of the analysis prevents the authors from concluding that all of the 1,600 sites mentioned in the title act as origins. The authors also show that the location of Mcm2-7 location after loading are highly similar in the top 500 binding sites, although the mobile nature of loaded Mcm2-7 double hexamers prevents any conclusions about the location of initial loading. Interestingly, by comparing subsets of the Mcm2-7 binding sites, they find that there is a propensity of at least a subset of these sites to be nucleosome depleted, to overlap with at least a partial match to the ACS sequence (found at all of the most well-characterized budding yeast origins), and a GC-skew. Each of which is a characteristic of previously characterized origins of replication.

Overall, this manuscript greatly broadens the number of sites that are capable of loading Mcm2-7 in budding yeast cells and shows that a subset of these additional sites act as replication origins. Although these sites do have a propensity to include a match to the ACS, these studies suggest that the mechanism of helicase loading in yeast and multicellular organisms is more similar than previously thought.

Reviewer #1 (Recommendations For The Authors):

Specific Comments:

1. The proposal, based on this study, that replication in S. cerevisiae is similar to that in Human cells (mentioned in the abstract, introduction and end of discussion) is not supported by the evidence, either in this paper or elsewhere. The authors suggest that even these inefficient origins are directed by specific sequences that load Mcm2-7 DH, but there is no evidence that this occurs outside a limited clade of budding yeasts and certainly no in human cells. Furthermore, the distribution and efficiency of origins of replication Human cells has not been shown to parallel the findings in this paper. Thus, the conclusion should be removed since it makes a statement that S. cerevisiae and Human cells have similar mechanisms for origin location. This might confuse non-specialists who do not appreciate the subtleties.

The reviewer's concern that we could confuse non-specialists is well-founded. We have made the following changes to emphasize the point that, while a wider distribution of origins makes S phase in yeast more like that in humans, the genome replication programs in the two organisms remain distinctly different:

1) The last sentence of the abstract was changed as follows:

a. These results shed light on recent reports that as many as 15% of replication events initiate outside of known origins, and they reveal S phase in yeast to be surprisingly similar to that in humans.

b. These results shed light on recent reports that as many as 15% of replication events initiate outside of known origins, and this broader distribu5on of replica5on origins suggest that S phase in yeast may be less dis5nct from that in humans than is widely assumed.

1. A sentence in the results was changed as follows:

a. Another characteris5c of known origins that we could use as a criterion to assess the nature of Mcm binding sites is the presence of an ACS.

b. Another characteris5c of known origins in S. cerevisiae (although not in most other organisms) that we could use as a criterion to assess the nature of Mcm binding sites is the presence of an ACS.

1. We changed the last sentence of the Discussion as follows:

a. On the other hand, the sharply focused nature of its replication origins made S phase in yeast appear distinct from that in other organisms. Our discovery that sites of replica5on ini5a5on in yeast are much more widely dispersed than previously believed, with at least 1600 and possibly as many as 5500 origins, emphasizes its continued relevance to understanding genome duplication in humans.

b. On the other hand, the sharply focused nature of its replication origins made S phase in yeast appear dis?nct from that in other organisms. Although by no means elimina5ng this dis5nc5on, our discovery that sites of replication ini5a5on in yeast are much more widely dispersed than previously believed, with at least 1600 and possibly as many as 5500 origins, emphasizes yeast's continued relevance to understanding S phase in humans.

1. The authors discuss in the introduction that origins in S. cerevisiae are equivalent to ARS sequences. Why didn't they ask if the inefficient origins also confer ARS activity? This would be a valuable addition and a very simple experiment.

The inefficient origins are not expected to confer ARS activity, because origins that are not licensed in essentially every G1 will be diluted out by cell division. We confirmed the absence of our inefficiently licensed origins in a data set generated by high throughput sequencing of a genomic library that was selected for origin activity (PMID: 23241746), but we did not note the results of this analysis in our manuscript, because the low complexity of the library used made this negative result uninformative. To clarify this point, we added the bolded clauses to the following sentences in the Introduction and Discussion:

1. Origins vary widely in their efficiency, with some being used in almost every cell cycle while others may be used in only one in one thousand S phases (Boos and Ferreira, 2019), with only the former being capable of supporting plasmid replication in the traditional ARS assay.
2. "Thus, we can detect Mcm complexes that are loaded in as few as 1 in 500 cells (Foss et al., 2021), even though such low affinity Mcm binding sites are not expected to be capable of supporting autonomous replication of a plasmid."

1. While the authors have shown that Mcm2-7 is loaded adjacent to the principal ARS consensus sequence, consistent with biochemical studies on pre-RC assembly, two reports have shown that the Mcm2-7 ChIP is dependent on the B2 element of ARS1, but the ORC ChIP is not, suggesting that Mcm2-7 is loaded there (See Lipford and Bell, Mol. Cell 2007 and Zou and Stillman, Mol. Cell. Biol. 2000).

We have added the following two sentences in the Results section to note these reports:

"Furthermore, in the case of ARS1, two reports have demonstrated a requirement for the B2 element for Mcm loading, though not for Orc binding, suggesting that Orc may bind to the ACS but then load Mcm at the B2 element (Zou and Stillman 2000; Lipford and Bell 2001). This would still leave Mcm loaded downstream of the ACS, but we note this result to emphasize that not all details of Mcm loading in vitro have been definitively established."

**Reviewer #2 (Recommendations For The Authors):>>

Specific points:

1. The authors state "It is notable that the Mcm-ChEC panel of Figure 3A shows no obvious change in Mcm stoichiometry across the entire range, from low abundance, at the bottom, to high abundance, at the top." The ChEC method does not intrinsically measure stoichiometry so this conclusion needs more explanation. The authors appear to be referring to the distribution of Mcm2-7 reads being similar across all origins, but this does not measure how many double hexamers are present at an origin. If the stoichiometry argument is based on a finding that each origin has only a single 60 bp region that is protected by Mcm2-7 (rather than a distribution of 60 bp regions spread across the origin), then the authors should provide more compelling evidence than what is shown in Fig. 3A.

We agree with the reviewer that our conclusion needs more explanation, and we have therefore made the following change, which we believe clarifies the point that we were trying to convey:

We agree with the reviewer that our conclusion needs more explanation, and we have therefore made the following change, which we believe clarifies the point that we were trying to convey:

1. Original version: It is notable that the Mcm-ChEC panel of Figure 3A shows no obvious change in Mcm stoichiometry across the entire range, from low abundance, at the bottom, to high abundance, at the top. This argues against models in which higher replication activity at more active origins reflect the loading of more Mcm double-hexamers at those origins within a single cell.

2. Updated version: It is notable that, when Mcm is present, it is present predominantly as a single double-hexamer (right panel of Figure 3A), and that this remains true across the entire range of abundance shown in Figure 3A. This argues against models in which higher replication activity at more active origins is caused by the loading of more Mcm double-hexamers at those origins within a single cell, since such models predict that multiple Mcm footprints should be more prevalent at the top (high abundance) of the Mcm-ChEC heat map in Figure 3A than at the bottom.

1. The authors state "we estimate that ~1-2 % cells have an Mcm complex loaded at the Mcm binding sites in the eighth cohort (ranks 1401-1600)" but it is not clear how this estimate is calculated. An explanation would help the reader to understand this statement.

We have expanded on our earlier statement to clarify how we arrived at the estimate:

1. Original version: Based on our previous analysis of MCM occupancy (Foss et al., 2021), which showed that approximately 90% cells have an MCM complex loaded at one of the most active known replication origins, we estimate that ~1-2 % cells have an Mcm complex loaded at the Mcm binding sites in the eighth cohort (ranks 1401-1600).

2. Updated version: We have previously used Southern blodng to demonstrate that approximately 90% of the DNA at one of the most active known origins (ARS1103) is cut by Mcm-MNase (Foss et al., 2021), and to thereby infer that 90% of cells have a doublehelicase loaded at this origin. Using this as a benchmark, we estimate that ~1-2 % cells have an Mcm complex loaded at the Mcm binding sites in the eighth cohort (ranks 14011600).

1. Although there is evidence that some subset of the CMBS sites exhibit nucleosome depletion, an ACS, and a GCskew, the authors should do a better job of making the reader aware that it is likely that a decreasing percentage of the individual origins in a group include these characteristic and that this is a likely factor explaining the increasingly rare use of these sites as Mcm2-7 loading sites and origins of replication.

We have added the following text to the Discussion to draw the reader's attention to this possibility, while also noting that we do not believe it to be a major factor in the increasingly rare use of sites within the first 5,500 CMBSs as replication origins:

Furthermore, it is possible that, as one moves to lower abundance groups of CMBSs within the most abundant 5500 sites, a smaller fraction of sites within those groups have any origin function at all. If one takes this model to the extreme, it would suggest that the continuous decline in replication activity seen in Figure 2B between the group comprised of ranks 1-200 and that comprised of ranks 1401-1600 reflects an ever increasing fraction of CMBSs with zero origin activity. At the other extreme, the decline in replication activity could be interpreted within a framework in which 100% of CMBSs in each group function as replication origins, but that their replication activity declines with rank, perhaps because continuously decreasing fractions of cells in the population contain a single double-hexamer. While the truth presumably lies between these two extremes, we favor a model that tilts toward the latter view, because of the abruptness of the transition that appears around rank 5,000 in (1) nucleosomal architecture (Figures 3A, 3B and S3); (2) intergenic versus genic localization and transcription levels (Figure 4A); (3) EACS position weight matrix scores (Figure 5B); and (4) GC skew (Figure 6B). By these criteria, the CMBSs below rank 5000 appear relatively homogeneous, while still showing a gradual decline in replication activity with MCM abundance within the range of detection (11600). Our assumption is that the qualitative homogeneity is more consistent with a quantitative, but not qualitative, change in CMBSs with declining MCM abundance among the top 5000 CMBSs.

1. The argument that there are as many as 5,500 origins is not well justified. Similarly, the evidence that there are even 1,600 origins is not compelling. As the authors state, to see the peaks observed in the various analyses (ssDNA association, nucleosome depletion, etc.) of the increasingly less populated CMBSs (e.g. those with fewer ChEC reads), only a small subset of the CMBS are likely to have a given characteristic. Given that the loading of a Mcm2-7 double hexamer makes any site a potential origin, it would be more appropriate to say that there could be as many as 5,500 potential origins but many if not most are unlikely to ever direct initiation.

The reviewer is correct that, because many of our analyses rely on group averages rather than individual measurements, we are oien unable to make statements that can be applied to every member of a group. We had tried to emphasize this point in our original manuscript with the following two sentences (in bold), which were in the Results and Discussion, respectively:

1. First, clear peaks of ssDNA signal extend down to the eighth cohort (brown line), which corresponds to CMBSs ranked 1401-1600. Of course, this does not imply that all of these sites function as replication origins, and nor does it imply that no sites below that rank do so, since we have reached the limits of detection of this ssDNA-based assay. Nonetheless, it suggests that replication activity is common among sites extending at least down to rank 1600.

2. Of course, we do not conclude that all CMBSs with ranks lower than 5500 function as replication origins, nor that none with ranks above 5500 do so, but only that the number of replication origins is likely to be approximately an order of magnitude higher than widely believed.

We have now added a third sentence to further underline this point (in bold):

Second, by averaging signals of replication from multiple Mcm binding sites, we were able to extract weak signals of replication. This is due to the fact that noise, which is randomly distributed, will tend to cancel itself out, while signals of replication will consistently augment the signal at the midpoint of the origin (Figure 2). An inevitable shortcoming to this approach is that it precludes analysis of specific sites; in other words, not every member of the group will share the average characteristic of that group.

A separate issue that this touches on is the distinction between a replication origin and a site at which Mcm2-7 has been loaded. While it strikes us as unlikely that a loaded Mcm complex would be completely incalcitrant to activation, it is a formal possibility. To alert the reader to this issue, we have added the following clause, in bold, to the Abstract, and we have also added the sentence below that to the Discussion:

We conclude that, if sites at which Mcm double-hexamers are loaded can function as replication origins, then DNA replication origins are at least 3-fold more abundant than previously assumed, and we suggest that replication may occasionally initiate in essentially every intergenic region.

Finally, it is important to note that, in equating Mcm binding sites with potential replication origins, we are assuming that if an Mcm double-hexamer is loaded onto the DNA, then it is conceivable that that complex can be activated.

1. The author's discussion of the relationship between Mcm2-7 location relative to the ACS and the mechanism of of Mcm2-7 loading does not consider that Mcm2-7 double hexamers can slide on DNA after loading (for example, Remus et al., 2009 PMID: 19896182). Thus, the authors are not looking at sites of loading only the distribution of Mcm2-7 molecules after loading. In addition, biochemical experiments do not predict a particular Mcm2-7 position relative to the ACS. Indeed, at ARS1, one would predict that the close proximity of the second weak match to the ACS (the B2 element) to the primary ACS would lead the Mcm2-7 double hexamer being initially formed at a site overlapping the ARS1 ACS. It is much more likely that the explanation for the distribution of Mcm2-7 locations relative to the ACS is that the ORC-bound ACS and the nucleosomes immediately flanking the origin prevents Mcm2-7 from occupying the right-side of the origin as illustrated in Fig. 5D.

We have tried to emphasize this point more clearly. In our original manuscript, we had brought up the possibility of Mcms sliding after being loaded in the following context (see bolded clause):

Specifically, in 112 out of 146 instances in which a peak of Mcm signal was within 100 base pairs of a known ACS, that peak was downstream of the ACS. The 34 exceptions may reflect (1) incorrect identification of the ACS; (2) incorrect inference of the directionality of the site; or (3) sliding of the Mcm complex after it has been loaded.

We have now added the following to further emphasize the point:

In interpreting the results above, it is important to remember that the locations at which we are detecting Mcm complexes by ChEC do not necessarily reflect the locations at which those complexes were loaded, since Mcm double-hexamers can slide along the DNA after loading (Remus et al. 2009; Gros et al. 2015; Foss et al. 2019).

We have also softened the following conclusion by changing "confirmation of" to "support for":

"...our results...provide in vivo support for in vitro predictions of the directionality of Mcm loading by Orc..."

There are missing references in several places:

1. "For example, 15 of the 56 genes that contained a high abundance site have been implicated in meiosis and sporulation and are not expressed during vegetative growth (~5 out of 56 expected from random sampling), consistent with previous observations (Mori and Shirahige, 2007)." Should include Blitzblau et al., 2012 (PMC3355065) which showed that Mcm2-7 loading was impacted by differences in meiotic and mitotic transcription.

2. "In contrast to the low abundance sites, the most abundant 500 sites showed a preference for convergent over divergent transcription (left of vertical dotted line in Figure 4B), in agreement with a previous report (Li et al., 2014)." This preference was first pointed out in MacAlpine and Bell, 2005 (PMID: 15868424).

3. "This sequence is recognized by the Origin Recognition Complex (Orc), a 6-protein complex that loads MCM (Broach et al., 1983; Deshpande and Newlon, 1992; Eaton et al., 2010; Kearsey, 1984; Newlon and Theis, 1993; Singh and Krishnamachari, 2016; Srienc et al., 1985)." This list should include a reference to Bell and Stillman, 1992 (PMID: 1579162), which first described ORC and showed that it recognized the ACS. It would also be more helpful to the reviewer to distinguish the references that identified that ACS from those concerning ORC binding to it.

We thank the reviewer for pointing out these missing references, and we have added them. We have also separated the references that note the identification of the ACS sequence from those that demonstrate Orc binding to that sequence.

Author Response

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

Reviewer #1 (Public Review):

"MAGIC" was introduced by the Rong Li lab in a Nature letters article in 2017. This manuscript is an extension of this original work and uses a genome wide screen the Baker's yeast to decipher which cellular pathways influence MAGIC. Overall, this manuscript is a logical extension of the 2017 study, however the manuscript is challenging to follow, complicated by the data often being discussed out of sequence. Although the manuscripts make claims of a mechanism being pinpointed, there are many gaps and the true mechanisms of how the factors identified in the screen influence MAGIC is not clear. A key issue is that there are many assumptions drawn on previous literature, but central aspects of the mechanisms being proposed are not adequately shown.

Key comments:

1. Reasoning and pipelines presented in the first two sections of the results are disordered and do not follow figure order. In some instances, the background to experimental analyses such as detailing the generation of spGFP constructs in the YKO mutant library, or validation of Snf1 activation are mentioned after respective results are discussed. This needs to be fixed.

We thank the reviewer for pointing out potential confusion to readers. We have revised the first two sections according to reviewer’s suggestion. (Page 4-6)

1. In general there is a lack of data to support microscopy data and supporting quantification analysis. The validity of this data could be significantly strengthened with accompanying western blots showing accumulation of a given constructs in mitochondrial sub compartments (as was the case in the lab’s original paper in 2017).

We appreciate the reviewer’s suggestion on biochemical validations. However, the validity of this imaging-based assay for detecting import of cytosolic misfolded proteins into mitochondria, including the use of FlucSM as a model misfolding-prone protein, was carefully established in our previous study by using appropriate controls, super resolution imaging, APEX-based proximity labeling, and classical biochemical fractionation and protease protection assay (Ruan et al., 2017 Nature, ref. 10). We have reminded readers of these validation experiments in the previous study on Page 4, line 14-17.

In recent years, advancements in imaging-based tools have allowed many protein interactions and dynamic processes, which were previously examined by using biochemical assays in lysates of populations of cells, to be observed with various level of quantitation in live cells with intact cellular compartments. Many of these assays, e.g., the RUSH assay for ER to Golgi transport, FRAP-based analysis for nuclear/cytoplasmic shuttling of proteins, or FRET-based assays for protein-protein interactions, have been well accepted and even embraced by the respective fields of study once validated with genetic and biochemical approaches. The advantages for live-cell imaging-based assays are often their unique ability to report dynamic processes or unstable molecular species with spatiotemporal sensitivity. Respectfully, it is our view, based on our own experience, that the traditional protease protection assay is not adequate or sufficiently quantitative for examining the presence of unstable misfolded proteins in mitochondrial sub-compartments, given the obligatorily lengthy in vitro cell lysis and mitochondrial isolation process, during which the unstable proteins are continuously being degraded. This likely explains our previous biochemical fractionation result that only weak protein signals were detected in the matrix fraction (Ruan et al., 2017 Nature, ref. 10). In addition, unlike stably folded, native mitochondrial matrix proteins, misfolded/unfolded proteins such as Lsg1 or FlucSM are highly susceptible to protease treatment. This sensitivity makes the assay unreliable for detecting such proteins if trace amount of the protease penetrates mitochondrial membranes during cell lysis even without detergent treatment.

While we agree that protease protection assay is highly valuable for qualitative detection of the presence of a protein in certain mitochondrial compartments or determining its topology on membranes, this assay (regrettably in our hands) does not allow quantitative comparisons that were necessary for this study, because of inherent sample to sample variation, yet the laborious and low throughput nature of this assay makes it difficult for adequate statistical analysis. Furthermore, the level of protein detection in various fractions is highly sensitive to how the sample is treated with protease and detergent. Our imaging-based quantification, on the other hand, allows us to compare increased or decreased presence of GFP11-tagged proteins in mitochondria under different metabolic conditions or in different mutant or wild-type strains. Data from hundreds of cells and at least three independent biological replicates allowed us to apply adequate statistical analysis to aid our conclusion.

1. Much of the mechanisms proposed relies on the Snf1 activation. This is however not shown but assumed to be taking place. Given that this activation is central to the mechanism proposed, this should be explicitly shown here - for example survey the phosphorylation status of the protein.

Both REG1 deletion and low glucose conditions have been demonstrated extensively for Snf1 phosphorylation and activation in yeast (e.g., many seminal papers from Marian Carlson’s and other lab, such as ref. 24-28). In our study, we have indeed corroborated this by showing that Mig1 was exported from the nucleus in Δreg1 mutant and in low glucose conditions (Figure 1—figure supplement 2H and I. The mechanism of Snf1-mediated nuclear export of Mig1 has been characterized in detail as well (e.g., ref. 29-31).

Recommendations for the authors: please note that you control which, if any, revisions, to undertake

Reviewer #1 (Recommendations For The Authors):

SPECIFIC COMMENTS

Genetic Screen o Line 20 - the narrative moves to SNF1, but the reasoning for the selection of this Class I substrate is not defined. What was the basis for this selection - what happened to the other Class I substrates. It is stated in the text that the other Class I proteins show the same increase in spGFP signal. The data showing this should be included in the Supp Figure 1 for transparency.

We have moved the narratives of Snf1 function to the second section and clarified that we were interested in this gene due to its central role in metabolism and mitochondrial functions that may influence MAGIC (Page 5: line 16-20). Other genes in class 1 were shown in Table S1. Detailed discussion of other genes in this category is beyond the scope of this study.

Snf1/AMPK prevents MP accumulation in mitochondria:

The FlucDM data in human RPE-1 mitochondria seems to be added to only increase the significance of the work. The mechanisms suggested here with Hap4 would not be possible in human cells as there is no homologue of this protein in human cells. Making generalisations that these pathways are conserved based on this one experiment is not appropriate.

We appreciate this feedback. Although the focus of this study is the regulation of MAGIC by the yeast AMPK Snf1, we would like to share our initial observation that suggests a similar role of AMPK in human RPE-1 cells. We acknowledge that the underlying mechanisms regarding the downstream transcription factors and pathway for misfolded protein import could be different in mammalian cells, but the overall effect of AMPK in mitochondrial biogenesis is well known to resemble that of Snf1. To avoid making over-generalization, we changed our statement of conclusion to: ‘These results suggest that AMPK in human cells regulates MP accumulation in mitochondria following a similar trend as in yeast, although the underlying mechanisms might differ between these organisms.’ (Page 7: line 2-4)

Mechanisms of MAGIC regulation by Snf1:

While the lysosome is ruled out here the authors have not considered the proteasomes. Is there a reason for this? Given accumulation of aggregates outside of mitochondria, and previous connections of the proteasome to mitochondrial quality control this would be an obvious thing to check. We examined the role of lysosomal degradation here because it is known to be activated under Snf1active condition (ref. 37). We appreciate this feedback and have included a new analysis on MG132treated FlucSM spGFP strains in which PDR5 gene was deleted to avoid drug efflux.

This result suggests that the proteosome inhibitor did not ablate the difference in FlucSM accumulation between these conditions. That MG132 promoted mitochondrial accumulation of FlucSM in both high glucose and low glucose conditions was not surprising, as FlucSM is also degraded by proteasome in the cytosol (Ruan et al., 2017 Nature, ref. 10), and preventing this pathway could divert more of such protein molecules toward MAGIC. (Page 7: line 26-29).

Line 13 "we hypothesized that elevated expression of mitochondrial preproteins induced by the activation of Snf1-Hap4 axis (REF) may outcompete MPs for import channels". This statement has some assumptions. The authors have not shown that Snf1 is activated in thier models and more importantly that they have an accumulation of mitochondrial preproteins. The data that follows using the cytosolic domains of the receptors is hard to rationalise without seeing evidence that there is in fact pre-protein accumulation or impacts on the mitochondrial proteome in this system.

As stated in our response to main point [3], Snf1 activation in reg1 mutant or in low glucose is evidenced by our data showing Mig1 export from nucleus to cytoplasm and had also been shown in many previous publications. A recent study (Tsuboi et al., 2020 eLife) also showed a dramatic increase in mitochondrial volume fraction in Δreg1 cells and wild-type cells in respiratory conditions, further supporting the role of Snf1 in mitochondrial biogenesis. We have provided relevant references in the manuscript (ref. 24-28).

The ability of Tom70 cytosolic domain (Tom70cd), which can bind mitochondrial preproteins but not localize to mitochondria due to lack of N-terminal targeting sequence, to compete with endogenous Tom70 for mitochondrial preproteins has been well documented (ref. 47-49). However, we agree with the reviewer that a future quantitative proteomics study to measure changes in mitochondrial proteome under Tom70cd over-expression could allow more accurate interpretation of our experimental result.

AMPK protects cellular fitness during proteotoxic stress:

The inhibition of preprotein import by overexpressing the cytosolic domains of receptors is not supported with some proof of principle data. If this was working as the authors assume, it is not clear why only an effect with Tom70 is observed. The majority of the mitochondrial proteome is imported via Tom20/Tom22 so this does not align with what the authors are suggesting. Is the Tom70CD and any associated Hsp proteins facilitating the observed changes to the MPs?

We thank the reviewer for raising this point. We expressed different TOM receptor cytosolic domains but found that Tom70cd had the strongest rescue on MAGIC under AMPK activation conditions. It is possible that certain Tom70 substrates or Tom70-assoicated heat shock proteins inhibit the import of MAGIC substrates. We admit that a clear explanation of this unexpected observation necessitates a better understanding of how native and MAGIC substrates are selected and imported by the outer-membrane channel. We can only offer our best interpretation based on the current state of the understanding, and we feel that we have been careful to acknowledge such in the manuscript.

While the effect of AMPK inactivation reducing FUS accumulation was striking, this was all in the context of overexpression and may not be physiologically relevant - or may occur very transiently under basal conditions. Is GST an appropriate control here, why not use WT FUS? Likewise, one representative image is shown in Figure 5 - can the authors show western blotting that mitochondrial accumulation of FUS can be reduced with AMPK activation?

We thank the reviewer for this suggestion, however, overexpressed FUS WT is also aggregation prone (Zhihui Sun et al., 2011, PloS Biology; Shulin Ju, 2011, PloS Biology; Jacqueline C. Mitchell et., 2013, Acta Neuro). We believe that GST, as a well-folded protein, is an appropriate control (Ruan et al., 2017 Nature, ref. 10). As we discussed in response to main point [1], the in vitro assay involving protease protection and western blots do not allow reliable quantitative comparison in our hands.

In text changes.

The analysis pipeline of the YKO mutant library should be introduced at the very start of the first paragraph, not the end.

Addressed on Page 4, second paragraph

"Fluc" should be introduced as "Firefly luciferase" within the first paragraph of the first section, also need to define SM and DM in FlucSM/FlucDM - these appear to be missing.

Addressed in both Introduction (Page 2: line 29; Page 3: line 8-9) and re-clarified in Result (Page 5: line 27-29)

The role of Reg1 should be explicitly stated in the text, not just in the figure.

Addressed on Page 6: line 3-6

Figure 1H legend states Reg1 (WT) is Snf1-inactive and Reg1 KO is Snf1-active. This wording is confusing and is not supported by data, but by assumption. If the authors want to use this wording then evidence needs to be provided - as suggested above.

We have changed this and other legends to only show genotypes and medium conditions.

"Tom70cd overexpression also exacerbated growth rate reduction due to FlucSM expression in HG medium (Figure 4A; Figure 4 - figure supplement 1A)" should be figure supplement 1B.

Fixed on Page 10: line 10

"These results suggest that glucose limitation protects mitochondria and cellular fitness during FlucSM induced proteotoxic stress through Snf1-dependent inhibition of MP import into mitochondria". The phrase "Snf1-dependent inhibition of MP import into mitochondria" may be misleading, as Snf1 isn't modulating import directly but is acting on transcriptional regulators to modulate mitochondrial import under stress.

We restated the conclusion as follows: ‘These results suggest that Snf1 activation under glucose limitation protects mitochondrial and cellular fitness under FlucSM-associated proteotoxic stress.’ (Page 10: line 20- 21)

"... Significantly increased the fraction of spGFP-positive and MMP-low cells in both HG and LG medium (Figure 4G-K)" should be (Figure 4J-K).

Fixed on Page 11: line 3

Reviewer #2 (Public Review):

Work of Rong Li´s lab, published in Nature 2017 (Ruan et al, 2017), led the authors to suggest that the mitochondrial protein import machinery removes misfolded/aggregated proteins from the cytosol and transports them to the mitochondrial matrix, where they are degraded by Pim1, the yeast Lon protease. The process was named mitochondria as guardian in cytosol (MAGIC).

The mechanism by which MAGIC selects proteins lacking mitochondrial targeting information, and the mechanism which allows misfolded proteins to cross the mitochondrial membranes remained, however, enigmatic. Up to my knowledge, additional support of MAGIC has not been published. Due to that, MAGIC is briefly mentioned in relevant reviews (it is a very interesting possibility!), however, the process is mentioned as a "proposal" (Andreasson et al, 2019) or is referred to require "further investigation to define its relevance for cellular protein homeostasis (proteostasis)" (Pfanner et al, 2019).

Rong Li´s lab now presents a follow-up story. As in the original Nature paper, the major findings are based on in vivo localization studies in yeast. The authors employ an aggregation prone, artificial luciferase construct (FlucSM), in a classical split-GFP assay: GFP1-10 is targeted to the matrix of mitochondria by fusion with the mitochondrial protein Grx5, while GFP11 is fused to FlucSM, lacking mitochondrial targeting information. In addition the authors perform a genetic screen, based on a similar assay, however, using the cytosolic misfolding-prone protein Lsg1 as a read-out.

My major concern about the manuscript is that it does not provide additional information which helps to understand how specifically aggregated cytosolic proteins, lacking a mitochondrial targeting signal could be imported into mitochondria. As it stands, I am not convinced that the observed FlucSM-/Lsg1-GFP signals presented in this study originate from FlucSM-/Lsg1-GFP localized inside of the mitochondrial matrix. The conclusions drawn by the authors in the current manuscript, however, rely on this single approach.

In the 2017 paper the authors state: "... we speculate that protein aggregates engaged with mitochondria via interaction with import receptors such as Tom70, leading to import of aggregate proteins followed by degradation by mitochondrial proteases such as Pim1." Based on the new data shown in this manuscript the authors now conclude "that MP (misfolded protein) import does not use Tom70/Tom71 as obligatory receptors." The new data presented do not provide a conclusive alternative. More experiments are required to draw a conclusion.

In my view: to confirm that MAGIC does indeed result in import of aggregated cytosolic proteins into the mitochondrial matrix, a second, independent approach is needed. My suggestion is to isolate mitochondria from a strain expressing FlucSM-GFP and perform protease protection assays, which are well established to demonstrate matrix localization of mitochondrial proteins. In case the authors are not equipped to do these experiments I feel that a collaboration with one of the excellent mitochondrial labs in the US might help the MAGIC pathway to become established.

We thank Reviewer 2 for these suggestions, but we would like to respectfully offer our difference in opinion:

a. Regarding the suggestion “to isolate mitochondria from a strain expressing FlucSM-GFP and perform protease protection assays”, in our previous study (Ruan et al., 2017 Nature, ref. 10), we have indeed applied two independent biochemical approaches: APEX-mitochondrial matrix proximity labeling and classic protease protection assay using non-spGFP strains, both consistently confirmed the entry of misfolded proteins into mitochondria under proteotoxic stress. Our super-resolution imaging further confirmed the import of the split GFP-labeled proteins to be inside mitochondria. Moreover, as we discussed in response to Reviewer 1’s main point [2], while the suggested biochemical assay is useful for validating topology within mitochondria, it is not quantitative and may not reliably report the in vivo accumulation of misfolded proteins in mitochondria due to the isolation process that takes hours, during which the unstable proteins could be continuously degraded within mitochondria.

While we agree with the reviewer that we do not yet understand how misfolded proteins are imported into mitochondria, it would be unfair to state “as it stands, I am not convinced..” simply because the underlying mechanism remains to be elucidated. We would like to point out that targeting sequences for many well-established mitochondrial proteins are still not well defined. It is well known that mitochondrial targeting sequences are not as uniformly predictable as, for example, nuclear targeting sequences. Our finding that deletion of TOM6 enhances the import of misfolded proteins suggest that their import may involve the TOM channel in a more promiscuous conformation, which may reduce the requirement for a specific sequence-based targeting signal associated with the substrate.

b. Regarding the role of Tom70, in our 2017 study, using proteomics and subsequently immunoprecipitation we validated the binding, albeit not necessarily direct, between misfolded protein FlucSM and Tom70. Therefore, “we speculate that protein aggregates engaged with mitochondria via interaction with import receptors such as Tom70”. Recent studies from different labs confirmed the interactions between Tom70 and aggregation prone proteins (Backes et al., 2021, Cell Reports; Liu et al., 2023, PNAS). In the current study, surprisingly, knockout of TOM70 did not block MAGIC, suggesting redundant components of mitochondria import system may facilitate the recruitment of misfolded proteins in the absence of Tom70, and this does not contradict the notion that Tom70 helps tether protein aggregates to mitochondria.

c. Regarding other studies also showing the import of misfolding or aggregation-prone cytosolic proteins into mitochondria, there have been at least several recent studies in the literature for mammalian cells involving either model substrates or disease proteins (e.g., ref. 12-15; 56-58; Vicario, M. et al. 2019 Cell Death Dis.). The studies are briefly mentioned in Introduction (Page 3, paragraph 2). The present manuscript documents a major effort from our group using whole genome screen in yeast to understand the mechanism and regulation of MAGIC. Many of the screen hits have yet to be studied in detail. We full agree that much remains to be understood about whether and how this pathway affects proteostasis and what might be the evolutionary origin for such a mechanism.

Additional comments:

The genetic screen:

The genetic screen identified five class 1 deletion strains, which lead to enhanced accumulation of Lsg1GFP and a larger set of class 2 mutants, which lead to reduced accumulation. Please note, in my opinion it is not clear that accumulation of the reporters occurs inside the mitochondria. In any case, the authors selected one single protein for further analysis: Snf1, the catalytic subunit of the yeast SNF complex, which is required for respiratory growth of yeast.

The results of the screen are not discussed in any detail. The authors mention that ribosome biogenesis factors are abundant among class 2 mutants. Noteworthy, Lsg1 is involved in 60S ribosomal subunit biogenesis. As Lsg1-GFP11 is overexpressed in the screen this should be discussed. Class 2 mutants also .include several 40S ribosomal subunit proteins (only one of the 60S subunit). What does this imply for the MAGIC model? Also, it should be discussed that the screen did not identify reg1 and hap4, which I had expected as hits based on the data shown in later parts of the manuscript.

We apologize for the confusion, but the GFP11 tag was in fact knocked into the C-terminus of Lsg1 in the endogenous LSG1 locus, and so Lsg1 was not overexpressed in the screen. We have made sure that this information is clearly conveyed in the revised manuscript (Page 4: line 20-22). How the ribosome small subunit affects MAGIC is beyond the focus of the current study and will be pursued in the future.

Regarding why certain mutants did not come out of our initial screen, this is not unexpected as the YKO collection, although extremely valuable to the community, is known to be potentially affected by false knockouts, suppressor accumulation and cross contamination (for references, e.g., Puddu et al., 2019 Nature). Additionally, high-through screens can also miss real hits. In our experience using this collection in several studies, we often found additional hits from analysis of genes implicated by known genetic or biochemical interactions.

Mutant yeast strains and growth assays:

The Δreg1 strain grows poorly in all growth conditions and frequently accumulates extragenic suppressor mutations (Barrett et al, 2012). It would be good to make sure that this is not the case in the strains employed in this study. My suggestion is to do (and show) standard yeast plating assays with the relevant mutant strains including Δreg1, snf1, hap4, Δreg1Δhap4 without the split GFP constructs and also with them (i.e. the strains that were used in the assays).

We thank the reviewer for the suggestion. We were indeed aware of potential accumulation of suppressor mutations from the YKO library. Therefore, deletion mutants like Δreg1 and loss of TFs downstream of Snf1 that we used in the study after the initial screen were all freshly made and validated. At least 3 independent colonies were analyzed for each mutant (mentioned in Methods & Materials; Page 33, line 57). Moreover, the plating assay suggested here may not reveal additional information other than growth, which was taken into consideration during our experiments.

Activation of Snf1 in the relevant strains should be tested with the commercially available antibody recognizing active Snf1, which is phosphorylated at Snf1-T210.

Snf1 activation was validated by the Mig1 exporting from the nucleus. We also noted above that many studies have clearly demonstrated Snf1 activation in reg1 mutant and under low glucose growth (e.g., ref. 24-28).

Effects of Snf1, Reg1, Hap4 and respiratory growth conditions:

The authors show that split GFP reporters show enhanced accumulation during fermentative growth, in Δsnf1, and Δreg1Δhap4 and fail to accumulate during respiratory growth, in Δreg1 and upon overexpression of HAP4. Analysis of Δhap4 should be included in Fig. 2. The suggestion that upon activation of Snf1 enhanced Hap4-dependent expression "outcompetes" misfolded protein import seems unlikely as only a fraction of mitochondrial genes is under control of Hap4. Without further experimental evidence I do not find that a valid assumption. More likely, the membrane potential plays a role: it is low during fermentative growth, in Δsnf1 and Δreg1Δhap4, and high during respiratory growth and in Δreg1 (Hübscher et al, 2016). Such an effect of the membrane potential seems to contradict the findings in the 2017 paper and the issue should be clarified and discussed. In any case, these data do not reveal that GFP reporters accumulate inside of the mitochondria. Based on the currently available evidence they may accumulate in close proximity/attached to the mitochondria. This has to be tested directly (see above).

We have included our analysis of Δhap4 in Page 8: line 14-15 and Figure 2—figure supplement 1H. Consistent with our result for Δreg1Δhap4 in glucose-rich medium, HAP4 deletion also resulted in a significant increase in mitochondrial accumulation of FlucSM in low glucose medium compared to WT. It did not have effect in high glucose condition in which Snf1 is largely inactive.

It is our view that the importance of Hap4 should not be judged by the number of nuclear encoded mitochondrial proteins they regulate. Still, this sub-group comprises a considerable number of proteins (at least 55 genes upregulated by Hap4 overexpression, ref. 43), and certain substrates may be more competitive with misfolded cytosolic proteins for import. Our genetic data strongly suggest that the inhibitory effect of active Snf1 on MAGIC is through Hap4, although we agree with the reviewer that detailed mechanism on how Hap4 substrates may compete with misfolded proteins need to be addressed in future studies.

Membrane potential is important for mitochondrial import. During respiratory growth and in Δreg1, membrane potential is well known to be elevated comparing to fermentative condition (e.g., Figure 4C). Our observation that the import of misfolded proteins into mitochondria is reduced under these conditions simply suggests that this reduction is not due to a lack of membrane potential. This is not in any way contradictory to our 2017 finding that misfolded protein import requires membrane potential (ref. 10).

Again, the accumulation of misfolded proteins in mitochondria, especially the model protein FlucSM, has been validated by using super resolution imaging (Figure 1—figure supplement 1A) in addition to the protease protection assay in our 2017 study.

Introduction and Discussion:

Both are really short, too short in my view. Please provide some background of the general principals of mitochondrial protein import and information of how exactly translocation of cytosolic, aggregated proteins (lacking targeting information) is supposed to work. I do not understand exactly how the authors actually envisage the process.

We thank the reviewer for the suggestion. In the revised manuscript, we have extended both Introduction (Page 2-3) and Discussion section (Page 11-13)

The results from the 2022 eLife paper (Liu et al, 2022), which suggests that Tom70 may "regulate both the transcription/biogenesis and import of mitochondrial proteins so the nascent mitochondrial proteins do not compromise cytosolic proteostasis or cause cytosolic protein aggregation" should be discussed with regard to the data obtained with overexpression of the Tom70 soluble domain.

We thank the reviewer for pointing out that study and we have included a brief comment in Discussion section (Page 12: line 13-16). As the function of Tom70 appears to be complex, we cannot exclude the possibility that overexpression of the cytosolic domain has additional or indirect effects in addition to that due to preprotein binding.

Andreasson, C., Ott, M., and Buttner, S. (2019). Mitochondria orchestrate proteostatic and metabolic stress responses. EMBO Rep 20, e47865.

Barrett, L., Orlova, M., Maziarz, M., and Kuchin, S. (2012). Protein kinase A contributes to the negative control of Snf1 protein kinase in Saccharomyces cerevisiae. Eukaryot Cell 11, 119-128.

Hubscher, V., Mudholkar, K., Chiabudini, M., Fitzke, E., Wolfle, T., Pfeifer, D., Drepper, F., Warscheid, B., and Rospert, S. (2016). The Hsp70 homolog Ssb and the 14-3-3 protein Bmh1 jointly regulate transcription of glucose repressed genes in Saccharomyces cerevisiae. Nucleic Acids Res. 44, 5629-5645.

Liu, Q., Chang, C.E., Wooldredge, A.C., Fong, B., Kennedy, B.K., and Zhou, C. (2022). Tom70-based transcriptional regulation of mitochondrial biogenesis and aging. Elife 11

Pfanner, N., Warscheid, B., and Wiedemann, N. (2019). Mitochondrial proteins: from biogenesis to functional networks. Nat Rev Mol Cell Biol 20, 267-284.

Ruan, L., Zhou, C., Jin, E., Kucharavy, A., Zhang, Y., Wen, Z., Florens, L., and Li, R. (2017). Cytosolic proteostasis through importing of misfolded proteins into mitochondria. Nature 543, 443-446.

I prefer to have "all in one", also due to time limitation.

It would be great to be able to upload the review file as otherwise formatting and symbols get lost.

Reviewer #3 (Public Review):

In this study, Wang et al extend on their previous finding of a novel quality control pathway, the MAGIC pathway. This pathway allows misfolded cytosolic proteins to become imported into mitochondria and there they are degraded by the LON protease. Using a screen, they identify Snf1 as a player that regulates MAGIC. Snf1 inhibits mitochondrial protein import via the transcription factor Hap4 via an unknown pathway. This allows cells to adapt to metabolic changes, upon high glucose levels, misfolded proteins an become imported and degraded, while during low glucose growth conditions, import of these proteins is prevented, and instead import of mitochondrial proteins is preferred.

This is a nice and well-structured manuscript reporting on important findings about a regulatory mechanism of a quality control pathway. The findings are obtained by a combination of mostly fluorescent protein-based assays. Findings from these assays support the claims well.

While this study convincingly describes the mechanisms of a mitochondria-associated import pathway using mainly model substrates, my major concern is that the physiological relevance of this pathway remains unclear: what are endogenous substrates of the pathway, to which extend are they imported and degraded, i.e. how much does MAGIC contribute to overall misfolded protein removal (none of the experiments reports quantitative "flux" information). Lastly, it remains unclear by which mechanism Snf1 impacts on MAGIC or whether it is "only" about being outcompeted by mitochondrial precursors.

We thank Reviewer 3 for the positive and encouraging comments on our manuscript. We agree with the reviewer that identifying MAGIC endogenous substrates and understanding what percentage of them are degraded in mitochondria are very important issues to be addressed. We are indeed carrying out projects to address these questions. We also agree with Reviewer 3 that the effect of Snf1 on MAGIC may have additional mechanisms in addition to precursors competition, such as Tom6 mediated conformational changes of TOM pores. In the revised manuscript, we had added a discussion to address these comments (Page 12: line 21-28).

Reviewer #3 (Recommendations For The Authors):

1. In their screen, the authors utilize differences in GFP intensity as a measure for import efficiency. However, reconstitution of the GFP from GFP1-10 and GFP11 in the matrix might also be affected (folding factors, differential degradation).

Upon Snf1 activation, the protein abundance of mitochondrial chaperones such as Hsp10, Hsp60, and Mdj1, and mitochondrial proteases such as Pim1 are not significantly changed (ref. 35). Therefore, it is unlikely that the folding and degradation capacity of mitochondrial matrix is drastically affected by Snf1 activation.

To examine the effect of Snf1 activation on spGFP reconstitution, Grx5 spGFP strain was constructed in which the endogenous mitochondrial matrix protein Grx5 was C-terminally tagged with GFP11 at its genomic locus, and GFP1-10 was targeted to mitochondria through cleavable Su9 MTS (MTS-mCherryGFP1-10) (ref. 10). Only modest reduction in Grx5 spGFP intensity was observed in LG compared to HG, and no significant difference after adjusting the GFP1-10 abundance (spGFP/mCherry ratio) (Figure 1— figure supplement 3A-D). These data suggest that any effect on spGFP reconstitution is insufficient to explain the drastic reduction of MP accumulation in mitochondria under Snf1 activation. Overall, our results demonstrate that Snf1 activation primarily prevents mitochondrial accumulation of MPs, but not that of normal mitochondrial proteins. (Page 6: line 17-25).

We admit, however, that to fully rule out these factors, specific intra-mitochondrial folding or degradation reporter assays would be needed.

1. Scoring of protein import always takes place using fluorescence-based assays. These always require folding of the "sensors" in the matrix. An additional convincing approach that would not rely on matrix folding could be pulse chase approaches coupled to fractionation assays and immunoprecipitation.

We thank reviewer 3 for this suggestion. In our previous study, we applied two different biochemical assays: APEX proximity labeling, and mitochondrial fractionation followed by protease protection. Both confirmed the entry of misfolded proteins into mitochondria as observed by using split GFP. As we discussed in response to Reviewer 1’s main point [3], the fractionation assays are not quantitative enough for the comparisons made in our study. In particular, during the over 2-hour assay, misfolded proteins continue to be degraded within mitochondria. By using proper controls, our spGFP system provides quantitative comparisons for mitochondrial accumulation of misfolded proteins in non-disturbed physiological conditions.

1. Could the pathway be reconstituted in vitro with isolated mitochondria to test for the "competition hypothesis"

This is an excellent suggestion, but setting up such a reconstituted system is a project on its own. The study documented in this manuscript already encompasses a large amount of work that we feel should be published timely.

1. Fluorescence figures are not colour blind friendly (red-green). This should be improved by changing the color scheme.

We thank reviewer 3 for pointing this out and sincerely apologize for any inconvenience. However, we are unfortunately unable to change all images within a limited time. We will adopt another color scheme in future work.

1. spGFP in human cells appears to form "spot-like" structures. What are these granules?

We indeed observed granule-like structures by spGFP labeled FUS in mitochondria, which is interesting, but we did not investigate this further because it is a not a focus of this study.

Author Response

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

Response to Reviewers

To whom it may concern, Thank you for your constructive feedback on our manuscript. I appreciate the time and effort that you and the reviewers have dedicated to providing your valuable feedback. We are grateful to the reviewers for their insightful comments and suggestions for our paper. I have been able to incorporate changes to reflect the majority of these suggestions provided. I have updated the analysis scripts (at https://github.com/neurogenomics/reanalysis_Mathys_2019) and have listed these changes in blue below:

eLife assessment:

This work is useful as it highlights the importance of data analysis strategies in influencing outcomes during differential gene expression testing. While the manuscript has the potential to enhance awareness regarding data analysis choices in the community, its value could be further enhanced by providing a more comprehensive comparison of alternative methods and discussing the potential differences in preprocessing, such as scFLOW. The current analysis, although insightful, appears incomplete in addressing these aspects.

We thank the reviewing editors for this note. We agree that the differences in preprocessing will affect the results and conceal which step in our reanalysis resulted in the discrepancies we noted. To address this, we have split out our reanalysis into two separate parts - In the main body of the text we discuss the differences resulting from just changing the differential expression approach where we use the same processed data as the authors to enable a fair comparison. Secondly, we still provide the reprocessed data and perform differential expression analysis on it and discuss the cause and impact the differences in the processing steps made to the results.

Reviewer 1:

I think readers would be interested to learn more about the genes that were found "significant" by the original paper but sorted out by the authors. Did they just fall short of the cutoffs? If so, how many more samples would have been required to ascertain significance? This would yield a recommendation for future studies and an overall more positive/productive spirit to the manuscript. On the other hand, I suspect a fraction of DEGs were false positives due to differences in the proportions of cells from different individuals compared to the original analysis. Which percentage of DEGs does this apply to? Again, this would raise awareness of the issue and support the use of pseudobulk approaches.

To investigate the relationship between the genes and how they differ across our analysis we have added a correlation analysis between our different DE approaches (using the same processed data), see paragraph 5 in the manuscript and supplementary table 3. In short, we find that there is a high correlation in the genes’ fold change values across our pseudobulk analysis and the author’s pseudoreplication analysis on the same dataset (pearson R of 0.87 for an adjusted p-value of 0.05) which is somewhat expected given the DE approaches are applied to the same dataset. However, the p-values, which pertain to the likelihood that a gene’s expressional changes is related to the case/control differences in AD, and resulting DEGs vary considerably due to the artificially inflated confidence of the author’s approach (Fig. 1c-e). Despite there being a correlation between the pseudoreplciation and pseudobulk approaches here, we do not think it makes sense to consider how many more samples would have been required to ascertain significance. The differences in results between the two approaches is not negatable with sample size as many DEGs identified by pseudoreplication will be false positives as highlighted in previous work1,2,3,4. However, perhaps we are misinterpreting the reviewer, who may have meant a power analysis which we have not conducted. Such an undertaking would require analysing a multitude of snRNA-Seq of large sample sizes to garner a confident estimate for power calculations based on pseudobulk approaches. Although we agree with the reviewer that this would be beneficial to the field, we do not believe it is in scope for this work. On the reviewer’s note regarding a fraction of DEGs being false positives due to differences in the proportions of cells from different individuals compared to the original analysis - We have analysed the same processed data the authors used to negate the differences caused by the differing processing steps. We thank the reviewer for this suggestion. We also give more insight into the cause of these differences, namely on filtering our nuclei with large proportions of mitochondrial reads and discuss their effect in paragraph 3 (also see Supplementary Figure 2).

Given there are only a few DEGs, it would be good to show more data about these genes to allow better assessment of the robustness of the results, i.e., boxplots of the pseudobulk counts in the compared groups and perhaps heatmaps of the raw counts prior to aggregation. This could rule out concerns about outliers affecting the results.

In Supplementary Figure 3, we have added boxplots of the sum pseudobulked, trimmed mean of M-values (TMM) normalised counts for three of our identified DEGs (b) and three of the authors’ DEGs which they discuss in their manuscript (a) to show the differences in counts across AD pathology and controls for these genes. We hope this gives some insight into the transcriptional changes highlighted by the differing approaches. In our opinion, there is a clear difference in the transcriptional signal in the genes identified from pseudobulk which is not present for the genes identified from the authors approach.

Overall, I believe the paper would deliver a clearer message by mainlining the QC from the original study and only changing the DE analysis. However, if keeping the part about QC/batch correction:

• Assess to which degree changes in cell type proportion are indeed due to batch correction (as suggested in the text) and not filtering by looking at the annotated cell types in the original publication and those in your analysis.

• Also perform the analysis without changing QC and state the # of DEGs in both cases, to at least allow some disentanglement of the effect of different steps of the analysis.

• Please state the number of cells removed by each QC step in the supplementary note.

We thank the reviewer for this suggestion. We agree with performing the DE analysis on the same processed data as the original authors and have split out our reanalysis into two separate parts, primarily focussing on the discrepancies caused by the choice of differential expression (DE) approach. By splitting our analysis in this manner, we can identify the substantial differences in results caused by differing the DE approach in the study. Secondly, we can see how differences in preprocessing affects the DE results in isolation too – see paragraph 8 but in short, the fold change correlation between pseudobulk DE analyses on the reprocessed data vs authors processed data only had a moderate correlation (Pearson R of 0.57).

In regards to the number of cells removed by each QC step, we have added an aggregated view for all samples in supplementary table 3 and also give the full statistics per sample in our Github repository: https://github.com/neurogenomics/reanalysis_Mathys_2019. Moreover, we investigated the root cause in the differences in nuclei numbers, uncovering filtering down to mitochondrial read proportions as the main culprit (Supplementary Figure 2).

I recommend the authors read the following papers, assess whether their methodology agrees with them, and add citations as appropriate to support statements made in the manuscript.

We thank the reviewer for this comprehensive list. We have updated our manuscript and supplementary file and main text throughout to cite many of these where appropriate. We believe this helps add context to our decisions for the differing tools and approaches used as part of the processing pipeline with scFlow and the differential expression approach.

I believe the authors' intention was to show the results of their reanalysis not as a criticism of the original paper (which can hardly be faulted for their strategy which was state-of-the-art at the time and indeed they took extra measures attempting to ensure the reliability of their results), but primarily to raise awareness and provide recommendations for rigorous analysis of sc/snRNA-seq data for future studies.

We thank the reviewer for this note, this was exactly our intent. Furthermore, we are based in a dementia research institute and our aim is to ensure that ensure that the Alzheimer’s disease research field does not focus on spuriously identified genes.We have updated the text of the manuscript (start paragraph 2) to explicitly state this so our message is not misconstrued.

In my opinion, the purpose of the paper might be better served by focusing on the DE strategy without changing QC and instead detailing where/how DEGs were gained/lost and supporting whether these were false positives.

We agree that the differences in preprocessing will affect the results and conceal which step in our reanalysis resulted in the discrepancies we noted. To address this, we have split out our reanalysis into two separate parts - In the main body of the text we discuss the differences resulting from just changing the differential expression approach where we use the same processed data as the authors to enable a fair comparison. Secondly, we still provide the reprocessed data and perform differential expression analysis on it and discuss the impact the differences in the processing steps made to the results. As previously mentioned, we have also added further investigation into the DEGs identified, looking at the correlation across the differing approaches and plotting the counts for selected genes.

For instance, removal with a mitochondrial count of <5% seems harsh and might account for a large proportion of additional cells filtered out in comparison to the original analysis. There is no blanket "correct cutoff" for this percentage. For instance, the "classic" Seurat tutorial https://satijalab.org/seurat/articles/pbmc3k_tutorial.html uses the 5% threshold chosen by the authors, an MAD-based selection of cutoff arrived at 8% here https://www.sc-best-practices.org/preprocessing_visualization/quality_control.html, another "best practices" guide choses by default 10% https://bioconductor.org/books/3.17/OSCA.basic/quality-control.html#quality-control-discarded, etc. Generally, the % of mitochondrial reads varies a lot between datasets.

Apologies, the 5% cut-off was a misprint – the actual cut-off used was 10% which, as the reviewer notes, is on the higher side of what is recommended. We have updated our manuscript to rectify this mistake and discuss the differences in the number of cells caused by the two approaches to mitochondrial filtering in the manuscript (paragraph 3). We found that over 16,000 nuclei that were removed in our QC pipeline were kept by the author’s (Supplementary Fig. 2), explaining the discrepancy in the number of nuclei after QC. Based on Supplementary Fig. 2, it is clear the author’s approach was ineffective at removing nuclei with high proportions of mitochondrial reads which is indicative of cell death5,6. We hope this alleviates the reviewer’s concerns around our alternative processing approach. Moreover, as mentioned, we swapped to compare the differences by DE approaches on the same data to avoid any effect by this.

Reviewer 2:

The paper would be better if the authors merged this work with the scFLOW paper so that they can justify their analysis pipeline and show it in an influential dataset.

We thank the reviewer for this note. We would like to clarify that the purpose of our work was not to show the scFlow analysis pipeline on an influential dataset but rather to raise awareness and provide recommendations for rigorous analysis of single-cell and single-nucleus RNA-Seq data (sc/snRNA-Seq) for future studies and to help redirect the focus of the Alzheimer’s disease research field away from possible spuriously identified genes. We have updated our manuscript text to highlight this (see start paragraph 2). Furthermore, we are aware our original approach reprocessing the data with scFlow will affect the results and conceal which step in our reanalysis resulted in the discrepancies we noted. Thus, we have split out our reanalysis into two separate parts - In the main body of the text we discuss the differences resulting from just changing the differential expression approach where we use the same processed data as the authors to enable a fair comparison. Secondly, we still provide the reprocessed data so that the community can benefit from it and perform differential expression analysis on it and discuss the impact the differences in the processing steps made to the results. We have also added further references supporting the choice of steps and tools used in scFlow in the supplementary text which should address the reviewer’s concerns about justifying the analysis pipeline. Moreover, we identified the cause of the nuclei count differences caused by the two processing approaches, namely on filtering our nuclei with large proportions of mitochondrial reads and discuss their effect in paragraph 3 (also see Supplementary Figure 2).

A major contribution is the use of the authors' own inhouse pipeline for data preparation (scFLOW), but this software is unpublished since 2021 and consequently not yet refereed. It isn't reasonable to take this pipeline as being validated in the field.

We believe our answer to the previous point addresses these concerns - We have added references supporting the choice of steps and tools used in scFlow in the supplementary text which should address the reviewer’s concerns about justifying the analysis pipeline. Moreover, as a result of the pipeline we identified that 16,000 of the nuclei kept by the authors are likely of low quality and indicative of cell death with high mitochondrial read proportions5,6.

They also worry that the significant findings in Mathys' paper are influenced by the number of cells of each type. I'm sure it is since power is a function of sample size, but is this a bad thing? It seems odd that their approach is not influenced by sample size.

We thank the reviewer for highlighting this point. As they noted, we conclude that the original authors number of DEGs is just a product of the number of cells. However, the reviewer states that ‘It seems odd that their approach is not influenced by sample size’. An increase in the number of cells is not an increase in sample size since these cells are not independent from one another - they come from the same sample. Therefore, an increase in the number of cells should not result in an increase in the number of DEGs whereas an increase in the number of samples would. This point is the major issue with pseudoreplication approaches which over-estimate the confidence when performing differential expression due to the statistical dependence between cells from the same patient not being considered. See these references for more information on this point1,2,7,8. We have added a discussion of this point to our manuscript in paragraph 6.

Moreover, recent work has established that the genetic risk for Alzheimer’s disease acts primarily via microglia9,10. Thus, it would be reasonable to expect that the majority of large effect size DEGs identified would be found in this cell type. This is what we found with our pseudobulk differential expression approach – 96% of all DEGs were in microglia. We have updated the text of our manuscript (paragraph 5) to highlight this last point.

References 1. Murphy, A. E. & Skene, N. G. A balanced measure shows superior performance of pseudobulk methods in single-cell RNA-sequencing analysis. Nat. Commun. 13, 7851 (2022).

1. Squair, J. W. et al. Confronting false discoveries in single-cell differential expression. Nat. Commun. 12, 5692 (2021).

2. Crowell, H. L. et al. muscat detects subpopulation-specific state transitions from multi-sample multi-condition single-cell transcriptomics data. Nat. Commun. 11, 6077 (2020).

3. Soneson, C. & Robinson, M. D. Bias, robustness and scalability in single-cell differential expression analysis. Nat. Methods 15, 255–261 (2018).

4. Ilicic, T. et al. Classification of low quality cells from single-cell RNA-seq data. Genome Biol. 17, 29 (2016).

5. Heumos, L. et al. Best practices for single-cell analysis across modalities. Nat. Rev. Genet. 24, 550–572 (2023).

6. Zimmerman, K. D., Espeland, M. A. & Langefeld, C. D. A practical solution to pseudoreplication bias in single-cell studies. Nat. Commun. 12, 738 (2021).

7. Lazic, S. E. The problem of pseudoreplication in neuroscientific studies: is it affecting your analysis? BMC Neurosci. 11, 5 (2010).

8. Skene, N. G. & Grant, S. G. N. Identification of Vulnerable Cell Types in Major Brain Disorders Using Single Cell Transcriptomes and Expression Weighted Cell Type Enrichment. Front. Neurosci. 0, (2016).

9. McQuade, A. & Blurton-Jones, M. Microglia in Alzheimer’s disease: Exploring how genetics and phenotype influence risk. J. Mol. Biol. 431, 1805–1817 (2019).

Author Response

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

eLife assessment

The findings of this article provide valuable information on the changes of cell clusters induced by chronic periodontitis. The observation of a new fibroblast subpopulation, named AG fibroblasts, is interesting, and the strength of evidence presented is solid.

We thank the Reviewing Editor and the Senior Editor for the positive assessment and strong support for our study.

Public Reviews:

Reviewer #1 (Public Review):

In this article, the authors found a distinct fibroblast subpopulation named AG fibroblasts, which are capable of regulating myeloid cells, T cells and ILCs, and proposed that AG fibroblasts function as a previously unrecognized surveillant to orchestrate chronic gingival inflammation in periodontitis. Generally speaking, this article is innovative and interesting.

We truly appreciate this public review.

Reviewer #2 (Public Review):

This study proposed the AG fibroblast-neutrophil-ILC3 axis as a mechanism contributing to pathological inflammation in periodontitis. In this study single-cell transcriptomic analysis was performed. But the signal mechanism behind them was not evaluated.

The authors achieved their aims, and the results partially support their conclusions.

We agree that we must conduct future studies to evaluate our hypothesis.

The mouse ligatured periodontitis models differ from clinical periodontitis in human, this study supplies the basis for future research in human.

This is an important subject. We have previously expressed a concern on the mouse ligature model that the microbial composition of the mouse ligature did not mirror the human oral microbial composition. Therefore, we developed the maxillary topical application (MTA) model, in which human oral biofilm was directly applied to the maxillary gingiva. In this study, the newly developed MTA model was further dissected by single cell RNA seq, which revealed that the extracellular substances of human oral biofilm might be an important trigger of gingival inflammation. RESULT has been revised.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I appreciate the authors' efforts. I think it would be much better to simplify INTRODUCTION.

INTRODUCTION has been simplified as suggested.

Reviewer #2 (Recommendations For The Authors):

1. Many host cells participate in immune responses, such as gingival epithelial cells. AG fibroblast is not the only cell involved in the immune response, and the weight of its role needs to be clarified. So the expression in the conclusion should be appropriate.

RESPONSE: We agree with this comment. Our study identified the AG fibroblast–neutrophil–ILC3 axis as a previously unrecognized mechanism which could play an additional role in the complex interplay between oral barrier immune cells.

1. The main results should be included in the Abstract.

Abstract has been revised.

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

We thank all reviewers for constructive critiques. We plan to perform new experiments and revise our manuscript accordingly. The text and Figures are currently undergoing the revision process. Below highlights our revision plan.

eLife assessment

The findings of this article provide valuable information on the changes of cell clusters induced by chronic periodontitis. The observation of a new fibroblast subpopulation, which was named as AG fibroblasts, was quite interesting, but needs further evidence. The strength of evidence presented is incomplete.

We discovered a new subpopulation of gingival fibroblasts, named AG fibroblasts, using non-biased single cell RNA sequencing (scRNA-seq) of mouse gingival samples undergoing the development of ligature-induced periodontitis. AG fibroblasts exhibited a unique gene expression profile: [1] constitutive expression of type XIV collagen; and [2] ligatureinduced upregulation of Toll-Like Receptors and their downstream signals as well as chemokines such as CXCL12. Thus, we have hypothesized that AG fibroblasts initially sense the pathological stress including oral microbial stimuli and secrete inflammatory signals through chemokine expression.

The current manuscript examined the relationship between AG fibroblasts and oral barrier immune cells focusing on the chemokines and other ligands derived from AG fibroblasts and their putative receptors in those immune cells. Using scRNA-seq data mining programs, our data demonstrated the compelling evidence that AG fibroblasts should play a critical role in orchestrating the oral barrier immunity, at least at the early stages of periodontal inflammation.

We agree that it is important to explore the functional/pathological role of AG fibroblasts. In this revision, we further investigated the role of TLRs in the pathogen sensing mechanism of AG fibroblasts. To accomplish this goal, we applied a newly developed mouse model in which mice were exposed to the maxillary topical application (MTA) of oral microbial pathogens without the ligature placement. With 1 hr exposure with human oral biofilm, not with planktonic microbiota, the mice maxillary tissue exhibited measurable degradation as evidenced by the activation of cathepsin K. To dissect the role of TLRs, we applied the putative stimulants of TLR9 and TLR2/4 using the discrete MTA model. The scRNA-seq from the MTA model revealed that the application of unmethylated CpG oligonucleotide and P. gingivalis lipopolysaccharide (LPS), respectively, induced the activation of chemokines by AG fibroblast.

The revised manuscript reported this critical data with the detailed information. As such the additional figures and corresponding results, discussion and materials & methods were included.

Public Reviews:

Reviewer #1 (Public Review):

In this article, the authors found a distinct fibroblast subpopulation named AG fibroblasts, which are capable of regulating myeloid cells, T cells and ILCs, and proposed that AG fibroblasts function as a previously unrecognized surveillant to orchestrate chronic gingival inflammation in periodontitis. Generally speaking, this article is innovative and interesting, however, there are some problems that need to be addressed to improve the quality of the manuscript.

We appreciate this comment. As suggested, we further investigated the surveillant function of AG fibroblasts by reanalyzing the scRNA-seq data for stress sensing receptors such as Toll-Like Receptors (TLR). In the revision, we addressed the role of TLR in the activation of AG fibroblasts using a newly developed mouse model employing the maxillary topical application (MTA) of putative TLR stimulants. The new information clearly demonstrated that AG fibroblasts play a pivotal role as the surveillant and translating the pathogenic stimulants to oral barrier inflammation through chemokine expression.

Reviewer #2 (Public Review):

This study proposed the AG fibroblast-neutrophil-ILC3 axis as a mechanism contributing to pathological inflammation in periodontitis. However, the immune response in the vivo is very complex. It is difficult to determine which is the cause and which is the result. This study explores the relevant issue from one dimension, which is of great significance for a deeper understanding of the pathogenesis of periodontitis. It should be fully discussed.

We appreciate this comment. We expanded the current understanding of oral immune signal communication in Discussion and highlight how AG fibroblast may fit to it. To address this question, we expanded our investigation in the pathological signal detection by AG fibroblasts by employing the newly developed maxillary topical application (MTA) model. The revised manuscript contains the new information and expanded the discussion in the context of complex immune response.

Reviewer #1 (Recommendations For The Authors):

Detailed comments are listed below:

Abstract：<br /> I am confused about the expression of "human periodontitis-like phenotype". How does the authors define this concept? Periodontitis is a complex disease, despite that alveolar bone resorption is a typical manifestation of periodontitis, its characteristics remain to be further studied. I hope the authors can provide some detailed information about this concept or describe it in another way.

This is an important comment. Radiographically, human periodontitis is diagnosed by alveolar bone resorption from the cervical region, not from root apex. To highlight this, we present dental radiographs of human periodontitis as supplementary information. However, we agree with this comment, our statement should be limited to alveolar bone resorption pattern in Rag2KO and Rag2gcKO mice. Abstract be revised accordingly.

Introduction:<br /> It is recommended to simplify the first to third paragraphs, and briefly explain the functions of various types of cells in different stages of periodontitis, as well as the role of different cluster markers play across the time course of periodontal inflammation development.

Following this recommendation, INTRODUCTION has been simplified.

Results:<br /> 1. It is recommended to add HE staining and immunohistochemistry staining to observe the inflammation, tissue damage, and repair status from 0 to 7 days, so that readers can understand cell phenotype changes corresponding to the periodontitis stage. The observation index can include inflammation and vascular related indicators.

As recommended, representative histological figures were included. We further performed new immunohistochemistry experiment of mouse gingival tissue (D0, D1, D3, D7) highlighting the infiltration of CD45+ immune cells. We found that inflammatory vascular formation in the H&E histology, which was highlighted. To characterize the tissue damage, the histological sections were stained by picrosirius red to highlight the change in collagen connective tissue of PDL and gingiva.

1. Figure 1A-1D can be placed in the supplementary figure.

Combining the new data above, Figure 1 was revised as suggested.

1. I suggest the authors to put the detection of the existence of AG fibroblasts before exploring its relationship with other types of cells.

2. The layout of the picture should be closely related to the topic of the article. It is recommended to readjust the layout of the picture. Figure 1 should be the detection of AG cells and their proportion changes from 0 to 7 days. In other figures, the authors can separately describe the proportion changes of myeloid cells, T cells and ILCs, and explored the association between AG fibroblasts and these cell types.

As suggested, the presentation order of Figures and text was revised to bring the information about AG fibroblasts first. The chemokine-receptor analysis was moved below.

1. Please provide the complete form of "KT" in Line 162.

KT fibroblasts (fibroblasts keeping typical phenotype) was described in the text.

Methods:<br /> It is recommended to separately list the statistical methods section. The statistical method used in the article should be one-way ANOVA.

A separate statistical method section is created. As pointed out, we used one-way ANOVA with post-hoc Tukey test (when multiple groups were compared).

Discussion:<br /> I suggest the authors remove Figures 3-6 from the discussion section. For example, in Line 283, "(Figure 3 and 4)" should be removed.

Revised as suggested.

Reference:<br /> Some information for the references is missing. For example, "Lin P, et al. Application of Ligature-Induced Periodontitis in Mice to Explore the Molecular Mechanism of Periodontal Disease. Int J Mol Sci 22, (2021)" should be "Lin P, et al. Application of Ligature-Induced Periodontitis in Mice to Explore the Molecular Mechanism of Periodontal Disease. Int J Mol Sci 22, 8900 (2021)". It is necessary to recheck all references.

The reference has been checked for the accuracy and the omission pointed out was corrected. Although we used EndNote program, we found some more inaccuracy in the references that were manually corrected. We appreciate your suggestion.

Reviewer #2 (Recommendations For The Authors):

1. Many host cells participate in immune responses, such as gingival epithelial cells. AG fibroblast is not the only cell involved in the immune response, and the weight of its role needs to be clarified. So the expression in the conclusion should be appropriate.

Following this critique, we revised INTRODUCTION, DISCUSSION and CONCLUSION, to highlight how AG fibroblasts function within a comprehensive immune response network.

1. This study cannot directly answer the issue of the relationship between periodontitis and systemic diseases.

We agree with this critique. We either deleted or de-emphasized the relationship between periodontitis and systemic diseases throughout the text.

Author response

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

We thank the editor for the eLife assessment and reviewers for their remaining comments. We will address them in this response.

First, we thank eLife for the positive assessment. Regarding the point of visual acuity that is mentioned in this assessment, we understand that this comment is made. It is not an uncommon comment when rodent vision is discussed. However, we emphasize that we took the lower visual acuity of rats and the higher visual acuity of humans into account when designing the human study, by using a fast and eccentric stimulus presentation for humans. As a result, we do not expect a higher discriminability of stimuli in humans. We have described this in detail in our Methods section when describing the procedure in the human experiment:

“We used this fast and eccentric stimulus presentation with a mask to resemble the stimulus perception more closely to that of rats. Vermaercke & Op de Beeck (2012) have found that human visual acuity in these fast and eccentric presentations is not significantly better than the reported visual acuity of rats. By using this approach we avoid that differences in strategies between humans and rats would be explained by such a difference in acuity”

Second, regarding the remaining comment of Reviewer #2 about our use of AlexNet:

While it is indeed relevant to further look into different computational architectures, we chose to not do this within the current study. First, it is a central characteristic of the study procedure that the computational approach and chosen network is chosen early on as it is used to generate the experimental design that animals are tested with. We cannot decide after data collection to use a different network to select the stimuli with which these data were collected. Second, as mentioned in our first response, using AlexNet is not a random choice. It has been used in many previously published vision studies that were relatively positive about the correspondence with biological vision (Cadieu et al., 2014; Groen et al., 2018; Kalfas et al., 2018; Nayebi et al., 2023; Zeman et al., 2020). Third, our aim was not to find a best DNN model for rat vision, but instead examining the visual features that play a role in our complex discrimination task with a model that was hopefully a good enough starting point. The fact that the designs based upon AlexNet resulted in differential and interpretable effects in rats as well as in humans suggests that this computational model was a good start. Comparing the outcomes of different networks would be an interesting next step, and we expect that our approach could work even better when using a network that is more specifically tailored to mimic rat visual processing.

Finally, regarding the choice to specifically chose alignment and concavity as baseline properties, this choice is probably not crucial for the current study. We have no reason to expect rats to have an explicit notion about how a shape is built up in terms of a part-based structure, where alignment relates to the relative position of the parts and concavity is a property of the main base. For human vision it might be different, but we did not focus on such questions in this study.

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

We would like to thank you for giving us the opportunity to submit a revised draft our manuscript. We appreciate the time and effort that you dedicated to providing insightful feedback on our manuscript and are grateful for the valuable comments and improvements on our paper. It helped us to improve our manuscript. We have carefully considered the comments and tried our best to address every one of them. We have added clarifications in the Discussion concerning the type of neural network that we used, about which visual features might play a role in our results as well as clarified the experimental setup and protocol in the Methods section as these two sections were lacking key information points.

Below we provide a response to the public comments and concerns of the reviewers.

Several key points were addressed by at least two reviewers, and we will respond to them first.

A first point concerns the type of network we used. In our study, we used AlexNet to simulate the ventral visual stream and to further examine rat and human performance. While other, more complex neural networks might lead to other results, we chose to work with AlexNet because it has been used in many other vision studies that are published in high impact journals ((Cadieu et al., 2014; Groen et al., 2018; Kalfas et al., 2018; Nayebi et al., 2023; Zeman et al., 2020). We did not try to find a best DNN model for rat vision but instead, we were looking for an explanation of which visual features play a role in our complex discrimination task. We added a consideration to our Discussion addressing why we worked with AlexNet. Since our data will be published on OSF, we encourage to researchers to use our data with other, more complex neural networks and to further investigate this issue.

A second point that was addressed by multiple reviewers concerns the visual acuity of the animals and its impact on their performance. The position of the rat was not monitored in the setup. In a previous study in our lab (Crijns & Op de Beeck, 2019), we investigated the visual acuity of rats in the touchscreen setups by presenting gratings with different cycles per screen to see how it affects their performance in orientation discrimination. With the results from this study and general knowledge about rat visual acuity, we derived that the decision distance of rats lies around 12.5cm from the screen. We have added this paragraph to the Discussion.

A third key point that needs to be addressed as a general point involves which visual features could explain rat and human performance. We reported marked differences between rat and human data in how performance varied across image trials, and we concluded through our computationally informed tests and analyses that rat performance was explained better by lower levels of processing. Yet, we did not investigate which exact features might underlie rat performance. As a starter, we have focused on taking a closer look at pixel similarity and brightness and calculating the correlation between rat/human performance and these two visual features.

We calculated the correlation between the rat performances and image brightness of the transformations. We did this by calculating the difference in brightness of the base pair (brightness base target – brightness base distractor), and subtracting the difference in brightness of every test target-distractor pair for each test protocol (brightness test target – brightness test distractor for each test pair). We then correlated these 287 brightness values (1 for each test image pair) with the average rat performance for each test image pair. This resulted in a correlation of 0.39, suggesting that there is an influence of brightness in the test protocols. If we perform the same correlation with the human performances, we get a correlation of -0.12, suggesting a negative influence of brightness in the human study.

We calculated the correlation between pixel similarity of the test stimuli in relation to the base stimuli with the average performance of the animals on all nine test protocols. We did this by calculating the pixel similarity between the base target with every other testing distractor (A), the pixel similarity between the base target with every other testing target (B), the pixel similarity between the base distractor with every other testing distractor (C) and the pixel similarity between the base distractor with every other testing target (D). For each test image pair, we then calculated the average of (A) and (D), and subtracted the average of (C) and (B) from it. We correlated these 287 values (one for each image pair) with the average rat performance on all test image pairs, which resulted in a correlation of 0.34, suggesting an influence of pixel similarity in rat behaviour. Performing the same correlation analysis with the human performances results in a correlation of 0.12.

We have also addressed this in the Discussion of the revised manuscript. Note that the reliability of the rat data was 0.58, clearly higher than the correlations with brightness and pixel similarity, thus these features capture only part of the strategies used by rats.

We have also responded to all other insightful suggestions and comments of the reviewers, and a point-by-point response to the more major comments will follow now.  

Reviewer #1, general comments:

The authors should also discuss the potential reason for the human-rat differences too, and importantly discuss whether these differences are coming from the rather unusual approach of training used in rats (i.e. to identify one item among a single pair of images), or perhaps due to the visual differences in the stimuli used (what were the image sizes used in rats and humans?). Can they address whether rats trained on more generic visual tasks (e.g. same-different, or category matching tasks) would show similar performance as humans?

The task that we used is typically referred to as a two-alternative forced choice (2AFC). This is a simple task to learn. A same-different task is cognitively much more demanding, also for artificial neural networks (see e.g. Puebla & Bowers, 2022, J. Vision). A one-stimulus choice task (probably what the reviewer refers to with category matching) is known to be more difficult compared to 2AFC, with a sensitivity that is predicted to be Sqrt(2) lower according to signal detection theory (MacMillan & Creelman, 1991). We confirmed this prediction empirically in our lab (unpublished observations). Thus, we predict that rats perform less good in the suggested alternatives, potentially even (in case of same-different) resulting in a wider performance gap with humans.

I also found that a lot of essential information is not conveyed clearly in the manuscript. Perhaps it is there in earlier studies but it is very tedious for a reader to go back to some other studies to understand this one. For instance, the exact number of image pairs used for training and testing for rats and humans was either missing or hard to find out. The task used on rats was also extremely difficult to understand. An image of the experimental setup or a timeline graphic showing the entire trial with screenshots would have helped greatly.

All the image pairs used for training and testing for rats and humans are depicted in Figure 1 (for rats) and Supplemental Figure 6 (for humans). For the first training protocol (Training), only one image pair was shown, with the target being the concave object with horizontal alignment of the spheres. For the second training protocol (Dimension learning), three image pairs were shown, consisting of the base pair, a pair which differs only in concavity, and a pair which differs only in alignment. For the third training protocol (Transformations) and all testing protocols, all combination of targets and distractors were presented. For example, in the Rotation X protocol, the stimuli consisted of 6 targets and 6 distractors, resulting in a total of 36 image pairs for this protocol. The task used on rats is exactly as shown in Figure 1. A trial started with two blank screens. Once the animal initiated a trial by sticking its head in the reward tray, one stimulus was presented on each screen. There was no time limit and so the stimuli remained on the screen until the animal made a decision. If the animal touched the target, it received a sugar pellet as reward and a ITI of 20s started. If the animal touched the distractor, it did not receive a sugar pellet and a time-out of 5s started in addition to the 20s ITI.

We have clarified this in the manuscript.

The authors state that the rats received random reward on 80% of the trials, but is that on 80% of the correctly responded trials or on 80% of trials regardless of the correctness of the response? If these are free choice experiments, then the task demands are quite different. This needs to be clarified. Similarly, the authors mention that 1/3 of the trials in a given test block contained the old base pair - are these included in the accuracy calculations?

The animals receive random reward on 80% on all testing trials with new stimuli, regardless of the correctness of the response. This was done to ensure that we can measure true generalization based upon learning in the training phase, and that the animals do not learn/are not trained in these testing stimuli. For the trials with the old stimuli (base pair), the animals always received real reward (reward when correct; no reward in case of error).

The 1/3rd trials with old stimuli are not included in the accuracy calculations but were used as a quality check/control to investigate which sessions have to be excluded and to assure that the rats were still doing the task properly. We have added this in the manuscript.

The authors were injecting noise with stimuli to cDNN to match its accuracy to rat. However, that noise potentially can interacted with the signal in cDNN and further influence the results. That could generate hidden confound in the results. Can they acknowledge/discuss this possibility?

Yes, adding noise can potentially interact with the signal and further influence the results. Without noise, the average training data of the network would lie around 100% which would be unrealistic, given the performances of the animals. To match the training performance of the neural networks with that of the rats, we added noise 100 times and averaged over these iterations (cfr. (Schnell et al., 2023; Vinken & Op de Beeck, 2021)).  

Reviewer #2, weaknesses:

1) There are a few inconsistencies in the number of subjects reported. Sometimes 45 humans are mentioned and sometimes 50. Probably they are just typos, but it's unclear.

Thank you for your feedback. We have doublechecked this and changed the number of subjects where necessary. We collected data from 50 human participants, but had to exclude 5 of them due to low performance during the quality check (Dimension learning) protocols. Similarly, we collected data from 12 rats but had to exclude one animal because of health issues. All these data exclusion steps were mentioned in the Methods section of the original version of the manuscript, but the subject numbers were not always properly adjusted in the description in the Results section. This is now corrected.

2) A few aspects mentioned in the introduction and results are only defined in the Methods thus making the manuscript a bit hard to follow (e.g. the alignment dimension), thus I had to jump often from the main text to the methods to get a sense of their meaning.

Thank you for your feedback. We have clarified some aspects in the Introduction, such as the alignment dimension.

4) Many important aspects of the task are not fully described in the Methods (e.g. size of the stimuli, reaction times and basic statistics on the responses).

We have added the size of the stimuli to the Methods section and clarified that the stimuli remained on the screen until the animals made a choice. Reaction time in our task would not be interpretable given that stimuli come on the screen when the animal initiates a trial with its back to the screen. Therefore we do not have this kind of information.

Reviewer #1

• Can the authors show all the high vs zero and zero vs high stimulus pairs either in the main or supplementary figures? It would be instructive to know if some other simple property covaried between these two sets.

In Figure 1, all images of all protocols are shown. For the High vs. Zero and Zero vs. High protocols, we used a deep neural network to select a total of 7 targets and 7 distractors. This results in 49 image pairs (every combination of target-distractor).

• Are there individual differences across animals? It would be useful for the authors to show individual accuracy for each animal where possible.

We now added individual rat data for all test protocols – 1 colour per rat, black circle = average. We have added this picture to the Supplementary material (Supplementary Figure 1).

• Figure 1 - it was not truly clear to me how many image pairs were used in the actual experiment. Also, it was very confusing to me what was the target for the test trials. Additionally, authors reported their task as a categorisation task, but it is a discrimination task.

Figure 1 shows all the images that were used in this study. Every combination of every target-distractor in each protocol (except for Dimension learning) was presented to the animals. For example in Rotation X, the test stimuli as shown in Fig. 1 consisted of 6 targets and 6 distractors, resulting in a total of 36 image pairs for this test protocol.

In each test protocol, the target corresponded to the concave object with horizontally attached spheres, or the object from the pair that in the stimulus space was closed to this object. We have added this clarification in the Introduction: “We started by training the animals in a base stimulus pair, with the target being the concave object with horizontally aligned spheres. Once the animals were trained in this base stimulus pair, we used the identity-preserving transformations to test for generalization.” as well as in the caption of Figure 1. We have changed the term “categorisation task” to “discrimination task” throughout the manuscript.

• Figure 2 - what are the red and black lines? How many new pairs are being tested here? Panel labels are missing (a/b/c etc)

We have changed this figure by adding panel labels, and clarifying the missing information in the caption. All images that were shown to the animals are presented on this figure. For Dimension Learning, only three image pairs were shown (base pair, concavity pair, alignment pair) and for the Transformations protocol, every combination of every target and distractor were shown, i.e. 25 image pairs in total.

• Figure 3 - last panel: the 1st and 2nd distractor look identical.

We understand your concern as these two distractors indeed look quite similar. They are different however in terms of how they are rotated along the x, y and z axes (see Author response image 1 for a bigger image of these two distractors). The similarity is due to the existence of near-symmetry in the object shape which causes high self-similarity for some large rotations.

Author response image 1.

• Line 542 – authors say they have ‘concatenated’ the performance of the animals, but do they mean they are taking the average across animals?

It is both. In this specific analysis we calculated the performance of the animals, which was indeed averaged across animals, per test protocol, per stimulus pair. This resulted in 9 arrays (one for each test protocol) of several performances (1 for each stimulus pair). These 9 arrays were concatenated by linking them together in one big array (i.e. placing them one after the other). We did the same concatenation with the distance to hyperplane of the network on all nine test protocols. These two concatenated arrays with 287 values each (one with the animal performance and one with the DNN performance) were correlated.

• Line 164 - What are these 287 image pairs - this is not clear.

The 287 image pairs correspond to all image pairs of all 9 test protocols: 36 (Rotation X) + 36 (Rotation Y) + 36 (Rotation Z) + 4 (Size) + 25 (Position) + 16 (Light location) + 36 (Combination Rotation) + 49 (Zero vs. high) + 49 (High vs. zero) = 287 image pairs in total. We have clarified this in the manuscript.

• Line 215 - Human rat correlation (0.18) was comparable to the best cDNN layer correlation. What does this mean?

The human rat correlation (0.18) was closest to the best cDNN layer - rat correlation (about 0.15). In the manuscript we emphasize that rat performance is not well captured by individual cDNN layers.  

Reviewer #2

Major comments

• In l.23 (and in the methods) the authors mention 50 humans, but in l.87 they are 45. Also, both in l.95 and in the Methods the authors mention "twelve animals" but they wrote 11 elsewhere (e.g. abstract and first paragraph of the results).

In our human study design, we introduced several Dimension learning protocols. These were later used as a quality check to indicate which participants were outliers, using outlier detection in R. This resulted in 5 outlying human participants, and thus we ended with a pool of 45 human participants that were included in the analyses. This information was given in the Methods section of the original manuscript, but we did not mention the correct numbers everywhere. We have corrected this in the manuscript. We also changed the number of participants (humans and rats) to the correct one throughout the entire manuscript.

• At l.95 when I first met the "4x4 stimulus grid" I had to guess its meaning. It would be really useful to see the stimulus grid as a panel in Figure 1 (in general Figures S1 and S4 could be integrated as panels of Figure 1). Also, even if the description of the stimulus generation in the Methods is probably clear enough, the authors might want to consider adding a simple schematic in Figure 1 as well (e.g. show the base, either concave or convex, and then how the 3 spheres are added to control alignment).

We have added the 4x4 stimulus grid in the main text.

• There is also another important point related to the choice of the network. As I wrote, I find the overall approach very interesting and powerful, but I'm actually worried that AlexNet might not be a good choice. I have experience trying to model neuronal responses from IT in monkeys, and there even the higher layers of AlexNet aren't that helpful. I need to use much deeper networks (e.g. ResNet or GoogleNet) to get decent fits. So I'm afraid that what is deemed as "high" in AlexNet might not be as high as the authors think. It would be helpful, as a sanity check, to see if the authors get the same sort of stimulus categories when using a different, deeper network.

We added a consideration to the manuscript about which network to use (see the Discussion): “We chose to work with Alexnet, as this is a network that has been used as a benchmark in many previous studies (e.g. (Cadieu et al., 2014; Groen et al., 2018; Kalfas et al., 2018; Nayebi et al., 2023; Zeman et al., 2020)), including studies that used more complex stimuli than the stimulus space in our current study. […] . It is in line with the literature that a typical deep neural network, AlexNet and also more complex ones, can explain human and animal behaviour to a certain extent but not fully. The explained variance might differ among DNNs, and there might be DNNs that can explain a higher proportion of rat or human behaviour. Most relevant for our current study is that DNNs tend to agree in terms of how representations change from lower to higher hierarchical layers, because this is the transformation that we have targeted in the Zero vs. high and High vs. zero testing protocols. (Pinto et al., 2008) already revealed that a simple V1-like model can sometimes result in surprisingly good object recognition performance. This aspect of our findings is also in line with the observation of Vinken & Op de Beeck (2021) that the performance of rats in many previous tasks might not be indicative of highly complex representations. Nevertheless, there is still a relative difference in complexity between lower and higher levels in the hierarchy. That is what we capitalize upon with the Zero vs. high and High vs. zero protocols. Thus, it might be more fruitful to explicitly contrast different levels of processing in a relative way rather than trying to pinpoint behaviour to specific levels of processing.”

• The task description needs way more detail. For how long were the stimuli presented? What was their size? Were the positions of the stimuli randomized? Was it a reaction time task? Was the time-out used as a negative feedback? In case, when (e.g. mistakes or slow responses)? Also, it is important to report some statistics about the basic responses. What was the average response time, what was the performance of individual animals (over days)? Did they show any bias for a particular dimension (either the 2 baseline dimensions or the identity preserving ones) or side of response? Was there a correlation within animals between performance on the baseline task and performance on the more complex tasks?

Thank you for your feedback. We have added more details to the task description in the manuscript.

The stimuli were presented on the screens until the animals reacted to one of the two screens. The size of the stimuli was 100 x 100 pixel. The position of the stimuli was always centred/full screen on the touchscreens. It was not a reaction time task and we also did not measure reaction time.

• Related to my previous comment, I wonder if the relative size/position of the stimulus with respect to the position of the animal in the setup might have had an impact on the performance, also given the impact of size shown in Figure 2. Was the position of the rat in the setup monitored (e.g. with DeepLabCut)? I guess that on average any effect of the animal position might be averaged away, but was this actually checked and/or controlled for?

The position of the rat was not monitored in the setup. In a previous study from our lab (Crijns & Op de Beeck, 2019), we investigated the visual acuity of rats in the touchscreen setups by presenting gratings with different cycles per screen to see how it affects their performance in orientation discrimination. With the results from this study and general knowledge about rat visual acuity, we derived that the decision distance of rats lies around 12.5cm from the screen. We have added this to the discussion.

Minor comments

• l.33 The sentence mentions humans, but the references are about monkeys. I believe that this concept is universal enough not to require any citation to support it.

Thank you for your feedback. We have removed the citations.

• This is very minor and totally negligible. The acronymous cDNN is not that common for convents (and it's kind of similar to cuDNN), it might help clarity to stick to a more popular acronymous, e.g. CNN or ANN. Also, given that the "high" layers used for stimulus selection where not convolutional layers after all (if I'm not mistaken).

Thank you for your feedback. We have changed the acronym to ‘CNN’ in the entire manuscript.

• In l.107-109 the authors identified a few potential biases in their stimuli, and they claim these biases cannot explain the results. However, the explanation is given only in the next pages. It might help to mention that before or to move that paragraph later, as I was just wondering about it until I finally got to the part on the brightness bias.

We expanded the analysis of these dimensions (e.g. brightness) throughout the manuscript.

• It would help a lot the readability to put also a label close to each dimension in Figures 2 and 3. I had to go and look at Figure S4 to figure that out.

Figures 2 and 3 have been updated, also including changes related to other comments.

• In Figure 2A, please specify what the red dashed line means.

We have edited the caption of Figure 2: “Figure 2 (a) Results of the Dimension learning training protocol. The black dashed horizontal line indicates chance level performance and the red dashed line represents the 80% performance threshold. The blue circles on top of each bar represent individual rat performances. The three bars represent the average performance of all animals on the old pair (Old), the pair that differs only in concavity (Conc) and on the pair that differs only in alignment (Align). (b) Results of the Transformations training protocol. Each cell of the matrix indicates the average performance per stimulus pair, pooled over all animals. The columns represent the distractors, whereas the rows separate the targets. The colour bar indicates the performance correct. ”

• Related to that, why performing a binomial test on 80%? It sounds arbitrary.

We performed the binomial test on 80% as 80% is our performance threshold for the animals

• The way the cDNN methods are introduced makes it sound like the authors actually fine-tuned the weights of AlexNet, while (if I'm not mistaken), they trained a classifier on the activations of a pre-trained AlexNet with frozen weights. It might be a bit confusing to readers. The rest of the paragraph instead is very clear and easy to follow.

We think the most confusing sentence was “ Figure 7 shows the performance of the network after training the network on our training stimuli for all test protocols. “ We changed this sentence to “ Figure 8 shows the performance of the network for each of the test protocols after training classifiers on the training stimuli using the different DNN layers.“

Reviewer #3

Main recommendations:

Although it may not fully explain the entire pattern of visual behavior, it is important to discuss rat visual acuity and its impact on the perception of visual features in the stimulus set.

We have added a paragraph to the Discussion that discusses the visual acuity of rats and its impact on perceiving the visual features of the stimuli.

The authors observed a potential influence of image brightness on behavior during the dimension learning protocol. Was there a correlation between image brightness and the subsequent image transformations?

We have added this to the Discussion: “To further investigate to which visual features the rat performance and human performance correlates best with, we calculated the correlation between rat performance and pixel similarity of the test image pairs, as well as the correlation between rat performance and brightness in the test image pairs. Here we found a correlation of 0.34 for pixel similarity and 0.39 for brightness, suggesting that these two visual features partly explain our results when compared to the full-set reliability of rat performance (0.58). If we perform the same correlation with the human performances, we get a correlation of 0.12 for pixel similarity and -0.12 for brightness. With the full-set reliability of 0.58 (rats) and 0.63 (humans) in mind, this suggests that even pixel similarity and brightness only partly explain the performances of rats and humans.”

Did the rats rely on consistent visual features to perform the tasks? I assume the split-half analysis was on data pooled across rats. What was the average correlation between rats? Were rats more internally consistent (split-half within rat) than consistent with other rats?

The split-half analysis was indeed performed on data pooled across rats. We checked whether rats are more internally consistent by comparing the split-half within correlations with the split-half between correlations. For the split-half within correlations, we split the data for each rat in two subsets and calculated the performance vectors (performance across all image pairs). We then calculated the correlation between these two vectors for each animal. To get the split-half between correlation, we calculated the correlation between the performance vector of every subset data of every rat with every other subset data from the other rats. Finally, we compared for each animal its split-half within correlation with the split-half between correlations involving that animal. The result of this paired t-test (p = 0.93, 95%CI [-0.09; 0.08]) suggests that rats were not internally more consistent.

Discussion of the cDNN performance and its relation to rat behavior could be expanded and clarified in several ways:

• The paper would benefit from further discussion regarding the low correlations between rat behavior and cDNN layers. Is the main message that cDNNs are not a suitable model for rat vision? Or can we conclude that the peak in mid layers indicates that rat behavior reflects mid-level visual processing? It would be valuable to explore what we currently know about the organization of the rat visual cortex and how applicable these models are to their visual system in terms of architecture and hierarchy.

We added a consideration to the manuscript about which network to use (see Discussion).

• The cDNN exhibited above chance performance in various early layers for several test protocols (e.g., rotations, light location, combination rotation). Does this limit the interpretation of the complexity of visual behavior required to perform these tasks?

This is not uncommon to find. Pinto et al. (2008) already revealed that a simple V1-like model can sometimes result in surprisingly good object recognition performance. This aspect of our findings is also in line with the observation of Vinken & Op de Beeck (2021) that the performance of rats in many previous tasks might not be indicative of highly complex representations. Nevertheless, there is still a relative difference in complexity between lower and higher levels in the hierarchy. That is what we capitalize upon with the High vs zero and the Zero vs high protocols. Thus, it might be more fruitful to explicitly contrast different levels of processing in a relative way rather than trying to pinpoint behavior to specific levels of processing. This argumentation is added to the Discussion section.

• How representative is the correlation profile between cDNN layers and behavior across protocols? Pooling stimuli across protocols may be necessary to obtain stable correlations due to relatively modest sample numbers. However, the authors could address how much each individual protocol influences the overall correlations in leave-one-out analyses. Are there protocols where rat behavior correlates more strongly with higher layers (e.g., when excluding zero vs. high)?

We prefer to base our conclusions mostly on the pooled analyses rather than individual protocols. As the reviewer also mentions, we can expect that the pooled analyses will provide the most stable results. For information, we included leave-one-out analyses in the supplemental material. Excluding the Zero vs. High protocol did not result in a stronger correlation with the higher layers. It was rare to see correlations with higher layers, and in the one case that we did (when excluding High versus zero) the correlations were still higher in several mid-level layers.

Author response image 2.

• The authors hypothesize that the cDNN results indicate that rats rely on visual features such as contrast. Can this link be established more firmly? e.g., what are the receptive fields in the layers that correlate with rat behavior sensitive to?

This hypothesis was made based on previous in-lab research ((Schnell et al., 2023) where we found rats indeed rely on contrast features. In this study, we performed a face categorization task, parameterized on contrast features, and we investigated to what extent rats use contrast features to perform in a face categorization task. Similarly as in the current study, we used a DNN that as trained and tested on the same stimuli as the animals to investigate the representations of the animals. There, we found that the animals use contrast features to some extent and that this correlated best with the lower layers of the network. Hence, we would say that the lower layers correlate best with rat behaviour that is sensitive to contrast. Earlier layers of the network include local filters that simulate V1-like receptive fields. Higher layers of the network, on the other hand, are used for object selectivity.

• There seems to be a disconnect between rat behavior and the selection of stimuli for the high (zero) vs. zero (high) protocols. Specifically, rat behavior correlated best with mid layers, whereas the image selection process relied on earlier layers. What is the interpretation when rat behavior correlates with higher layers than those used to select the stimuli?

We agree that it is difficult to pinpoint a particular level of processing, and it might be better to use relative terms: lower/higher than. This is addressed in the manuscript by the edit in response to three comments back.

• To what extent can we attribute the performance below the ceiling for many protocols to sensory/perceptual limitations as opposed to other factors such as task structure, motivation, or distractibility?

We agree that these factors play a role in the overall performance difference. In Figure 5, the most right bar shows the percentage of all animals (light blue) vs all humans (dark blue) on the old pair that was presented during the testing protocol. Even here, the performance of the animals was lower than humans, and this pattern extended to the testing protocols as well. This was most likely due to motivation and/or distractibility which we know can happen in both humans and rats but affects the rat results more with our methodology.

Minor recommendations:

• What was the trial-to-trial variability in the distance and position of the rat's head relative to the stimuli displayed on the screen? Can this variability be taken into account in the size and position protocols? How meaningful is the cDNN modelling of these protocols considering that the training and testing of the model does not incorporate this trial-to-trial variability?

We have no information on this trial-to-trial variability. We have information though on what rats typically do overall from an earlier paper that was mentioned in response to an earlier comment (Crijns et al.).

We have added a disclaimer in the Discussion on our lack of information on trial-to-trial variability.

• Several of the protocols varied a visual feature dimension (e.g., concavity & alignment) relative to the base pair. Did rat performance correlate with these manipulations? How did rat behavior relate to pixel dissimilarity, either between target and distractor or in relation to the trained base pair?

We have added this to the Discussion. See also our general comments in the Public responses.

• What could be the underlying factor(s) contributing to the difference in accuracy between the "small transformations" depicted in Figure 2 and some of the transformations displayed in Figure 3? In particular, it seems that the variability of targets and distractors is greater for the "small transformations" in Figure 2 compared to the rotation along the y-axis shown in Figure 3.

There are several differences between these protocols. Before considering the stimulus properties, we should take into account other factors. The Transformations protocol was a training protocol, meaning that the animals underwent several sessions in this protocol, always receiving real reward during the trials, and only stopping once a high enough performance was reached. For the protocols in Figure 3, the animals were also placed in these protocols for multiple sessions in order to obtain enough trials, however, the difference here is that they did not receive real reward and testing was also stopped if performance was still low.

• In Figure 3, it is unclear which pairwise transformation accuracies were above chance. It would be helpful if the authors could indicate significant cells with an asterisk. The scale for percentage correct is cut off at 50%. Were there any instances where the behaviors were below 50%? Specifically, did the rats consistently choose the wrong option for any of the pairs? It would be helpful to add "old pair", "concavity" and "alignment" to x-axis labels in Fig 2A .

We have added “old”, “conc” and “align” to the x-axis labels in Figure 2A.

• Considering the overall performance across protocols, it seems overstated to claim that the rats were able to "master the task."

When talking about “mastering the task”, we talk about the training protocols where we aimed that the animals would perform at 80% and not significantly less. We checked this throughout the testing protocols as well, where we also presented the old pair as quality control, and their performance was never significantly lower than our 80% performance threshold on this pair, suggesting that they mastered the task in which they were trained. To avoid discussion on semantics, we also rephrased “master the task” into “learn the task”.

• What are the criteria for the claim that the "animal model of choice for vision studies has become the rodent model"? It is likely that researchers in primate vision may hold a different viewpoint, and data such as yearly total publication counts might not align with this claim.

Primate vision is important for investigating complex visual aspects. With the advancements in experimental techniques for rodent vision, e.g. genetics and imaging techniques as well as behavioural tasks, the rodent model has become an important model as well. It is not necessarily an “either” or “or” question (primates or rodents), but more a complementary issue: using both primates and rodents to unravel the full picture of vision.

We have changed this part in the introduction to “Lately, the rodent model has become an important model in vision studies, motivated by the applicability of molecular and genetic tools rather than by the visual capabilities of rodents”.

• The correspondence between the list of layers in Supplementary Tables 8 and 9 and the layers shown in Figures 4 and 6 could be clarified.

We have clarified this in the caption of Figure 7

• The titles in Figures 4 and 6 could be updated from "DNN" to "cDNN" to ensure consistency with the rest of the manuscript.

Thank you for your feedback. We have changed the titles in Figures 4 and 6 such that they are consistent with the rest of the manuscript.

Author Response

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

eLife assessment

This valuable manuscript attempts to identify the brain regions and cell types involved in habituation to dark flash stimuli in larval zebrafish. Habituation being a form of learning widespread in the animal kingdom, the investigation of neural mechanisms underlying it is an important endeavor. The authors use a combination of behavioral analysis, neural activity imaging, and pharmacological manipulation to investigate brain-wide mechanisms of habituation. However, the data presented are incomplete and do not show a convincing causative link between pharmacological manipulations, neural activity patterns, and behavioral outcomes.

We thank the reviewers and editors for their careful reading and reviews of our work. We are grateful that they appreciate the value in our experimental approach and results. We acknowledge what we interpret as the major criticism, that in our original manuscript we focused too heavily on the hypothesized role of GABAergic neurons in driving habituation. This hypothesis will remain only indirectly supported until we can identify a GABAergic population of neurons that drives habituation. Therefore, we have revised our manuscript, decreasing the focus on GABA, and rather emphasizing the following three points:

1) By performing the first Ca2+ imaging experiments during dark flash habituation, we identify multiple distinct functional classes of neurons which have different adaptation profiles, including non-adapting and potentiating classes. These neurons are spread throughout the brain, indicating that habituation is a complex and distributed process.

2) By performing a pharmacological screen for dark flash habituation modifiers, we confirm habituation behaviour manifests from multiple distinct molecular mechanisms that independently modulate different behavioural outputs. We also implicate multiple novel pathways in habituation plasticity, some of which we have validated through dose-response studies.

3) By combining pharmacology and Ca2+ imaging, we did not observe a simple relationship between the behavioural effects of a drug treatment and functional alterations in neurons. This observation further supports our model that habituation is a multidimensional process, for which a simple circuit model will be insufficient.

We would like to point out that, in our opinion, there appears to be a factual error in the final sentence of the eLife assessment:

“However, the data presented are incomplete and do not show a convincing causative link between pharmacological manipulations, neural activity patterns, and behavioral outcomes”.

We believe that a “convincing causative link” between pharmacological manipulations and behavioural outcomes has been clearly demonstrated for PTX, Melatonin, Estradiol and Hexestrol through our dose response experiments. Similarly a link between pharmacology and neural activity patterns has also been directly demonstrated. As mentioned in (3), we acknowledge that our data linking neural activity and behaviour is more tenuous, as will be more explicitly reflected in our revised manuscript.

Nevertheless, we maintain that one of the primary strengths of our study is our attempt to integrate analyses that span the behavioural, pharmacological, and neural activity-levels.

In our revised manuscript, we have substantially altered the Abstract and Discussion, removed the Model figure (previously Figure 8), and changed the title from :

“Inhibition drives habituation of a larval zebrafish visual response”

to:

“Functional and pharmacological analyses of visual habituation learning in larval zebrafish”

Text changes from the initial version are visible as track changes in the word document: “LamireEtAl_2022_eLifeRevisions.docx”

Reviewer #1 (Public Review):

This manuscript addresses the important and understudied issue of circuit-level mechanisms supporting habituation, particularly in pursuit of the possible role of increases in the activity of inhibitory neurons in suppressing behavioral output during long-term habituation. The authors make use of many of the striking advantages of the larval zebrafish to perform whole brain, single neuronal calcium imaging during repeated sensory exposure, and high throughput screening of pharmacological agents in freely moving, habituating larvae. Notably, several blockers/antagonists of GABAA(C) receptors completely suppress habituation of the O-bend escape response to dark flashes, suggesting a key role for GABAergic transmission in this form of habituation. Other substances are identified that strikingly enhance habituation, including melatonin, although here the suggested mechanistic insight is less specific. To add to these findings, a number of functional clusters of neurons are identified in the larval brain that has divergent activity through habituation, with many clusters exhibiting suppression of different degrees, in line with adaptive filtration during habituation, and a single cluster that potentiates during habituation. Further assessment reveals that all of these clusters include GABAergic inhibitory neurons and excitatory neurons, so we cannot take away the simple interpretation that the potentiating cluster of neurons is inhibitory and therefore exerts an influence on the other adapting (depressing) clusters to produce habituation. Rather, a variety of interpretations remain in play.

Overall, there is great potential in the approach that has been used here to gain insight into circuit-level mechanisms of habituation. There are many experiments performed by the authors that cannot be achieved currently in other vertebrate systems, so the manuscript serves as a potential methodological platform that can be used to support a rich array of future work. While there are several key observations that one can take away from this manuscript, a clear interpretation of the role of GABAergic inhibitory neurons in habituation has not been established. This potential feature of habituation is emphasized throughout, particularly in the introduction and discussion sections, meaning that one is obliged as a reader to interrogate whether the results as they currently stand really do demonstrate a role for GABAergic inhibition in habituation. Currently, the key piece of evidence that may support this conclusion is that picrotoxin, which acts to block some classes of GABA receptors, prevents habituation. However, there are interpretations of this finding that do not specifically require a role for modified GABAergic inhibition. For instance, by lowering GABAergic inhibition, an overall increase in neural activity will occur within the brain, in this case below a level that could cause a seizure. That increase in activity may simply prevent learning by massively increasing neural noise and therefore either preventing synaptic plasticity or, more likely, causing indiscriminate synaptic strengthening and weakening that occludes information storage. Sensory processing itself could also be disrupted, for instance by altering the selectivity of receptive fields. Alternatively, it could be that the increase in neural activity produced by the blockade of inhibition simply drives more behavioral output, meaning that more excitatory synaptic adaptation is required to suppress that output. The authors propose two specific working models of the ways in which GABAergic inhibition could be implemented in habituation. An alternative model, in which GABAergic neurons are not themselves modified but act as a key intermediary between Hebbian assemblies of excitatory neurons that are modified to support memory and output neurons, is not explored. As yet, these or other models in which inhibition is not required for habituation, have not been fully tested.

This manuscript describes a really substantial body of work that provides evidence of functional clusters of neurons with divergent responses to repeated sensory input and an array of pharmacological agents that can influence the rate of a fundamentally important form of learning.

We thank the reviewer for their careful consideration of our work, and we agree that multiple models of how habituation occurs remain plausible. As discussed above and below in more detail, we have revised our manuscript to better reflect this. We hope the reviewer will agree that this has improved the manuscript.

Reviewer #2 (Public Review):

In this study, Lamire et al. use a calcium imaging approach, behavioural tests, and pharmacological manipulations to identify the molecular mechanisms behind visual habituation. Overall, the manuscript is well-written but difficult to follow at times. They show a valuable new drug screen paradigm to assess the impact of pharmacological compounds on the behaviour of larval zebrafish, the results are convincing, but the description of the work is sometimes confusing and lacking details.

We thank the reviewer for identifying areas where our description lacked details. We apologize for these omissions and have attempted to add relevant details as described below. We note that all of the analysis code is available online, though we appreciate that navigating and extracting data from these files is not straightforward.

The volumetric calcium imaging of habituation to dark flashes is valuable, but the mix of responses to visual cues that are not relevant to the dark flash escape, such as the slow increase back to baseline luminosity, lowers the clarity of the results. The link between the calcium imaging results and free-swimming behaviour is not especially convincing, however, that is a common issue of head-restrained imaging with larval zebrafish.

We agree with the reviewer that the design of our stimulus, and specifically the slow increase back to baseline luminosity, is perhaps confusing for the interpretation of some of the response profiles of neurons. We originally chose this stimulus type (rather than a square wave of 1s of darkness, for example) in order to better highlight the responses of the larvae to the onset of darkness (rather than the response to abruptly returning to full brightness). We therefore believe that the slow return to baseline is an important feature of the stimulus,, which better separates activity related to the fast offset from activity related to light onset. And since all of the foundational behavioural data (Randlett et al., Current Biology 2019), and pharmacological data, used this stimulus type, we did not change it for the Ca2+ imaging experiments. Our use of relatively slow nuclear-targeted GCaMP indicators also means that the temporal resolution of our imaging experiments is relatively poor, and therefore we felt that using a stimulus that highlighted light offset might be best.

We also fully acknowledge in the Results section that the behaviour of the head embedded fish is not the same as that of free-swimming fish, and that therefore establishing a direct link between these types of experiments is complicated. This is an unavoidable caveat in the head-embedded style experiments. To further emphasize this, we have also added a paragraph to the discussion where this is acknowledged explicitly.

“We also found that the same pharmacological treatments that result in strong alterations to habituation behaviour in freely swimming larvae ([fig:5]), resulted in relatively subtle and complex functional alterations in the circuit ([fig:6]). Making direct comparisons between freely-swimming behaviour and head-fixed Ca2+ imaging is always challenging due to the differences in behaviour observed in the two contexts, and therefore our failure to identify a clear logic in these experiments may have technical explanations that will require approaches to measure neural activity from unrestrained and freely-behaving animals to resolve . Alternatively, these results are again consistent with the idea that habituation is a multidimensional and perhaps highly non-linear phenomenon in the circuit, which cannot be captured by a simple model.”

The strong focus on GABA seems unwarranted based on the pharmacological results, as only Picrotoxinin gives clear results, but the other antagonists do not give a consistent results. On the other hand, the melatonin receptor agonists, and oestrogen receptor agonists give more consistent results, including more convincing dose effects.

We agree that our manuscript focused too strongly on GABA and have toned this down. We are currently performing genetic experiments aimed at identifying the Melatonin, Estrogen and GABA receptors that function during habituation, which we think will be necessary to move beyond pharmacology and the necessary caveats that such experiments bring.

The pharmacological manipulation of the habituation circuits mapped in the first part does not arrive at any satisfying conclusion, which is acknowledged by the authors. These results do reinforce the disconnect between the calcium imaging and the behavioural experiments and undercut somewhat the proposed circuit-level model.

We agree with this criticism and have toned down the focus on GABA specifically in the circuit, and have removed the speculative model previously in Figure 8.

Overall, the authors did identify interesting new molecular pathways that may be involved in habituation to dark flashes. Their screening approach, while not novel, will be a powerful way to interrogate other behavioural profiles. The authors identified circuit loci apparently involved in habituation to dark flashes, and the potentiation and no adaptation clusters have not been previously observed as far as I know.

The data will be useful to guide follow-up experiments by the community on the new pathway candidates that this screen has uncovered, including behaviours beyond dark flash habituation.

We again thank the reviewer for both their support of our approach, and in pointing out where our conclusions were not well supported by our data.

Reviewer #3 (Public Review):

To analyze the circuit mechanisms leading to the habituation of the O-bed responses upon repeated dark flashes (DFs), the authors performed 2-photon Ca2+ imaging in larvae expressing nuclear-targeted GCaMP7f pan-neuronally panning the majority of the midbrain, hindbrain, pretectum, and thalamus. They found that while the majority of neurons across the brain depress their responsiveness during habituation, a smaller population of neurons in the dorsal regions of the brain, including the torus longitudinalis, cerebellum, and dorsal hindbrain, showed the opposite pattern, suggesting that motor-related brain regions contain non-depressed signals, and therefore likely contribute to habituation plasticity.

Further analysis using affinity propagation clustering identified 12 clusters that differed both in their adaptation to repeated DFs, as well as the shape of their response to the DF.

Next by the pharmacological screening of 1953 small molecule compounds with known targets in conjunction with the high-throughput assay, they found that 176 compounds significantly altered some aspects of measured behavior. Among them, they sought to identify the compounds that 1) have minimal effects on the naive response to DFs, but strong effects during the training and/or memory retention periods, 2) have minimal effects on other aspects of behaviors, 3) show similar behavioral effects to other compounds tested in the same molecular pathway, and identified the GABAA/C Receptor antagonists Bicuculline, Amoxapine, and Picrotoxinin (PTX). As partial antagonism of GABAAR and/or GABACR is sufficient to strongly suppress habituation but not generalized behavioral excitability, they concluded that GABA plays a very prominent role in habituation. They also identified multiple agonists of both Melatonin and Estrogen receptors, indicating that hormonal signaling may also play a prominent role in habituation response.

To integrate the results of the Ca2+ imaging experiments with the pharmacological screening results, the authors compared the Ca2+ activity patterns after treatment with vehicle, PTX, or Melatonin in the tethered larvae. The behavioral effects of PTX and Melatonin were much smaller compared with the very strong behavioral effects in freely-swimming animals, but the authors assumed that the difference was significant enough to continue further experiments. Based on the hypothesis that Melatonin and GABA cooperate during habituation, they expected PTX and Melatonin to have opposite effects. This was not the case in their results: for example, the size of the 12(Pot, M) neuron population was increased by both PTX and Melatonin, suggesting that pharmacological manipulations that affect habituation behavior manifest in complex functional alterations in the circuit, making capturing these effects by a simple difficult.

Since the 12(𝑃𝑜𝑡, 𝑀) neurons potentiate their responses and thus could act to progressively depress the responses of other neuronal classes, they examined the identity of these neurons with GABA neurons. However, GABAergic neurons in the habituating circuit are not characterized by their Adaptation Profile, suggesting that global manipulations of GABAergic signaling through PTX have complex manifestations in the functional properties of neurons.

Overall, the authors have performed an admirably large amount of work both in whole-brain neural activity imaging and pharmacological screening. However, they are not successful in integrating the results of both experiments into an acceptably consistent interpretation due to the incongruency of the results of different experiments. Although the authors present some models for interpretation, it is not easy for me to believe that this model would help the readers of this journal to deepen the understanding of the mechanisms for habituation in DF responses at the neural circuit level.

This reviewer would rather recommend the authors divide this manuscript into two and publish two papers by adding some more strengthening data for each part such as cellular manipulations, e.g. ablation to prove the critical involvement of 12(Pot, M) neurons in habituation.

We thank the reviewer for their careful consideration of our manuscript, and we agree that our emphasis on a particular model of DF habituation, namely the potentiation of GABAergic synapses, was overly speculative. We hope they will agree that our revised manuscript better reflect the results from our experiments, and we have tried to more specifically emphasize the incongruency in our behavioural and Ca2+ imaging data after pharmacological treatment, which we agree shows that a simple model is insufficient to capture both of these sets of observations.

We have opted not to split the paper into two, since we feel that the collective message of this paper and approach combining molecular and functional analysis will be of interest. Moreover, we feel that the molecular and functional analyses feed off of each other and provide a level of complementarity that would be lost if the manuscript would be split, even if the message in this particular case is rather complex

Reviewer #1 (Recommendations For The Authors):

There is much to commend about this manuscript. The advantages of studying habituation in the zebrafish larva are very clearly demonstrated, including the wonderful calcium imaging across the brain and the relatively high throughput screening of large numbers of different pharmacological agents. The habituation to dark flashes in freely moving larvae is also striking and the very large effect size serves the screening beautifully. Thus, if we take the really substantial amount of work of a very high standard that has been done here, there is clearly potential for an important new contribution to the literature. However, as you will see from my public review, I am of the opinion that a specific role for the modification of GABAergic inhibitory systems has not yet been established through this work. While the potential role for GABAergic inhibitory neurons in habituation, either as the key modifiable element or as an intermediary between memory and motor output, is an attractive theory with many strengths, your study as it currently stands does not categorically demonstrate that one of those two options holds. For instance, the more traditional view, that adaptive filtration is mediated by weakened synaptic connectivity between excitatory sensory systems and excitatory motor output or reduced intrinsic excitability in those same neurons, could still be in operation here. By lowering GABAergic influence over post-synaptic targets with picrotoxin, it is possible that motor output remains highly active, and even lower activity or synaptic drive from those excitatory sensory systems that feed into the output may still reliably produce behavioral output. Alternatively, it could be the formation of a memory of the familiar stimulus is disrupted by reduced inhibition that alters sensory coding either by introducing noise or reducing the selectivity of receptive fields. I believe that there are several options to address these concerns:

1) You could change the emphasis of the manuscript so that it is less focused on inhibition and instead emphasizes the categorization of clusters of neurons that have divergent responses during habituation, including either strong suppression to potentiation. To this, you add a high throughput screening system with a wide range of different agents being tested, several of which produce a significant effect on habituation in either direction. These observations in themselves provide powerful building blocks for future work.

2) If GABAergic neurons play a key role in habituation in this paradigm, then picrotoxin is having its effect by blocking receptors on excitatory neurons. Thus, it seems that selectively imaging GABAergic neurons before and after the application of these drugs is not likely to reveal the contribution of GABAergic synaptic influence on excitatory targets. More important is to get a stronger sense of how the GABAergic neurons change their activity throughout habituation and then influence the downstream target neurons of those GABAergic neurons (some of which may themselves be inhibitory and participating in disinhibition). For instance, you could interrogate whether anti-correlations in activity levels exist between presynaptic inhibitory neurons and putative post-synaptic targets. This analysis could be further bolstered by removing that relationship in the presence of Picrotoxin, thereby demonstrating a direct influence of inhibition from a GABAergic presynaptic partner on a postsynaptic target. While this would constitute a lot more work, it is likely to yield greater insight into a specific role for GABAergic neurons in habituation, and I suspect much of that information is in the existing datasets.

3) To really reveal causal roles for inhibition in this form of habituation, it seems to me that there needs to be some selective intervention in GABAergic neuronal activity, ideally bidirectionally, to transiently interrupt or enhance habituation. Optogenetic or chemogenetic stimulation/inactivation is one option in this regard, which I imagine would be challenging to implement and certainly involves a lot of further work, particularly if you are then going to target specific subpopulations of GABAergic neurons. I appreciate that this option seems way beyond the scope of a review process and would probably constitute a follow-up study.

We agree with the reviewer that we have not “categorically demonstrated” that GABAergic inhibitory neurons drive habituation by increasing their influence on the circuit, and appreciate the suggestions for how to reformulate our manuscript to better reflect this. We have opted to follow suggestion (1), and have considerably changed the focus of the manuscript.

The additional analysis suggested in (2) is very interesting, but since we can not identify which cells are inhibitory in our imaging experiments with picrotoxinin treatment, nor which are pre- or post-synaptic, we feel that this analysis will be very unconstrained. Also, if GABA is acting as an inhibitory neurotransmitter, it therefore is expected to act to drive anticorrelations among pre and postsynaptic neurons through inhibition. Therefore, blockage of GABA through PTX would be expected to result in increased correlations, regardless of our hypothesized role of neurons during habituation. Our current efforts are aimed at identifying critical neurons driving habituation plasticity, and we will perform such analysis once we have mechanisms for identifying these neurons.

Finally, we agree that (3) is the obvious and only way to demonstrate causation here, and this is where we are working towards. However, since we currently have no means of genetically targeting these neurons, we are not able to perform these suggested experiments today.

I have some additional concerns that I would really appreciate you addressing:

1) The behavioral habituation is striking in the freely moving larvae, but very hard to monitor in the larvae that are immobilized for calcium imaging. Are there steps that could be taken in the long run to improve direct observation of the habituation effect in these semi-stationary fish? For instance, is it possible to observe eye movements or some more subtle behavioral readout than the O-bend reflex? I apologize if this is a naïve question, but I am not entirely familiar with this specific experimental paradigm.

In the Dark Flash paradigm, we do not have readouts beyond the “O-bend” response itself, which is characterized by a large-angle bend of the tail and turning maneuver. We have not observed other, more subtle behavioural responses, such as eye or fin movements, for example. If we would be able to identify alternative behavioural outputs that were more robustly performed during head-embedded preparations, this would indeed be an advantage allowing us to more directly interpret the Ca2+ imaging results with respect to behaviour.

2) The dark flash as a stimulus to which the larvae habituate is obviously used as a powerful and ethologically relevant stimulus. However, it does leave an element of traditional habituation paradigms out, which is a novel stimulus that can be used to immediately re-instate the habituated response (otherwise known as dishabituation). Is there a way that you can imagine implementing that with zebrafish larvae, for instance through systematically altering a visual feature, such as spatial frequency or orientation? This would be a powerful development in my view as it would not only allow you to rule out motor or sensory fatigue as an underlying cause of reduced behavior but also it would provide an extra feature that strengthens your assessment of neuronal response profiles in candidate populations of inhibitory and excitatory neurons.

We agree that identifying a dishabituating stimulus would be very powerful for our experiments. For short-term habituation of the acoustic startle response, Wolman et al demonstrated that dishabituation occurs after a touch stimulus (Wolman et al., PNAS, 2011; https://doi.org/10.1073/pnas.1107156108). We attempted to dishabituate the O-Bend response with tap and touch stimuli, and this unfortunately did not occur. Our understanding of dishabituation is that this generally requires a second stimulus that elicits the same behaviour as the habituated stimulus (e.g. both acoustic and touch-stimuli elicit the Mauthner-dependent C-bend response). In zebrafish the only stimulus that has been identified that elicits the O-bend is a dark-flash. This lack of an appropriate alternative stimulus is perhaps why we have been unsuccessful in identifying a dishabituating stimulus.

3) You have written about the concept of 'short' and 'long' response shapes when using calcium imaging as a proxy for neural activity, surmising that the short response shape may reflect transient bursting. Although calcium imaging obviously has many advantages, this feature reveals one notable limitation of calcium imaging in contrast to electrophysiology, in that the time course of the signal is considerably longer and does not allow you with confidence to fully detect the response profile of neurons. Is there some kind of further deconvolution process that you could implement to improve the fidelity of your calcium imaging to the occurrence of action potentials? The burstiness of neurons is obviously important as it can indicate a particular type of neuron (for instance fast-spiking inhibitory neurons) or it might reveal a changing influence on post-synaptic neurons. For instance, bursting can be a response to inhibition due to the triggering of T-type calcium channels in response to hyperpolarization.

One of the major limitations to Ca2+ imaging is the lack of temporal resolution. In our particular approach, using nuclear-targeted H2B-GCaMP indicators, further reduces our temporal resolution. Deconvolution approaches can be used in some instances to approximate spike rate, since the rise-time of Ca2+ indicators can be relatively fast. However, in our imaging we chose to image larger volumes at the expense of scan rate, where our imaging is performed at only 2hz. Therefore, deconvolution and spike-rate estimation is not appropriate. Considering these limitations, we would argue that the fact that we can observe differences in kinetics of the 'short' and 'long' response shapes indicates that they likely show very different response kinetics, which we hope to confirm by electrophysiology once we have established ways of targeting these neurons for recordings.

4) I note that among the many substances you screened with is MK801. An obvious candidate mechanism in habituation is the NMDA receptor, given the importance of this receptor for so many forms of learning and bidirectional synaptic plasticity. If I am to understand correctly, this NMDA receptor blocker actually enhances habituation in the zebrafish larvae, similar to melatonin. That is a very surprising observation, which is worth looking into further or at least discussed in the manuscript. The finding would, at least, be consistent with the idea that plasticity is not occurring at excitatory synapses and could potentially bolster the argument that plasticity of inhibitory synapses is at play in this particular form of habituation.

This is a very important point. We were also particularly interested in MK801, which has been shown to inhibit other forms of habituation, like short-term acoustic habituation (Wolman et al., PNAS, 2011; https://doi.org/10.1073/pnas.1107156108). In our experiments we did see that fish become even less responsive to dark flashes when treated with MK-801 (SSMD fingerprint data: Prob-Train = -0.39, Prob-Test = -1.58) which would indicate that MK-801 promotes dark flash habituation, similar to Melatonin. However, we also observed that MK-801 caused a decrease in the performance in the other visual assay we tested: the optomotor response (OMR-Perf = -0.93), indicating that MK-801 causes a generalized decrease in visual responses, perhaps by acting on circuits within the retina. Therefore, based on these experiments with global drug applications, we cannot determine if MK-801 influences the plasticity process in dark-flash habituation, and this is why we did not pursue it further in this project.

Anyway, I hope that you take these suggestions as constructive and, in the spirit that they are intended, as possible routes for improving an already very interesting manuscript.

We are very grateful for your suggestions, which we feel has helped us to improve our manuscript substantially.

Reviewer #2 (Recommendations For The Authors):

Overall, the manuscript is well-written, but confusing at times. The results are not always presented in a consistent way, and I found myself having to dig in the raw data or code to find answers. There is a certain disconnect between the free-swimming results, and the calcium imaging, which is somewhat inevitable based on other published work. But I am unsure of what they each bring to the other, as the results from Fig.6 do not match at all the changes observed in the behavioural assays, it almost feels like two separate studies and the inconsistencies make the model appear unlikely.

We agree that there is a disconnect at the behavioural level in our free-swimming and head-embedded imaging experiments. However, this does not necessarily mean that the activity we observe during the imaging experiments cannot be informative about processes that are also occurring in freely-swimming fish. For example, it is possible that the dark-flash circuit is responding and habitating similarly in the head-embedded and freely-swimming preparations, but that in the latter context there is an additional blockade on motor output that massively decreases the propensity of the fish to initiate any movements. In such a case, the “disconnect between the free-swimming results, and the calcium imaging” would indicate that the relationship between neural activity and habituation behaviour is rather complex.

Without a method to record activity from freely swimming fish at our disposal, we can not determine this, one way or the other.

We hope that we now acknowledge these concerns appropriately in the discussion:

“We also found that the same pharmacological treatments that result in strong alterations to habituation behaviour in freely swimming larvae ([fig:5]), resulted in relatively subtle and complex functional alterations in the circuit ([fig:6]). Making direct comparisons between freely-swimming behaviour and head-fixed Ca2+ imaging is always challenging due to the differences in behaviour observed in the two contexts, and therefore our failure to identify a clear logic in these experiments may have technical explanations that will require approaches to measure neural activity from unrestrained and freely-behaving animals to resolve . Alternatively, these results are again consistent with the idea that habituation is a multidimensional and perhaps highly non-linear phenomenon in the circuit, which cannot be captured by a simple model. “

I am not convinced by the results surrounding GABA, from the inconsistent GABA receptor antagonist profile to the post hoc identification of GABAergic neurons as it is currently done in the manuscript. I think that the current focus on GABA does a disservice to the manuscript. However, the novel findings surrounding the potential role of Melatonin, and Estrogen, in habituation are quite interesting.

We agree that we focused too heavily on our hypothesized role for GABA in our original manuscript, and we hope that the reviewer agrees that our updated manuscript is an improvement. We also thank the reviewer for their interest in our Melatonin and Estrogen results, for which follow up studies are ongoing to characterize the effects of these hormones and their receptors on habituation.

There is an assumption that all the adaptation profiles are related to the DF (although that is somewhat alleviated in the discussions of the ON responses) and not to the luminosity changes. But there is no easy way to deconvolve those two in the current experiments. I would like the timing of the fluorescence rise to be quantified compared to the dark flash stimulus onset, potentially spike inference methods could help with giving a better idea of the timing of those responses. Based on the behavioural responses that were <500ms in Randlet O et al, eLife, 2019; we would expect only the fastest DF responses to be linked to the behaviour.

We agree that we are unable to disambiguate responses to the dark flash that initiate the O-bend response, and those that are related to only changes in luminosity. As discussed above, our Ca2+ imaging approach is severely limited in temporal resolution and therefore spike inference methods are not appropriate.

Major comments

Fig.1: There seems to be a very variable lag between the motor events and DF responses, furthermore, it does not seem that the motor responses follow a similar habituation rate as in 1Bi. Although this only shows the smoothed 'movement cluster' from the rastermap, it could hide individual variability. It would be important to know what the 'escape' rate was in the embedded experiment, as

Fig.1 sup.1 seems to indicate there was little to no habituation. It would also be needed to know which motor events are considered linked to the DF stimulus, and how that was decided. Was there a movement intensity threshold and lag limit in the response?

We interpret this concern as relating to the data presented in Figure 6A, where we quantify the habituation rate in the head-embedded experiments. As we have discussed, both above and in the manuscript, we saw very strongly muted responses to DFs in the head-embedded preparation, but we neglected to describe our method of quantifying the responses. We have added the following description to the methods:

“To quantify responses to the dark flash stimuli we used motion artifacts in the imaging data to identify frames associated with movements ([fig:1]-[fig:S1]). Motion artifact was quantified using the “corrXY” parameter from suite2p, which reflects the peak of phase correlation comparing each acquired frame and reference image used for motion correction. The “motion power” was quantified as the standard deviation of a 3-frame rolling window, which was smoothed in time using a Savitzky-Golay filter (window length = 15 frames, polyorder = 2). A response to a dark flash was defined as a “motion power” signal greater than 3 (z-score) occurring within 10-seconds of the dark-flash onset, and was used to quantify habituation in the head-embedded preparation ([fig:6]A).“

Line 94: This seems to be a strong claim based on the sparse presence of non-habituating, or potentiating, neurons in downstream regions. However, these neurons appear to be extremely rare, and as mentioned in my comment above, the behavioural habituation appears minimal. These neurons could encode the luminosity and be part of other responses, such as light-seeking in Karpenko S et al, eLife, 2020 or escape directionality in Heap et al, Neuron, 2018. Furthermore, dimming information has been shown to have parallel processing pathways in Robles E et al, JCN, 2020; so it would make sense that not all the observed responses in this manuscript would be involved in behavioural habituation to dark flashes.

We agree that without functional interventions, we do not know which of the neurons we have categorized are specifically involved in the dark flash response habituation. It is possible that the non-adapting and potentiating neurons are involved in other behaviours. We have therefore removed this statement.

Line 103: It appears that several of those responses are to the changes in luminosity and not the DF itself, especially the ON and sustained responses. Based on the previous DF habituation study from Randlet O et al, eLife, 2019; the latency of the response is below 0.5s. So the behaviour-relevant responses must only include the shortest latency one, as discussed above.

We appreciate the point that the reviewer is making here, but we are less clear about what the difference between “changes in luminosity” and a “dark flash” response are, since a dark flash consists of a change in luminosity. We take it that the reviewer means the difference between a luminance stimulus that elicits an O-bend, from one that does not. In order to disambiguate the two, one would likely need to use stimuli where the luminosity changes, but do not elicit O-bends.

Perhaps due to the limited temporal resolution of our Ca2+ imaging data, we do not see a clear difference in the onset of the stimulus response for any of the functional clusters that would help us to determine which neurons are more relevant to the acute DF response.

Fig.2B. It is very difficult to make out the actual average z-scored fluorescence, a supplementary figure would help by making these bigger. A plot to quantify the maximum response would also be useful to judge how it changes between the first few and few last DF. Another plot to give the time between the onset of the responses and the onset of the DF stimulus is also needed to judge which cluster may be relevant to the DF escapes observed in the free-swimming experiments.

We agree with the reviewer that interpreting these datasets are challenging. We did include the actual average z-scored fluorescence in Figure 6—figure supplement 1, panel D. This figure also includes a comparison between the predicted Ca2+ response to the dark flash (the stimulus convolved with the approximate GCaMP response kernel), which shows that all OFF-responding neuronal classes show very similar rise time response kinetics, and thus this analysis does not help to judge whether a cluster is more or less relevant to O-bend responses in the free-swimming experiments. We appreciate that there are differences in opinion about the best way to present the data, but we have opted to leave our original presentation.

Line 130: Is a correlation below 0.1 meaningful or significant? It does not seem like this cluster would be a motor or decision cluster.

Our goal with this correlational analysis to motor signals was to identify if certain clusters of DF responsive neurons were more associated with motor output, and therefore may be more downstream in the sensori-motor cascade. Cluster 4 showed the highest median correlation across the population of cells. Whether a median correlation of ~0.1 is “meaningful” is impossible for us to answer, but it is highly “significant” in the statistical sense, as is evident by the 99.99999% confidence intervals plotted. We note that these cells were not selected based on their correlation to the motor stimulus, but only to the dark flash stimulus. There are “motor” clusters that show much higher correlations to the motors signals, as is evident in Figure 1G.

Line 165: Did the changes observed for Pimozide fall below the significance threshold, were lethal, or were the results not repeated? It does not appear in source data 2.

Pimozide was lethal in our screen and therefore does not appear in the source data file. Indeed, in our previous experiments with Pimozide we had already established that a 10uM dose is lethal, and that the maximal effective dose we tried was 1uM as reported in (Randlett et al., Current Biology, 2019).

We have clarified this in the text:

“While the false negative rate is difficult to determine since so little is known about the pharmacology of the system, we note that of the three small molecules we previously established to alter dark flash habituation that were included in the screen, Clozapine, Haloperidol and Pimozide , the first two were identified among our hits while Pimozide was lethal at the 10\muM screening concentration.”

Fig.1B and Fig.3B are the same data, which is awkward and should be explicitly stated. But the legends do not match in terms of the rest period. Which is correct? It is also important to note the other behavioural assays in the 'rest' period.

We thank the reviewer for pointing out this discrepancy in the legend. We have corrected the typo in the figure legend of Figure 3B :

“Habituation results in a progressive decrease in responsiveness to dark flashes repeated at 1-minute intervals, delivered in 4 training blocks of 60 stimuli, separated by 1hr of rest (from 0:00-7:00).”

We have also added a statement that the data is the same as that in Figure 1B.

Figure 3-4: SSMD fingerprint, there is no description of the different behavioural parameters. What they represent is left to the reader's inference. There is no mention of SpontDisp in the GitHub for example, so it is hard to know how these different parameters were measured. Even referring to the previous manuscript on habituation (Randlet O et al, eLife, 2019) does not shed light on most of them, for example, I suppose TwoMvmt represents the 'double responses' from the previous manuscript. Furthermore, there are inconsistencies between 3C and 4B, some minor (SpontDisp becomes SpntDisp), but Curve-Tap has disappeared for example, and I suspect became BendAmp-Tap. A more thorough description of these measures, and making the naming scheme consistent, are essential for readers to know what they are looking at.

We again thank the reviewer for their careful assessment of our data, and we apologize for this sloppiness. We have gone through and made the naming of these parameters consistent in both figures, and have added another supplementary table that describes in more detail what each parameter is, and how it relates to the analysis code (Figure3_sourcedata3_SSMDFingerprintParameters.xls). This was an essential missing piece of information from our original manuscript.

Line 206: While this prioritization makes sense, how was it implemented, how was the threshold decided and which were they? A table, or supplementary figure, would help to clarify the reason behind the choices. Fig.4C being cropped only around the response probability makes it impossible to judge if the criteria were respected, as the main heatmap is too small. For example, the choice of GABA receptor antagonists is somewhat puzzling, as besides PTX it does not seem that the other compounds had strong effects, with Amoxapine for example having seemingly as much effect on Naive and Train, with little in Test. And Bicuculline gave negative SSMD for prob in the three cases. The dose-response for PTX does lend credence to its effect, but I would have liked the other compounds, especially bicuculline. The melatonin results, for example, are much more convincing and interesting in our opinion.

While in hindsight it may have been possible to do the hit prioritization in a systematic way using thresholding and ranking, we did this manually by inspecting the clustered fingerprints. We have clarified this in the text: “This manual prioritization led to the identification of the GABAA/C Receptor antagonists…”

While we agree that it is not possible to judge how well we performed this prioritization based on the images presented, we note that we do provide the full fingerprint data in the supplementary data, for which the reader is welcome to draw their own conclusions.

We have not performed further experiments with amoxapine, so we can not comment further on this. We did perform additional experiments with bicuculline, for which we did see effects similar to those of PTX, were habituation was inhibited. However, the effects are weaker and more variable than what we observe with PTX, and bicuculline also inhibits the initial responses of the larvae, causing their Naive response to be lower. Therefore we did not include it in our manuscript. We include these data here in Author response image 1 to reassure the Reviewer that picrotoxinin is not the only GABA Receptor antagonist for which we see inhibitory effects on habituation.

Author response image 1.

Fig.6: Why was the melatonin concentration used only 1um instead of 10um on the screen?

Based on dose response experiments (Figure 5B, and others not shown), we found that the effect of Melatonin on habituation saturates at about 1uM, and therefore we used this dose.

Line 277: As the correlation with motor output is marginal at best, and the authors recognize the lack of behaviour in tethered animals, I would be careful about such speculation. Especially since the other changes are complex and go in all directions.

While we appreciate the reviewer's caution, we feel that our statement is appropriately hedged using “might be”. We have also removed the statement “and thus is most closely associated with behavioural initiation”.

We now state:

“However, opposite effects of PTX and Melatonin were observed for 4_L^{strgD} neurons ([fig:6]C), which we found to be most strongly correlated with motor output ([fig:2]F). Therefore, this class might be most critical for habituation of response Probability.”

Fig.7: I am not sure how convincing these results are. 7F may have been more convincing, but to be thorough the authors would need to register the Gad1b identity to the calcium imaging and use their outline to extract the neuron's fluorescence. As it is, in the tectum, it is hard to be sure that all the identified neurons are indeed Gad1b positive, as that population is intermingled with other neuronal populations. The authors should consider the approach of Lovett-Barron M et al, Nat Neuro, 2020. Alternatively, the authors can tone down the language used in this section to match the confidence level of the association they propose.

Figure 7A-E are what can be considered “virtual colocalization” analyses, where we are comparing the localization of data acquired in different experiments using image registration to common atlas coordinates. We agree that these results alone will never be very strong evidence for the identification of individual cells. The MultiMAP approach of Lovett-Barron is a powerful approach, though it makes the assumption that registration accuracy will be subcellular, which in practice may often not be the case. We believe that a better approach is to label the cells of interest during the Ca2+ imaging experiment itself, as we did 7F and G. The challenge in this experiment is binarizing the ROIs and thus deciding what is and is not a Gad1b-positive cell. In our opinion, the fact that these two independent experiments came to the same conclusion regarding Cluster 10 and 11 is good evidence that these cell types are likely predominantly GABAergic.

As discussed above, we have re-written the manuscript to tone down our claims about the role of GABA and GABAergic neurons in habituation, which we hope the reviewer will agree better reflects the limitations of the data in Figure 6 and 7.

Line 317: Based on the somewhat inconsistent results of the other GABA antagonists, I would be careful. Picrotoxin has been reported to antagonize other receptors besides GABA, see Das P et al, Neuropharma, 2003. So the results may be explained by a complex set of effects on multiple pathways with PTX.

Off target effects are an important concern with any pharmacological experiment, and perhaps especially in zebrafish where receptors and targets can be quite divergent from those in mammals where most drug targets have been characterized. We have added this sentiment to the discussion:

“We cannot rule out the possibility that off-targets of PTX, or subtle non-specific changes in excitatory/inhibitory balance alter habituation behaviour.”

Line 400-403, 430: There are some conflicting statements regarding the potential role of clusters 1 and 2 in DF habituation. Do the authors think they play a role in the behaviour measured in this manuscript? Could they clarify what they mean?

We see how our original statement in line 429 about the presence of cluster 1 and 2 neurons in the TL implied a role in dark flash habituation. This was not our intent, and we have removed “which also contains high concentrations of on-responding neurons”.

Our thoughts on these neurons are now stated in the discussion as:

“We also observed classes exhibiting an On-response profile ( and ). These neurons fire at the ramping increase in luminance after the DF, making it unlikely that they play a role in aspects of acute DF behaviour we measured here. These neurons exist in both non-adapting and depressing forms suggesting a yet unidentified role in behavioural adaptation to repeated DFs.“

Minor comments

Line 73 (and elsewhere): Why use adaptation instead of habituation (also in the adaptation profile)? Do you suspect your observations do not reflect habituation, but a sensory adaptation mechanism?

We have used the convention that “habituation” refers to observations at the behavioural level, while “depression” and “potentiation” refer to observations at the neuronal level. We use the term “adaptation” to refer to neuronal adaptations of either sign (depression or potentiation), as in line 73.

We believe that our observations reflect neuronal adaptations that underlie habituation behaviour.

Line 71: It is debatable that the strongest learning happens in the first block, the difference between the first and last response seems to grow larger with each successive block. What do the authors mean by 'strongest'

We agree that “strongest” was ambiguous. We have changed this to “initial”:

“We focused on a single training block of 60 DFs to identify neuronal adaptations that occur during the initial phase of learning ”

Fig.1F: there is no rastermap call in the GitHub repository, was the embedding done in the GUI? If so, it should also be shared for reproducibility's sake.

Yes, Fig.1F was created using the suite2p GUI, as we have now clarified in the methods:

“The clustered heatmap image of neural activity (([fig:3]F) was generated using the suite2p GUI using the “Visualize selected cells” function, and sorting the neurons using the rastermap algorithm ”

The image is available in the “Figure1 - Ca2Imaging.svg” file available here: https://github.com/owenrandlett/lamire_2022/tree/main/LamireEtAl_2022

Line 101: while true that AffinityPropagation does not require input on the number of clusters, preference can influence the number of clusters. It seems that at least two values were tested in the search for the clusters, can the authors comment on how many clusters the other preference value converged (or failed to converge) on?

Indeed, as with any clustering approach, the resultant clusters are highly dependent on the input parameters, in this case the “preference”, as well as “damping” and the choice of affinity metric. By varying these parameters one can arrive at anywhere between 2 and hundreds of clusters.

It is for this reason that we feel that the anatomical analyses of these clusters is very important, making the assumption that neurons of differing functional types will have different localizations in the brain, as we explained in the Results:

“While these results indicate the presence of a dozen functionally distinct neuron types, such clustering analyses will force categories upon the data irrespective of if such categories actually exist. To determine if our cluster analyses identified genuine neuron types, we analyzed their anatomical localization ([fig:2]C-E). Since our clustering was based purely on functional responses, we reasoned that anatomical segregation of these clusters would be consistent with the presence of truly distinct types of neurons.”

We also acknowledge in the Results that the clustering approach has limitations:

“These results highlight a diversity of functional neuronal classes active during DF habituation. Whether there are indeed 12 classes of neurons, or if this is an over- or under-estimate, awaits a full molecular characterization. Independent of the precise number of neuronal classes, we proceed under the hypothesis that these clusters define neurons that play distinct roles in the DF response and/or its modulation during habituation learning“

Fig.2. My understanding is that the cluster numbers are arbitrary unless there is a meaning to them, which then should be explained. I would recommend grouping the clusters per functional category as in Fig.6 to make it easier for the reader.

Cluster number reflects the ordering in the hierarchical clustering tree shown in Figure 2B. We feel that this is the most logical representation of their functional similarity. We have clarified this in the Methods:

“ We then used the Affinity Propagation clustering from scikit-learn , with “affinity” computed as the Pearson product-moment correlation coefficients (corrcoef in NumPy ), preference=-9, and damping=0.9, and clustered using Hierarchical clustering (cluster.hierarchy in SciPy ). Cluster number was assigned based on the ordering of the hierarchical clustering tree. ”

Fig.3 SSMD fingerprint, it would be much easier for the readers if the list of parameters was clearer and rotated 90 degrees. Maybe in a supplementary figure to show what each represents.

We agree that the SSMD fingerprint is very difficult to interpret. As discussed above, we have now included a supplementary table (Figure3_sourcedata2_SSMDFingerprintParameters.xlsx) where we have clarified what each parameter represents.

Fig.4: The use of the same colours across the clustering methods is confusing, especially after the use of colours for the SSMD fingerprint in Fig.3. and at the bottom of 4A. Fig.4A for example could have been colour coded according to the most affected behaviour in the fingerprint at the bottom.

Fig.4B the coloured text is difficult to read, especially for the lighter colours.

We agree that our use of color is not perfect, but we have attempted to use them consistently: for example when referring to a functional cluster, or a drug manipulation. We don’t think that there is a sufficient number of distinguishable colors for us to never use the same color twice.

Fig.4C if the goal is to show similarity, the relevant drugs could be placed adjacent to each other. One could also report the Euclidean distance, or compute how correlated the different fingerprints are within one pharmacological target space.

The goal of Fig 4C is to highlight where Bicuculline, Amoxapine, Picrotoxinin, Melatonin, Ethinyl Estradiol and Hexestrol lie within the clustered heatmap of the behavioural fingerprints (Fig 4A), and<br /> demonstrate how the probability of response to dark flashes is modulated by these drugs. In our analyses, “similarity” is a function of the clustering distance.

Fig.6D 'Same data as M, ...' I assume should be 'Same data as C,...'

Indeed, thank you for pointing out this error that we have corrected.

Fig. 7 How many GCaMP6s double transgenic larvae were imaged?

6 fish were imaged, as is stated in the legend to Fig 7G

Line 407: all is repeated.

We apologize, but we do not see what is repeated at line 407. Can you please clarify?

Line 481: Would testing spontaneous activity after training for 7h be unbiased, could there be fatigue effects?

We tested for fatigue effects in our previous study, comparing larvae that received the training for 7hrs and those that did not, and we saw no deficits in spontaneous activity, tap response, or OMR performance (Figure S1, Randlett et al., Current Biology, 2019).

Line 610: There are some inconsistencies between the authors' contributions in the manuscript and the one provided to eLife.

Thank you, we will double check this in the resubmission forms. The authors' contributions in the manuscript are correct.

Reviewer #3 (Recommendations For The Authors):

I would rather recommend the authors divide this manuscript into two and publish two papers by adding some more strengthening data for each part such as cellular manipulations, e.g. ablation to prove the critical involvement of 12(Pot, M) neurons in habituation.

We thank the reviewer for their suggestion, but have opted not to split the paper into two. We feel that the collective message of this paper and approach combining molecular and functional analysis will be of interest, and we believe the incongruencies in our results reflects the complexity inherent within the system.

Author Response

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

Thank you for the detailed and constructive reviews. We revised the paper accordingly, and a point-by-point reply appears below. The main changes are:

• An extended discussion section that places our work in context with other related developments in theory and modeling.

• A new results section that demonstrates a substantial improvement in performance from a non-linear activation function. This led to addition of a co-author.

• The mathematical proof that the resolvent of the adjacency matrix leads to the shortest path distances has been moved to a separate article, available as a preprint and attached to this resubmission. This allows us to present that work in the context of graph theory, and focus the present paper on neural modeling.

Reviewer #1 (Public Review):

This paper presents a highly compelling and novel hypothesis for how the brain could generate signals to guide navigation towards remembered goals. Under this hypothesis, which the authors call "Endotaxis", the brain co-opts its ancient ability to navigate up odor gradients (chemotaxis) by generating a "virtual odor" that grows stronger the closer the animal is to a goal location. This idea is compelling from an evolutionary perspective and a mechanistic perspective. The paper is well-written and delightful to read.

The authors develop a detailed model of how the brain may perform "Endotaxis", using a variety of interconnected cell types (point, map, and goal cells) to inform the chemotaxis system. They tested the ability of this model to navigate in several state spaces, representing both physical mazes and abstract cognitive tasks. The Endotaxis model performed reasonably well across different environments and different types of goals.

The authors further tested the model using parameter sweeps and discovered a critical level of network gain, beyond which task performance drops. This critical level approximately matched analytical derivations.

My main concern with this paper is that the analysis of the critical gain value (gamma_c) is incomplete, making the implications of these analyses unclear. There are several different reasonable ways in which the Endotaxis map cell representations might be normalized, which I suspect may lead to different results. Specifically, the recurrent connections between map cells may either be an adjacency matrix, or a normalized transition matrix. In the current submission, the recurrent connections are an unnormalized adjacency matrix. In a previous preprint version of the Endotaxis manuscript, the recurrent connections between the map cells were learned using Oja's rule, which results in a normalized state-transition matrix (see "Appendix 5: Endotaxis model and the successor representation" in "Neural learning rules for generating flexible predictions and computing the successor representation", your reference 17). The authors state "In summary, this sensitivity analysis shows that the optimal parameter set for endotaxis does depend on the environment". Is this statement, and the other conclusions of the sensitivity analysis, still true if the learned recurrent connections are a properly normalized state-transition matrix?

Yes, this is an interesting topic. In v.1 of our bioRxiv preprint we used Oja’s rule for learning, which will converge on a map connectivity that reflects the transition probabilities. The matrix M becomes a left-normalized or right-normalized stochastic matrix, depending on whether one uses the pre-synaptic or the post-synaptic version of Oja’s rule. This is explained well in Appendix 5 of Fang 2023.

In the present version of the model we use a rule that learns the adjacency matrix A, not the transition matrix T. The motivation is that we want to explain instances of oneshot learning, where an agent acquires a route after traversing it just once. For example, we had found experimentally that mice can execute a complex homing route on the first attempt.

An agent can establish whether two nodes are connected (adjacency) the very first time it travels from one node to the other. Whereas it can evaluate the transition probability for that link only after trying this and all the other available links on multiple occasions. Hence the normalization terms in Oja’s rule, or in the rule used by Fang 2023, all involve some time-averaging over multiple visits to the same node. This implements a gradual learning process over many experiences, rather than a one-shot acquisition on the first experience.

Still one may ask whether there are advantages to learning the transition matrix rather than the adjacency matrix. We looked into this with the following results:

• The result that (1/γ − A)−1 is monotonically related to the graph distances D in the limit of small γ (a proof now moved to the Meister 2023 preprint) , holds also for the transition matrix T. The proof follows the same steps. So in the small gain limit, the navigation model would work with T as well.

• If one uses the transition matrix to compute the network output (1/γ − T)-1 then the critical gain value is γc = 1. It is well known that the largest eigenvalue of any Markov transition matrix is 1, and the critical gain γc is the inverse of that. This result is independent of the graph. So this offers the promise that the network could use the same gain parameter γ regardless of the environment.

• In practice, however, the goal signal turned out to be less robust when based on T than when based on A. We illustrate this with the attached Author response image 1. This replicates the analysis in Figure 3 of the manuscript, using the transition matrix instead of the adjacency matrix. Some observations:

• Panel B: The goal signal follows an exponential dependence on graph distance much more robustly for the model with A than with T. This holds even for small gain values where the exponential decay is steep.

• Panel C: As one raises the gain closer to the critical value, the goal signal based on T scatters much more than when based on A.

• Panels D, E: Navigation based on A works better than based on T. For example, using the highest practical gain value, and a readout noise of ϵ = 0.01, navigation based on T has a range of only 8 steps on this graph, whereas navigation based on A ranges over 12 steps, the full size of this graph.

We have added a section “Choice of learning rule” to explain this. The Author response image 1 is part of the code notebook on Github.

Author response image 1.

Overall, this paper provides a very compelling model for how neural circuits may have evolved the ability to navigate towards remembered goals, using ancient chemotaxis circuits.

This framework will likely be very important for understanding how the hippocampus (and other memory/navigation-related circuits) interfaces with other processes in the brain, giving rise to memory-guided behavior.

Reviewer #2 (Public Review):

The manuscript presents a computational model of how an organism might learn a map of the structure of its environment and the location of valuable resources through synaptic plasticity, and how this map could subsequently be used for goal-directed navigation.

The model is composed of 'map cells', which learn the structure of the environment in their recurrent connections, and 'goal-cell' which stores the location of valued resources with respect to the map cell population. Each map cell corresponds to a particular location in the environment due to receiving external excitatory input at this location. The synaptic plasticity rule between map cells potentiates synapses when activity above a specified threshold at the pre-synaptic neuron is followed by above-threshold activity at the post-synaptic neuron. The threshold is set such that map neurons are only driven above this plasticity threshold by the external excitatory input, causing synapses to only be potentiated between a pair of map neurons when the organism moves directly between the locations they represent. This causes the weight matrix between the map neurons to learn the adjacency for the graph of locations in the environment, i.e. after learning the synaptic weight matrix matches the environment's adjacency matrix. Recurrent activity in the map neuron population then causes a bump of activity centred on the current location, which drops off exponentially with the diffusion distance on the graph. Each goal cell receives input from the map cells, and also from a 'resource cell' whose activity indicates the presence or absence of a given values resource at the current location. Synaptic plasticity potentiates map-cell to goal-cell synapses in proportion to the activity of the map cells at time points when the resource cell is active. This causes goal cell activity to increase when the activity of the map cell population is similar to the activity where the resource was obtained. The upshot of all this is that after learning the activity of goal cells decreases exponentially with the diffusion distance from the corresponding goal location. The organism can therefore navigate to a given goal by doing gradient ascent on the activity of the corresponding goal cell. The process of evaluating these gradients and using them to select actions is not modelled explicitly, but the authors point to the similarity of this mechanism to chemotaxis (ascending a gradient of odour concentration to reach the odour source), and the widespread capacity for chemotaxis in the animal kingdom, to argue for its biological plausibility.

The ideas are interesting and the presentation in the manuscript is generally clear. The two principle limitations of the manuscript are: i) Many of the ideas that the model implements have been explored in previous work. ii) The mapping of the circuit model onto real biological systems is pretty speculative, particularly with respect to the cerebellum.

Regarding the novelty of the work, the idea of flexibly navigating to goals by descending distance gradients dates back to at least Kaelbling (Learning to achieve goals, IJCAI, 1993), and is closely related to both the successor representation (cited in manuscript) and Linear Markov Decision Processes (LMDPs) (Piray and Daw, 2021, https://doi.org/ 10.1038/s41467-021-25123-3, Todorov, 2009 https://doi.org/10.1073/pnas.0710743106). The specific proposal of navigating to goals by doing gradient descent on diffusion distances, computed as powers of the adjacency matrix, is explored in Baram et al. 2018 (https://doi.org/10.1101/421461), and the idea that recurrent neural networks whose weights are the adjacency matrix can compute diffusion distances are explored in Fang et al. 2022 (https://doi.org/10.1101/2022.05.18.492543). Similar ideas about route planning using the spread of recurrent activity are also explored in Corneil and Gerstner (2015, cited in manuscript). Further exploration of this space of ideas is no bad thing, but it is important to be clear where prior literature has proposed closely related ideas.

We have added a discussion section on “Theories and models of spatial learning” with a survey of ideas in this domain and how they come together in the Endotaxis model.

Regarding whether the proposed circuit model might plausibly map onto a real biological system, I will focus on the mammalian brain as I don't know the relevant insect literature. It was not completely clear to me how the authors think their model corresponds to mammalian brain circuits. When they initially discuss brain circuits they point to the cerebellum as a plausible candidate structure (lines 520-546). Though the correspondence between cerebellar and model cell types is not very clearly outlined, my understanding is they propose that cerebellar granule cells are the 'map-cells' and Purkinje cells are the 'goal-cells'. I'm no cerebellum expert, but my understanding is that the granule cells do not have recurrent excitatory connections needed by the map cells. I am also not aware of reports of place-field-like firing in these cell populations that would be predicted by this correspondence. If the authors think the cerebellum is the substrate for the proposed mechanism they should clearly outline the proposed correspondence between cerebellar and model cell types and support the argument with reference to the circuit architecture, firing properties, lesion studies, etc.

On further thought we agree that the cerebellum-like circuits are not a plausible substrate for the endotaxis algorithm. The anatomy looks compelling, but plasticity at the synapse is anti-hebbian, and - as the reviewer points out - there is little evidence for recurrence among the inputs. We changed the discussion text accordingly.

The authors also discuss the possibility that the hippocampal formation might implement the proposed model, though confusingly they state 'we do not presume that endotaxis is localized to that structure' (line 564).

We have removed that confusing bit of text.

A correspondence with the hippocampus appears more plausible than the cerebellum, given the spatial tuning properties of hippocampal cells, and the profound effect of lesions on navigation behaviours. When discussing the possible relationship of the model to hippocampal circuits it would be useful to address internally generated sequential activity in the hippocampus. During active navigation, and when animals exhibit vicarious trial and error at decision points, internally generated sequential activity of hippocampal place cells appears to explore different possible routes ahead of the animal (Kay et al. 2020, https://doi.org/10.1016/j.cell.2020.01.014, Reddish 2016, https:// doi.org/10.1038/nrn.2015.30). Given the emphasis the model places on sampling possible future locations to evaluate goal-distance gradients, this seems highly relevant.

In our model, the possible future locations are sampled in real life, with the agent moving there or at least in that direction, e.g. via VTE movements. In this simple form the model has no provision for internal planning, and the animal never learns any specific route sequence. One can envision extending such a model with some form of sequence learning that would then support an internal planning mechanism. We mention this in the revised discussion section, along with citation of these relevant articles.

Also, given the strong emphasis the authors place on the relationship of their model to chemotaxis/odour-guided navigation, it would be useful to discuss brain circuits involved in chemotaxis, and whether/how these circuits relate to those involved in goal-directed navigation, and the proposed model.

The neural basis of goal-directed navigation is probably best understood in the insect brain. There the locomotor decisions seem to be initiated in the central complex, whose circuitry is getting revealed by the fly connectome projects. This area receives input from diverse sensory areas that deliver the signal on which the decisions are based. That includes the mushroom body, which we argue has the anatomical structure to implement the endotaxis algorithm. It remains a mystery how the insect chooses a particular goal for pursuit via its decisions. It could be revealing to force a change in goals (the mode switch in the endotaxis circuit) while recording from brain areas like the central complex. Our discussion now elaborates on this.

Finally, it would be useful to clarify two aspects of the behaviour of the proposed algorithm:

1) When discussing the relationship of the model to the successor representation (lines 620-627), the authors emphasise that learning in the model is independent of the policy followed by the agent during learning, while the successor representation is policy dependent. The policy independence of the model is achieved by making the synapses between map cells binary (0 or 1 weight) and setting them to 1 following a single transition between two locations. This makes the model unsuitable for learning the structure of graphs with probabilistic transitions, e.g. it would not behave adaptively in the widely used two-step task (Daw et al. 2011, https://doi.org/10.1016/ j.neuron.2011.02.027) as it would fail to differentiate between common and rare transitions. This limitation should be made clear and is particularly relevant to claims that the model can handle cognitive tasks in general. It is also worth noting that there are algorithms that are closely related to the successor representation, but which learn about the structure of the environment independent of the subjects policy, e.g. the work of Kaelbling which learns shortest path distances, and the default representation in the work of Piray and Daw (both referenced above). Both these approaches handle probabilistic transition structures.

Yes. Our problem statement assumes that the environment is a graph with fixed edge weights. The revised text mentions this and other assumptions in a new section “Choice of learning rule”.

2) As the model evaluates distances using powers of adjacency matrix, the resulting distances are diffusion distances not shortest path distances. Though diffusion and shortest path distances are usually closely correlated, they can differ systematically for some graphs (see Baram et al. ci:ted above).

The recurrent network of map cells implements a specific function of the adjacency matrix, namely the resolvent (Eqn 7). We have a mathematical proof that this function delivers the shortest graph distances exactly, in the limit of small gain (γ in Eqn 7), and that this holds true for all graphs. For practical navigation in the presence of noise, one needs to raise the gain to something finite. Figure 3 analyzes how this affects deviations from the shortest graph distance, and how nonetheless the model still supports effective navigation over a surprising range. The mathematical details of the proof and further exploration of the resolvent distance at finite gain have been moved to a separate article, which is cited from here, and attached to the submission. The preprint by Baram et al. is cited in that article.

Reviewer #3 (Public Review):

This paper argues that it has developed an algorithm conceptually related to chemotaxis that provides a general mechanism for goal-directed behaviour in a biologically plausible neural form.

The method depends on substantial simplifying assumptions. The simulated animal effectively moves through an environment consisting of discrete locations and can reliably detect when it is in each location. Whenever it moves from one location to an adjacent location, it perfectly learns the connectivity between these two locations (changes the value in an adjacency matrix to 1). This creates a graph of connections that reflects the explored environment. In this graph, the current location gets input activation and this spreads to all connected nodes multiplied by a constant decay (adjusted to the branching number of the graph) so that as the number of connection steps increases the activation decreases. Some locations will be marked as goals through experiencing a resource of a specific identity there, and subsequently will be activated by an amount proportional to their distance in the graph from the current location, i.e., their activation will increase if the agent moves a step closer and decrease if it moves a step further away. Hence by making such exploratory movements, the animal can decide which way to move to obtain a specified goal.

I note here that it was not clear what purpose, other than increasing the effective range of activation, is served by having the goal input weights set based on the activation levels when the goal is obtained. As demonstrated in the homing behaviour, it is sufficient to just have a goal connected to a single location for the mechanism to work (i.e., the activation at that location increases if the animal takes a step closer to it); and as demonstrated by adding a new graph connection, goal activation is immediately altered in an appropriate way to exploit a new shortcut, without the goal weights corresponding to this graph change needing to be relearnt.

As the reviewer states, allowing a graded strengthening of multiple synapses from the map cells increases the effective range of the goal signal. We have now confirmed this in simulations. For example, in the analysis of Fig 3E, a single goal synapse enables perfect navigation only over a range of 7 steps, whereas the distributed goal synapses allow perfect navigation over the full 12 steps. This analysis is included in the code notebook on Github.

Given the abstractions introduced, it is clear that the biological task here has been reduced to the general problem of calculating the shortest path in a graph. That is, no real-world complications such as how to reliably recognise the same location when deciding that a new node should be introduced for a new location, or how to reliably execute movements between locations are addressed. Noise is only introduced as a 1% variability in the goal signal. It is therefore surprising that the main text provides almost no discussion of the conceptual relationship of this work to decades of previous work in calculating the shortest path in graphs, including a wide range of neural- and hardwarebased algorithms, many of which have been presented in the context of brain circuits.

The connection to this work is briefly made in appendix A.1, where it is argued that the shortest path distance between two nodes in a directed graph can be calculated from equation 15, which depends only on the adjacency matrix and the decay parameter (provided the latter falls below a given value). It is not clear from the presentation whether this is a novel result. No direct reference is given for the derivation so I assume it is novel. But if this is a previously unknown solution to the general problem it deserves to be much more strongly featured and either way it needs to be appropriately set in the context of previous work.

As far as we know this proposal for computing all-pairs-shortest-path is novel. We could not find it in textbooks or an extended literature search. We have discussed it with two graph theorist colleagues, who could not recall seeing it before, although the proof of the relationship is elementary. Inspired by the present reviewer comment, we chose to publish the result in a separate article that can focus on the mathematics and place it in the appropriate context of prior work in graph theory. For related work in the area of neural modeling please see our revised discussion section.

Once this principle is grasped, the added value of the simulated results is somewhat limited. These show: 1) in practical terms, the spreading signal travels further for a smaller decay but becomes erratic as the decay parameter (map neuron gain) approaches its theoretical upper bound and decreases below noise levels beyond a certain distance. Both follow the theory. 2) that different graph structures can be acquired and used to approach goal locations (not surprising) .3) that simultaneous learning and exploitation of the graph only minimally affects the performance over starting with perfect knowledge of the graph. 4) that the parameters interact in expected ways. It might have been more impactful to explore whether the parameters could be dynamically tuned, based on the overall graph activity.

This is a good summary of our simulation results, but we differ in the assessment of their value. In our experience, simulations can easily demolish an idea that seemed wonderful before exposure to numerical reality. For example, it is well known that one can build a neural integrator from a recurrent network that has feedback gain of exactly 1. In practical simulations, though, these networks tend to be fickle and unstable, and require unrealistically accurate tuning of the feedback gain. In our case, the theory predicts that there is a limited range of gains that should work, below the critical value, but large enough to avoid excessive decay of the signal. Simulation was needed to test what this practical range was, and we were pleasantly surprised that it is not ridiculously small, with robust navigation over a 10-20% range. Similarly, we did not predict that the same parameters would allow for effective acquisition of a new graph, learning of targets within the graph, and shortest-route navigation to those targets, without requiring any change in the operation of the network.

Perhaps the most biologically interesting aspect of the work is to demonstrate the effectiveness, for flexible behaviour, of keeping separate the latent learning of environmental structure and the association of specific environmental states to goals or values. This contrasts (as the authors discuss) with the standard reinforcement learning approach, for example, that tries to learn the value of states that lead to reward. Examples of flexibility include the homing behaviour (a goal state is learned before any of the map is learned) and the patrolling behaviour (a goal cell that monitors all states for how recently they were visited). It is also interesting to link the mechanism of exploration of neighbouring states to observed scanning behaviours in navigating animals.

The mapping to brain circuits is less convincing. Specifically, for the analogy to the mushroom body, it is not clear what connectivity (in the MB) is supposed to underlie the graph structure which is crucial to the whole concept. Is it assumed that Kenyon cell connections perform the activation spreading function and that these connections are sufficiently adaptable to rapidly learn the adjacency matrix? Is there any evidence for this?

Yes, there is good evidence for recurrent synapses among Kenyon cells (map cells in the model), and for reward-gated synaptic plasticity at the synapses onto mushroom body output cells (goal cells in our model). We have expanded this material in the discussion section. Whether those functions are sufficient to learn the structure of a spatial environment has not been explored; we hope our paper might give an impetus, and are exploring behavioral experiments on flies with colleagues.

As discussed above, the possibility that an algorithm like 'endotaxis' could explain how the rodent place cell system could support trajectory planning has already been explored in previous work so it is not clear what additional insight is gained from the current model.

Please see our revised discussion section on “theories and models of spatial learning”. In short, some ingredients of the model have appeared in prior work, but we believe that the present formulation offers an unexpectedly simple end-to-end solution for all components of navigation: exploration, target learning, and goal seeking.

Reviewer #1 (Recommendations For The Authors):

Major concern:

See the public review. How do the results change depending on whether the recurrent connections between map cells are an adjacency matrix vs. a properly normalized statetransition matrix? I'm especially asking about results related to critical gain (gamma_c), and the dependence of the optimal parameter values on the environment.

Please see our response above including the attached reviewer figure.

Minor concerns:

It is not always clear when the learning rule is symmetric vs asymmetric (undirected vs directed graph), and it seems to switch back and forth. For example, line 127 refers to a directed graph; Fig 2B and the intro describe symmetric Hebbian learning. Most (all?) of the simulations use the symmetric rule. Please make sure it's clear.

For simplicity we now use a symmetric rule throughout, as is appropriate for undirected graphs. We mention that a directed learning rule could be used to learn directed graphs. See the section on “choice of learning rule”. M_ij is not defined when it's first introduced (eq 4). Consider labeling the M's and the G's in Fig 2.

Done.

The network gain factor (gamma, eq 4) is distributed over both external and recurrent inputs (v = gamma(u + Mv)), instead of local to the recurrent weights like in the Successor Representation. This notational choice is obviously up to the authors. I raise slight concern for two reasons -- first, distributing gamma may affect some of the parameter sweep results (see major concern), and second, it may be confusing in light of how gamma is used in the SR literature (see reviewer's paper for the derivation of how SR is computed by an RNN with gain gamma).

In our model, gamma represents the (linear) activation function of the map neuron, from synaptic input to firing output. Because the synaptic input comes from point cells and also from other map cells, the gain factor is applied to both. See for example the Dayan & Abbott book Eqn 7.11, which at steady state becomes our Eqn 4. In the formalism of Fang 2023 (Eqn 2), the factor γ is only applied to the recurrent synaptic input J ⋅ f, but somehow not to the place cell input ϕ. Biophysically, one could imagine applying the variable gain only to the recurrent synapses and not the feed-forward ones. Instead we prefer to think of it as modulating the gain of the neurons, rather than the synapses. The SR literature follows conventions from the early reinforcement learning papers, which were unconstrained by thinking about neurons and synapses. We have added a footnote pointing the reader to the uses of γ in different papers.

In eq 13, and simulations, noise is added to the output only, not to the activity of recurrently connected neurons. It is possible this underestimates the impact of noise since the same magnitude of noise in the recurrent network (map cells) could have a compounded effect on the output.

Certainly. The equivalent output noise represents the cumulative effect of noise everywhere in the network. We argue that a cumulative effect of 1% is reasonable given the overall ability of animals at stimulus discrimination, which is also limited by noise everywhere in the network. This has been clarified in the text.

Fig 3 E, F, it looks like the navigated distance may be capped. I ask because the error bars for graph distance = 12 are so small/nonexistent. If it's capped, this should be in the legend.

Correct. 12 is the largest distance on this graph. This has been added to the caption.

Fig 3D legend, what does "navigation failed" mean? These results are not shown.

On those occasions the agent gets trapped at a local maximum of the goal signal other than the intended goal. We have removed that line as it is not needed to interpret the data.

Line 446, typo (Lateron).

Fixed.

Line 475, I'm a bit confused by the discussion of birds and bats. Bird behavior in the real world does involve discrete paths between points. Even if they theoretically could fly between any points, there are costs to doing so, and in practice, they often choose discrete favorite paths. It is definitely plausible that animals that can fly could also employ Endotaxis, so it is confusing to suggest they don't have the right behavior for Endotaxis, especially given the focus on fruit flies later in the discussion.

Good points, we removed that remark. Regarding fruit flies, they handle much important business while walking, such as tracking a mate, fighting rivals over food, finding a good oviposition site.

Section 9.3, I'm a bit confused by the discussion of cerebellum-like structures, because I don't think they have as dense recurrent connections as needed for the map cells in Endotaxis. Are you suggesting they are analogous to the output part of Endotaxis only, not the whole thing?

Please see our reply in the public review. We have removed this discussion of cerebellar circuits.

Line 541, "After sufficient exploration...", clarify that this is describing learning of just the output synapses, not the recurrent connections between map cells?

We have revised this entire section on the arthropod mushroom body.

In lines 551-556, the discussion is confusing and possibly not consistent with current literature. How can a simulation prove that synapses in the hippocampus are only strengthened among immediately adjacent place fields? I'd suggest either removing this discussion or adding further clarification. More broadly, the connection between Endotaxis and the hippocampus is very compelling. This might also be a good point to bring up BTSP (though you do already bring it up later).

As suggested, we removed this section.

Line 621 "The successor representation (at least as currently discussed) is designed to improve learning under a particular policy" That's not actually accurate. Ref 17 (reviewer's manuscript, cited here) is not policy-specific, and instead just learns the transition statistics experienced by the animal, using a biologically plausible learning rule that is very similar to the Endotaxis map cell learning rule (see our Appendix 5, comparing to Endotaxis, though that was referencing the previous version of the Endotaxis preprint where Oja's rule was used).

We have edited this section in the discussion and removed the reference to policyspecific successor representations.

Line 636 "Endotaxis is always on" ... this was not clear earlier in the paper (e.g. line 268, and the separation of different algorithms, and "while learning do" in Algorithm 2).

The learning rules are suspended during some simulations so we can better measure the effects of different parts of endotaxis, in particular learning vs navigating. There is no interference between these two functions, and an agent benefits from having the learning rules on all the time. The text now clarifies this in the relevant sections.

Section 9.6, I like the idea of tracing different connected functions. But when you say "that could lead to the mode switch"... I'm a bit confused about what is meant here. A mode switch doesn't need to happen in a different brain area/network, because winnertake-all could be implemented by mutual inhibition between the different goal units.

This is an interesting suggestion for the high-level control algorithm. A Lorenzian view is that the animal’s choice of mode depends on internal states or drives, such as thirst vs hunger, that compete with each other. In that picture the goal cells represent options to be pursued, whereas the choice among the options occurs separately. But one could imagine that the arbitrage between drives happens through a competition at the level of goal cells: For example the consumption of water could lead to adaptation of the water cell, such that it loses out in the winner-take-all competition, the food cell takes over, and the mouse now navigates towards food. In this closed-loop picture, the animal doesn’t have to “know” what it wants at any given time, it just wants the right thing. This could eliminate the homunculus entirely! Of course this is all a bit speculative. We have edited the closing comments in a way that leaves open this possibility.

Line 697-704, I need more step-by-step explanation/derivation.

We now derive the properties of E step by step starting from Eqn (14). The proof that leads to Eqn 14 is now in a separate article (available as a preprint and attached to this submission).

Reviewer #3 (Recommendations For The Authors):

• Please include discussion and comparison to previous work of graph-based trajectory planning using spreading activation from the current node and/or the goal node. Here is a (far from comprehensive) list of papers that present similar algorithms:

Glasius, R., Komoda, A., & Gielen, S. C. (1996). A biologically inspired neural net for trajectory formation and obstacle avoidance. Biological Cybernetics, 74(6), 511-520.

Gaussier, P., Revel, A., Banquet, J. P., & Babeau, V. (2002). From view cells and place cells to cognitive map learning: processing stages of the hippocampal system. Biological cybernetics, 86(1), 15-28.

Gorchetchnikov A, Hasselmo ME. A biophysical implementation of a bidirectional graph search algorithm to solve multiple goal navigation tasks. Connection Science. 2005;17(1-2):145-166

Martinet, L. E., Sheynikhovich, D., Benchenane, K., & Arleo, A. (2011). Spatial learning and action planning in a prefrontal cortical network model. PLoS computational biology, 7(5), e1002045.

Ponulak, F., & Hopfield, J. J. (2013). Rapid, parallel path planning by propagating wavefronts of spiking neural activity. Frontiers in computational neuroscience, 7, 98.

Khajeh-Alijani, A., Urbanczik, R., & Senn, W. (2015). Scale-free navigational planning by neuronal traveling waves. PloS one, 10(7), e0127269.

Adamatzky, A. (2017). Physical maze solvers. All twelve prototypes implement 1961 Lee algorithm. In Emergent computation (pp. 489-504). Springer, Cham.

Please see our reply to the public review above, and the new discussion section on “Theories and models of spatial learning”, which cites most of these papers among others.

• Please explain, if it is the case, why the goal cell learning (other than a direct link between the goal and the corresponding map location) and calculation of the overlapping 'goal signal' is necessary, or at least advantageous.

Please see our reply in the public review above.

• Map cells are initially introduced (line 84) as getting input from "only one or a few point cells". The rest of the paper seems to assume only one. Does it work when this is 'a few'? Does it matter that 'a few' is an option?

We simplified the text here to “only one point cell”. A map cell with input from two distant locations creates problems. After learning the map synapses from adjacencies in the environment, the model now “believes” that those two locations are connected. This distorts the graph on which the graph distances are computed and introduces errors in the resulting goal signals. One can elaborate the present toy model with a much larger population of map cells that might convey more robustness, but that is beyond our current scope.

• (line 539 on) Please explain what feature in the mushroom body (or other cerebellumlike) circuits is proposed to correspond to the learning of connections in the adjacency matrix in the model.

Please see our response to this critique in the public review above. In the mushroom body, the Kenyon cells exhibit sparse responses and are recurrently connected. These would correspond to map cells in Endotaxis. For vertebrate cerebellum-like circuits, the correspondence is less compelling, and we have removed this topic from the discussion.

Author Response

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

Public Reviews:

Reviewer #1 (Public Review):

Cell death plays a critical role on regulating organogenesis. During tooth morphogenesis, apoptosis of embryonic dental tissue plays critical roles on regulating tooth germ development. The current study focused on ferroptosis, another way of cell death which has rarely been investigated in tooth development, and showed it may also play an important role on regulating the tooth dimension. The topic is novel and interesting, but the experimental design has many flaws which significantly compromised the study.

1. The entire study was based on ex vivo tooth germ explant culture. Mandibular tooth germs of E15.5 (bell stage) were isolated for ex vivo culture. Most tooth germ explant culture experiments were actually using tooth germ of much earlier stages (E11.5-E13.5) for organ culture. After E16.5, both the large size and initially formed enamel/dentin could prevent nutrition from penetrating inside. Also, using tooth germ of earlier stage will help identify impact of ferroptosis upon early tooth development.

2. Due to limited penetration, the ex vivo culture in the study lasted for no more than 5 days. I would recommend the authors to perform kidney capsule transplantation as an alternative approach, which can support tooth germ development much longer even into root formation.

3. The major justification of using tooth germ ex vivo culture as the model in the study was to "conduct high-throughput analysis". However, the study could hardly be qualified as a high-throughput analysis. I would recommend the authors perform RNA sequencing for comparing tooth germs before/after erastin treatment. Such experiments won't take too much time or resource.

We are grateful for the insightful feedback on our ex vivo tooth germ culture model. We initially chose the E15.5 tooth germ over earlier stages due to peak Gpx4 expression and iron accumulation during molar development, which occurs between E15.5 and E17.5 (Figure 1A & 1B). This period may be the most sensitive to ferroptotic stress during tooth development. Our experiments also demonstrated that the tooth germ displays robust growth after seven days of ex vivo cultivation (Figure supplement 1B).

Kidney capsule transplantation is indeed an ideal method for ex vivo tooth germ culture. However, in our studies, we used erastin – a classic ferroptosis inducer – which exhibits instability in vivo, thereby constraining our investigation using kidney capsule transplantation.

Our results about Gpx4 expression in the tooth germ during development (Figure 1A) showed a spatiotemporal pattern. This pattern suggests that bulk RNA sequencing of the tooth germ might not yield accurate revelations about changes in ferroptosis-related genes. We are presently using transgenic mice to further study the impact of excessive in vivo ferroptotic stress on tooth development. In these experiments, we intend to conduct single-cell RNA sequencing to explore detailed alterations in the tooth germ.

1. Although the study mostly used molars as the model, the in vivo iron concentration was only demonstrated on incisors, but not molars (Figure 1).

We have updated Figure 1B to include images of molars, which illustrate the accumulation of iron during molar development. The iron concentration peaks at E17.5, then decreases at PN0. Interestingly, unlike Gpx4 expression, iron accumulation rebounds at PN3. To gain a more accurate understanding, further in vivo studies utilizing transgenic mice are required.

1. Phenotype analysis in Figure 2 is too superficial. Only dimensional information was provided. Cusps number, cusps distribution pattern and rooth/furcation formation were not evaluated. Differentiation of ameloblast/odontoblast was not evaluated. The proliferation rate in the dental epithelium/mesenchyme was not analyzed.

The cusps number/distribution pattern are not influenced by erastin treatment in recent model (Figure 2A & 2C). Recent ex vivo culture model of tooth germ is unable to investigate the possible function of ferroptotic stress in rooth/furcation formation since it mainly initiates from PN4 to PN7. The proliferation and differentiation of dental epithelium/mesenchyme will be analyzed using transgenic mice in vivo.

1. Low magnification images should be included in Figure 3 to display the entire tooth germs.

The emission spectrum of recent utilized iron probe will extend due to increasing concentration of iron. This property makes the counter staining of tissue samples unavailable. The structure of the ex vivo cultured tooth germ could only be recognized in high magnification. The calculation could represent the entire alternation.

1. In Figure 4, does ferroptotic inhibitor eliminate the iron accumulation in the tooth germ? How about the expression level of several target genes shown in Figure 3?

In Fig 5, Fer-1 reduced the iron accumulation in tooth germ. Different inhibitors suppressed ferroptosis via different ways, Lip-1 mainly inhibits lipid peroxidation, DFO is an iron chelator which reduces the labile iron pool, Fer-1 is reported to both inhibit lipid peroxidation and reduce the labile iron pool, their functions to the accumulation of iron might be varied. The core risk factors of ferroptosis are lipid peroxidation and iron accumulation, thus in Fig 5, we analyzed the expression of 4HNE and the accumulation of iron to illustrated the suppression o ferroptosis instead of detecting several regulatory genes.

1. The manuscript has many typos and grammar mistakes. All "submandibular" should be simply "mandibular". "eastin" should be "erastin" (line 92). "partly" should be "partially" (line 611).

We addressed all the gramma and typo errors.

Reviewer #2 (Recommendations for The Authors):

This is a very well done study. However, writing is absolutely substandard. The authors should check and review extensively for improvements to the use of English. This is not just about language but also about style of the paper and presentation. As written, the abstract is not concise at all, and the overall logic of the study is not well presented. Currently, the abstract reads like another introduction.

We improved our presentation.

Reviewer #3 (Recommendations for The Authors):

This is an interesting work reporting ferroptosis that is involved in the tooth morphogenesis. The authors showed that Gpx4, the core anti-lipid peroxidation enzyme in ferroptosis, is upregulated in tooth development using ex vivo culture system. They convincingly demonstrated that ferroptosis, but apoptosis, was present in tooth morphogenesis. The findings are interesting and novel. The work represents one of the earliest works studying Ferroptosis in tooth morphogenesis. There are several minor concerns.

1) The abstract is too long and should be shortened.

We modified the abstract to make it concise.

2) Can the Gpx4 quantitatively be measured by qRT-PCR?

3) How is Gpx4 regulated during development? If unknown, the authors should discuss it at least

4) Are there any tooth developmental defects associated with ferroptosis? If there is one, the authors should discuss it.

Our research on Gpx4 expression in the tooth germ during development (Figure 1A) highlights a specific spatiotemporal pattern. This pattern suggests that bulk RNA sequencing of the tooth germ may not provide accurate insight into changes in ferroptosis-related genes.

The developmental role of Gpx4 had been studied even before the ferroptosis was formally described (before 2012). In situ hybridization indicated expression of Gpx4 in all developing germ layers during gastrulation and in the somite stage in the developing central nervous system and in the heart, which made Gpx4 (-/-) mice die embryonically in utero by midgestation (E7.5) and are associated with a lack of normal structural compartmentalization. Specific deletion of Gpx4 during developmental process were found to participate in the maturation and survival of cerebral and photoreceptor cell. Recent years, more ferroptosis related function of Gpx4 were discovered in neutrophil and chondrocyte of adult mice, in which specific deletion will lead to ferroptosis-induced organ dysregulation and degeneration.

At present, no systematic study has been conducted on ferroptosis or ferroptotic stress in relation to tooth developmental defects. However, as early as the 1930s, pioneering dental biologists had already identified the presence of iron in the teeth of various animals. They also found that some enamel defects in mice were related to abnormal iron metabolism. Lipid metabolism and lipid peroxidation, which are other key risk factors of ferroptosis, were also described in the initial stages of dental biology research.

We are currently generating transgenic mice with dental epithelium/mesenchymal specific deletions of Gpx4. This will allow us to further investigate the developmental defects related to ferroptosis and ferroptotic stress.

Author Response

Reviewer #1 (Public Review):

The authors performed an RNAi screen to identify epigenetic regulators involved in oxygen-glucose deprivation (OGD)-induced neuronal injury using immortalized mouse hippocampal neuronal cell line HT-22. They identified PRMT5 as a novel negative regulator of neuronal cell survival after OGD. Both in vitro and in vivo experiments were then performed to evaluate the roles of PRMT5 in OGD and ischemic stroke-induced injury. The authors found that genetic and pharmacological inhibition of PRMT5 protected against neuronal cell death in both in vitro and in vivo models. Furthermore, they found that in response to OGD and ischemia, PRMT5 was translocated from the cytosol to the nucleus, where PRMT5 bound to the chromatin and promoter regions of targeted genes to repress the expression of downstream genes. Further, they showed that silencing PRMT5 significantly altered the OGD-induced changes for a large-scale of genes. In a mouse model of middle cerebral artery occlusion (MCAO), PRMT5 inhibitor EPZ015666 protected against neuronal death in vivo. This study reveals a potential therapeutic target for the treatment of ischemic stroke. Overall, the authors have done elegant work showing the role of PRMT5 in neuronal cell survival. However, the essential mechanisms underlying PRMT5 nuclear translocation have not been investigated, and the in vivo animal studies should be further strengthened.

Thank you very much for your comments and suggestions. While stroke stands as the second leading cause of death globally, and the burden of post-onset disability is substantial, particularly surging at a faster rate in low- and middle-income countries compared to high-income countries. The exploration of new drugs for stroke treatment holds profound societal implications. The concept of neuroprotective drug development is not novel; over the past half-century, considerable research and resources have been invested in this field. Yet, progress appears to be notably limited, and interest is currently waning.

Our research team is dedicated to devising rapid and cost-effective functional screening strategies grounded in the nervous system. Through this forward research approach, we aim to delve into potential neuroprotective targets across various neurological diseases. This endeavor not only bears significance for acute stroke but also holds potential application value for a spectrum of generalized nerve injuries.

Building on your insights, our upcoming studies will involve in vivo animal experiments, integrating the PRMT5 nuclear translocation mechanism. We anticipate that our continued research will benefit from further professional insights and guidance from your expertise.

Reviewer #2 (Public Review):

Haoyang Wu et al. have shown that the symmetric arginine methyltransferase PRMT5 binds to the promoter region of several essential genes and represses their expression, leading to neuronal cell death. Knocking down PRMT5 in HT-22 cells by shRNA leads to pertinent improvement in cell survival after oxygen-glucose deprivation (OGD) conditions. In another set of experiments, inhibition of the catalytic activity of PRMT5 by a specific inhibitor, EPZ015666, in a middle cerebral artery occlusion (MCAO) mice model also showed protective effects against neuronal cell death. In this manuscript, the authors have established the negative role of PRMT5 in cerebral ischemia both in vitro and in vivo.

However, my primary concern is the novelty of the manuscript. It has already been reported that inhibition of PRMT5 attenuates cerebral ischemia/reperfusion condition (Inhibition of PRMT5 attenuates cerebral ischemia/reperfusion-induced inflammation and pyroptosis through suppression of NF-κB/NLRP3 axis. Xiang Wu et al. Neuroscience Letters, Volume 776, 2022, 136576, ISSN 0304-3940, https://doi.org/10.1016/j.neulet.2022.136576.). Even these authors have also shown that treatment of PRMT5 specific catalytic inhibitor, LLY-283, could rescue ischemia-induced over-expression of inflammation-related factors.

However, it would be better to verify the specificity of the inhibitor, EPZ015666, using other methyltransferases to be sure that the rescue is indeed mediated by PRMT5 catalytic inhibition.

Thank you sincerely for dedicating time from your busy schedule to review our papers. Your comments and suggestions hold immense value for us, contributing significantly to the enhancement of our work. We acknowledge with honesty that this research journey has been a prolonged and challenging experience.

The major functional study, as indicated by the CHIP-seq data record, was concluded between 2017 and 2019. Since then, our efforts and resources have been devoted to conducting in-depth mechanism and regulation research for PRMT5. Notably, PRMT5 is involved in 4-5 types of histone arginine methylation, and it plays a role in complex modification effects for proteins in the cytoplasm. Despite employing a variety of investigative methods, understanding and controlling these intricate mechanisms in experimental design have proven quite challenging. This not only places us at a disadvantage compared to some competitors but also hinders the creative potential of our lab team.

We firmly believe that there is ample room for further research on the role of PRMT5 in the nervous system. We aspire to collaborate with other research teams to explore this area collectively.

Author Response

Reviewer #1 (Public Review):

Summary:

In this work, the authors use an OT setup to measure the DNA gripping and DNA slipping dynamics of phage lambda terminase motor interaction with DNA. They discover major differences in the dynamics of these two events, in comparison to the phage T4 motor, which they previously investigated. They attribute these differences to the presence of the TerS (small terminase) subunit of the motor complex of phage lambda in addition to the TerL (large terminase) subunit in phage, while in T4 only the TerL subunit is present. By exposing the stalled phage lambda procapsid-DNA complex (stalled with ATP-gammaS) to solutions containing 1) no nucleotide, 2) poorly hydrolyzed ATP, and 3) ADP, they found that the gripping persistence is strongest with ATP, weaker with ADP, and weakest with no nucleotide. This demonstrates nucleotide-dependent DNA gripping and friction of the motor. However, both persistence of gripping and friction are dramatically stronger than in the T4 TerL motor, due to the presence of the TerS subunit. While TerS was believed to be essential for the initiation of packaging in vivo, its role during DNA translocation was unclear. This study reveals the key role played by TerS in DNA gripping and DNA-motor friction, highlighting its role in DNA translocation where TerS acts as a "sliding clamp".

The study also provides a method to investigate factors affecting the stability of the initiation complex in viral packaging motors.

Strengths:

The experiments are well carried out and the conclusions are justified. These findings are of great significance and advance our understanding of viral motor function in the DNA packaging process and packaging dynamics.

Weaknesses:

While the collected OT data is quantitative, therefore is no further quantitative analysis of the motor packaging dynamics with regard to different motor subunit functions and the presence of nucleotides.

We thank the reviewer for the feedback and we will address the additional recommendations in a revised manuscript. Regarding the comment about quantitative analysis of the packaging dynamics, we emphasize that the present study focuses only on analysis of the grip/slip dynamics in the absence of ATP, since we have already studied the packaging dynamics (DNA translocation dynamics) with ATP in prior studies (refs 34, 35, 39-43). Note that in the present paper we do relate the present studies to these prior studies (such as on p. 7-8 regarding the mechanism of DNA gripping/release during translocation, on p. 8 regarding the finding that the T4 motor (without TerS) exhibits more frequent slipping during packaging, and on p. 8-9 regarding the cause of pauses during packaging).

Reviewer #2 (Public Review):

Summary:

In their paper Rawson et al investigate the nanomechanical properties of the lambda bacteriophage packaging motor in terms of its ability to allow either the slippage of DNA out of the capsid or exerting a grip on the DNA, thereby preventing the slipping. They use a fascinatingly elegant single-molecule biophysics approach, in which gentle forces, generated and controlled by optical tweezers, are used to pull on the DNA molecule about to be packaged by the virus. A microfluidic device is then used to change the nucleotide environment of the reaction, so that the packaging motor can be investigated in its nucleotide-free (apo), ADP-, and non-hydrolyzable ATP-analog-bound states. The authors show that the apo state is dominated by DNA slippage which is impeded by friction. The slippage is stochastically halted by gripping stages. In ADP the DNA-gripped state becomes overwhelming, resulting in a much slowed DNA slippage. In non-hydrolyzable ATP analogs, the DNA slippage is essentially halted and the gripped state becomes exclusive. The authors also show that the slipping and gripping states are controlled not only by nucleotides but also by the force exerted on DNA. Altogether, DNA transport through/by the lambda-phage packaging motor is regulated by nucleotides and mechanical force. Furthermore, the authors document an intriguingly interesting DNA end-clamping mechanism that prevents the DNA from slipping entirely out of the capsid, which would make the packaging process inefficient even on the statistical level. The authors claim that their findings are likely related to the function of a small terminase subunit (TerS) in the lambda-phage motor, which may act as a sliding clamp.

Strengths:

Altogether this is a very elegantly executed, thought-provoking, and interesting work with numerous significant practical implications. The paper is well-written and nicely documented.

Weaknesses:

There are really no major weaknesses, apart from a few minor issues detailed below in my recommendations.

We thank the reviewer for the feedback and we will address the minor issues in a revised manuscript.

Author Response

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

We have substantially revised our manuscript based on the extensive and highly constructive comments of the reviewers. We have included new data, refined existing data, and revised the text. To do this, some figures had to be split and several figures had to be renumbered. The additional experiments presented at the end of the Results also led us to expand our discussion of current limitations of our story.

Recommendations for the authors

Reviewer #1:

To improve the manuscript, I have some recommendations for the authors.

1) The cell size was quantified using flow cytometry (forward scatter). While this approach provides a convenient way to measure cell size, it is only a relative way to compare the cell size. A 10% increase in FSC value does not necessarily mean a 10% increase in diameter, this depends on the instrument. Consequently, the claims of density changes such as based on the panel 5B may be incorrect. It would be useful also to perform some experiments with Coulter Counter or imaging based quantification of cell size.

We agree and this is precisely why we had also measured cell diameters by imaging (reported at the bottom of page 7 and figure supplement 1D in the initial version of the manuscript). In the revised manuscript, we have added a cautionary note in the same context. Regarding density changes, those measurements by FRAP are independent of assumptions about cell diameter. When cell density is down and cells are larger by whatever factor, one can safely conclude that total protein did not scale.

2) When the Hsp90a/b KOs are introduced on page 9, it would be helpful to know at this stage whether the double KO cells are viable to understand why the individual KOs rather than double knockout cells were used.

We have now added a statement to indicate that total Hsp90 KOs are not viable in eukaryotes.

3) How the following can be reconciled with previous work is a bit unclear and needs some clarification: Neurohr et al 2019 identifies cytoplasmic dilution in larger cells, but in this manuscript WT cells maintain the same cytoplasmic density while becoming larger under chronic stress while the Hsp90 KO cells have reduced cytoplasmic density. Does this mean that the cytoplasmic dilution does not relate to cell size but is indirect and related to heat stress? Or is this related to uncoupling of cell size and density only in excessively large cells as for example HEK cells only increase their diameter by 30% based on the flow cytometry analysis?

Yes, indeed, beyond a certain threshold, excessively enlarged cells cannot scale protein anymore. In the revised manuscript, we not only look at cells exposed to stress for much longer (up to one month) (see last paragraph of revised Results). These cells become even bigger, and in agreement with Neurohr and colleagues, we find that protein scaling breaks down.

4) Related to the previous, the authors state that "Hsp90 levels rather than a specific isoform are critical for maintaining the cytoplasmic density", but there is no direct evidence connecting Hsp90 levels to cell size. Given the number of proteomics experiments done in this work, can a correlation between Hsp90 levels and cell size/cell density be identified? Or is this related to the way cell size is increased in chronic stress as later the authors say that with the CDK4/6 inhibitor Hsp90α/β KO cells can scale the total protein.

We have previously determined total Hsp90 levels quantitatively by mass spec (Bhattacharya et al., 2022; see Figure S8 there) (now explicitly mentioned in the same context as our revision related to point #2, see above), and we have now also added the quantitation, including that of total Hsp90 levels, in what is now Figure 9.

5) Page 17 states "Hsp90α/β KO cells increase cell size while translation is still reduced. Thus, cell size and translation must be coupled for adaptation to chronic stress." This feels like an important conclusion of the paper, yet the direct evidence is rather limited and the authors are clearly not sure how the Hsp90 KO cells increase their size without increasing the translational capacity. Yes, a potential explanation is provided immediately afterward as the authors show that Hsp90α/β KO cells subjected to chronic HS also have reduced proteasomal activity. Reducing protein degradation allows cells to gain more protein even if the synthesis rate does not increase (steady-state protein levels is a balance between synthesis and degradation). As stated by the authors in the discussion, the KO cells "fail to couple cell size increase to translation" simply because they can increase total protein, and cell size, by reducing protein degradation.

Yes, reducing protein turnover might be a viable strategy, but here, reduced protein degradation in the Hsp90 KOs is clearly not enough since total protein levels cannot keep up with the cell size increase.

6) What is unclear to me is to what extent these results (where chronic heat stress increases cell size and cells proliferate) relate to large senescent cells which are arrested. The discussion speculates that a failure to adapt to stress leads to aging, but direct evidence is lacking.

Even though we feel quite strongly that (some) speculation should be allowed, we now provide more direct evidence for senescence (see Figure 10 of revised manuscript and corresponding text). Moreover, we had already demonstrated in Bhattacharya et al. 2022 that senescence is triggered by below-threshold levels of Hsp90 (i.e. cells express senescence markers). But note that senescence is only manifest upon prolonged exposure to chronic mild stress, and that our standard protocol for chronic mild stress was established in such a way as to avoid much of an effect on viability and proliferation (see Figure 1). So no, at least for wild-type cells, except for the experiments of Figure 10, what we studied are not large senescent and arrested cells.

7) The clarity and content of the figures need some improvement. For example, in Fig 1, it is difficult to see the small symbols specifying the cell lines as the replicates are often overlapping. The font for p values is also too small. For Fig 2, legend says "the statistical significance between the groups was analyzed by two-tailed unpaired Student's t-tests." but there are no statistics shown. The use of statistical testing is also inconsistent across different figures and panels, for example Fig 3 A vs 3C and 5A vs 5H. In Fig 4. the legend talks about p-value, but y axis in panels is q value. The authors need to clarify this by mentioning that these are adjusted p values. Fig 7. should also explain "Rapa" in the legend or state "Rapamycin" in the figure.

To avoid overloading figures further with enlarged text, we prefer not to increase the font size of the p-values, and for graphs where data points are too small or overlap, we remind the reviewer that all original data will be available with the paper (and linked to from each figure). For Figure 2, we removed the indicated orphaned statement. We've now added stats for Figure 3C, and double checked all others; note that in most cases where the differences are really obvious, we did not add p-values. Wherever there were q-values as Y axis, we have now also added the term "adjusted p-value" in the legend. As for "Rapa", it was and still is defined in the legend.

8) The data in Fig 5A looks curious as the 39C response is bimodal suggesting that only some cells adapt to the heat stress or could this be a technical issue with the measurements?

The reason for this is that the data points are from 2 independent experiments. This means that the measurements were done on different days with a microscope that had to be calibrated again and may have been in a slightly different mode. This is not uncommon with this type of data. As an example of that, please see Fig. 3C of Persson et al. Cell 183:1572-1585 (https://doi.org/10.1016/j.cell.2020.10.017).

Reviewer #2:

Specific comments for authors:

Major comments:

1. Fig. 1F: if cells are not split for 7 days than they start growing in multi-layers. The density within a plate affects their proliferation rate as well as their translation rate. Therefore, a proliferation curve (with counting) when cells are kept for the duration of the 7 day experiment at sub-confluent density (ideally <90%) would be much more informative in this case, and also help to understand the dynamics within the timecourse. For example, if initially there is cell cycle arrest (at day1, as shown in Fig. 1d), then proliferation rates should reflect that.

See next point.

1. On a more general note: What is the confluence of the 4-7day experiments? Initial density can change the cell's behavior not only for RPE cells (as shown in fig. 7e), but HEK cells are sensitive to that as well. It is critical that experiments for translation, protein content, cell size, etc. be done in sub-confluent conditions, as the over-confluency alone could be a confounder for cell size, translation rates, etc. If this is indeed the way it was done, this should be clarified. Otherwise, this is a critical confounder which should be eliminated.

The risk of the confounding effects of overcrowding is indeed an important point, which we avoided, unfortunately without explicitly mentioning it in the manuscript (assuming that it went without saying). While we had already mentioned the seeding density and type of plate in Materials and Methods, we now address it explicitly both with additional data (new figure supplement 1B) and clarifying additions in the text. In our experience, the most common problem with confluent plates is not that cells grow on top of each other, but that they come off the plate and die. Regarding the cell cycle analysis of Fig. 1D and the proliferation assays of Fig. 1G, note that in the latter, we standardized cell numbers to those of day 1.

1. The speculations about the link to aging and senescence are very interesting, however since these are only hypothesis at this stage, the current phrasing in the abstract is a bit misleading. In fact, I was expecting at least one experiment to deal with aging/senescence, primed by the abstract.

You are perfectly correct. We have now added new experimental evidence that shows cells display activity of the senscence marker SA-βgal after prolonged chronic stress (Figure 10). Please see our response to point #6 of reviewer #1 for further comments.

1. Fig. 2D - nuclei are also getting much larger - what is the contribution of the nuclear increase to the overall cell increase? Does it scale linearly? Or does it contribute more/less compared to the entire cell?

Good point! We now include additional data on nuclear size in Figure 2E and figure supplement 2D, and corresponding additions in Results and Discussion. And as you correctly spotted, nuclei become bigger, too. The data suggest that the ratio of cytoplasm to nuclear size is more or less maintained. One can speculate that nuclei are larger because of partial "unfolding" (opening) of chromatin, which might very well be driven by the activation of Hsf1. But that's for future studies to figure out.

1. Fig 3a-c: in fig. 2a it looks like the knockout of one isoform leads to a basal increase in the expression of the other. However, since different antibodies are used for alpha and beta, the question of whether this increase leads to complete compensation of the total levels of hsp90 cannot be answered. qPCR for common regions could help answer this question, and this could help explain the increased hsf1 activity in the knockouts.

As pointed out in response to reviewer #1, point #4, we had previously determined total Hsp90 levels quantitatively by mass spec (Bhattacharya et al., 2022; see Figure S8 there), and we now mention that explicitly. Moreover, we have now added new data including the quantitation of total Hsp90 levels in Figure 9. RT-PCR might not be of much help considering that we had shown in Bhattacharya et al. 2022 that below-threshold Hsp90 levels (even less than what happens here) trigger translation through an IRES in the Hsp90β mRNA, whose levels don't change.

1. What is the HSE-luc construct used for the hsf1 activity? Is that an artificial HSE? Or the Hspa7 promoter? It would be interesting to check the activity with respect to the hsp90 promoter using a similar assay, to understand whether cells compensation for overall reduction in hsp90 levels is the primary "goal" for hsf1 activation.

The HSE-luc reporter is an artificial construct (we now clarify this in the Materials and Methods). Although Hsp90 is important, Hsf1's goal in life goes well beyond it. It notably also regulates lots of genes in the absence of stress, notably in cancer cells. Fig. 4B is an example of a blot that shows that chronic stress does not dramatically affect the levels of Hsp90α/β.

1. The proteomics data are very interesting, however additional details are missing and it is hard to extract them from source data 1. Specifically - focusing on the 2 hsp90s, what do they look like? The compensation questions above could be answered using the proteomics data as well.

As mentioned above in response to this reviewer's point #5 (and #4 of reviewer #1), we have previously addressed that in a paper that was focused on precisely this issue, and we have adapted the current manuscript accordingly.

1. How many proteins go up/down in the proteomics data? How does this compare between WT and knockout cells? The authors should detail the specific differences, which pathways? Which proteins? otherwise the volcano plots alone, on their own, are really not informative.

We have now added a GO analysis (Figure 5C), and heat maps for chaperones/co-chaperones and Hsp90 interactors (new figure supplements 4 and 5). We have still left some volcano plots because they are a good visualization of the overall changes. The text has been revised accordingly, notably also to clarify what we are trying to show with volcano plots (GO analysis and heat maps).

1. Fig. 3f: cells with hsf1 knockdown even decreased in size after HS. Is this significant? Why could that be?

The be honest, we do not know. A wild speculation would be that Hsf1 is not only required to drive the cell size increase, but that a certain minimal level of Hsf1 is required to maintain normal cell size (specifically in A549 cells?).

1. The siHSF1 cells showing no change in cell size is central to the paper's claims. This should be done in HEK293 cells at least, for which much of the data in the paper is shown, preferably also in RPE1 cells.

We have now added new data with the results obtained with HEK293T cells (Fig. 3F).

1. Technical note: it is very strange that MAFs can be transfected for luciferase assay. Such primary cells, to my knowledge, are largely non-transfectable. How was transfection performed in these cells? The authors should show that these cells can be transfected using imaging, or give a reference.

We did both. We gave references and the experimental details in Materials and Methods, but we now say it even more explicitly in there. Note that the transfection efficiency is not so critical in luciferase assays as one only reads out the activities of the transfected cell population.

1. The claim that proteostasis remains intact and the complexity of the proteome is unchanged should be examined more quantitatively. Specifically, analysis directly comparing between WT and KO cells should be performed: are the induced and repressed proteins the same? Is there a correlation between the levels of significantly changed proteins between WT and KO cells? This analysis should be done for chaperones, hsp90 interactors, as well as for the total proteome. Additionally, proteins whose levels differ could suggest (additional) mechanisms underlying the effects.

This comment also relates back to point #8. We hope that our newly added comment in the Results section associated with the new heat maps makes it clearer what purpose the proteomic data serve and that it is beyond the scope of this paper to quantitate differences further or to home in on this or that protein (with the exception of those proteins we have done immunoblots for). To go deeper into mechanisms is going to be a full project(s) in itself.

1. "Surprisingly, we found that Hsp90α/β KO cells do even better than WT cells under basal conditions (37{degree sign} C) (Figure 4D)." This is not so surprising, in light of the fact that HSF1 activity in these cells is higher, thus their chaperoning capacity should be better (for example, more HSP70 present?), as the authors themselves point out later in the text.

It is surprising considering that there is less of a major molecular chaperone. It's definitely not the first thing you suspect when you knock out Hsp90. But to avoid confusion, we have taken out "surprisingly" and reworded the statement.

1. "Similarly, Hsp90α/β KO cells might do better than WT cells under chronic HS because of their ability to further increase the levels of other molecular chaperones, such as Hsp27, Hsp40, and Hsp70, during chronic HS." This relates to the point above - the authors can directly quantify the changes in the levels of all other chaperones, since they have the proteomics data, and substantiate these claims, which are now only suggestions.

The subordinate clause ("... because...") is not a speculation, it is a statement based on the data (Fig. 4B and figure supplement 4A-B, and yes, of course, the proteomic data). However, that KOs indeed do better because of that remains to be proven (hence, the "might do better").

1. In A549 cells, knockout of Hsp90 led to lower basal diffusion coefficient (proxy for cytosolic density) at normal temperatures. Then, at 40 degrees, it seems that the coefficient goes back to being more or less equal to that of WT cells (fig. S5D). How can the authors explain this?

One cannot really compare them one on one. After all, the Hsp90 KOs are different cell lines, their EGFP expression levels may differ, and their heat sensitivity definitely differs. What can be compared is cells of a given cell line (i.e. WT or KO), transfected as a pool and then split to be cultured at different temperatures.

1. P-eIF2alpha and other translation marker western blots should be repeated and quantified and in also performed in A549 KO cells. The latter is very important, as the changed in A549 WT cells during adaptation of all translation regulatory markers: p-eIF2alpha, p-mTOR, and most strikingly total mTOR, are sky-rocketing, while in HEK cells these remain constant. As mTOR is a well-known regulator of cell size, and a target of Hsp90, could it be the major mediator of this effect in A549 cells? And if so, what is the substitute in HEK cells?

We now include bar graphs with quantitation of multiple experiments for both HEK and A549 cells, including for the KOs (Figure 6C-D - figure supplement 8). What they show is that p-mTOR levels increase during chronic stress. But since overall it also increases in Hsp90α/β KO cells, we had to conclude that this cannot explain the differences between cells of different genotypes. We have added a statement to that effect in the corresponding Results section.

1. Figs. 5D (and S5F) are both for HEK cells, while Fig. 5H is for A549. The corresponding plots for both cell lines should be provided for clarity, as the magnitudes in 5D and S5F seem much larger in HEK cells than seen in 5H. If there are differences between the cell lines these should be pointed out, as currently, showing some figures for one and not the other is confusing.

HEK and A549 cells in these experiments, which are different, serve different purposes. We now explicitly mention already in the text of the Results, which cell line is used. Hopefully that makes it less confusing.

1. Fig. 6C lacks a pvalue.

It's missing because it cannot be calculated. The graph shows the average of "only" 2 biologically independent samples (as stated in the legend).

1. Fig. S6C - the legend doesn't match the figure. Additionally, #aggregates should be normalized to the respective #of cells in each micrograph, and p-values should be presented for those normalized values.

For what is now figure supplement 9C, this has been fixed as suggested.

1. Also, under non-HS conditions, Hsp90 knockout cells show less aggregates than the WT. Is this significant (numbers are small, so perhaps it isn't)? What does this mean for the basal proteostasis state of Hsp90 knockout cells? Is it perhaps better than that of the WT?

The suggested way of quantitating the aggregates took care of that. There is no clear difference anymore between WT and KO, but clearly many more aggregates under chronic stress (figure supplement 9C).

1. The data on the connection between size and survival under chronic stress is highly compelling, even though correlative. The authors speculate in the discussion about one possible explanation to the question of how the enlarged size protect from the chronic stress. In fact, their proteomics dataset has the potential to help address, at least in part, their hypothesis about thresholds of certain proteins, by saying which proteins cross the detectability threshold in the data, and which processes these relate to.

What the proteomic data say is that most things don't change (standardized to total protein). While it is possible that a few proteins do change in interesting ways, characterizing those is beyond the scope of this study.

1. Fig. 7G should have a respective quantification with a p-value.

We have added additional data. What is now Fig. 9 shows the quantitation of multiple biological replicates (with p-values).

Minor comments:

1. "it is known that acute HS causes ribosomal dissociation from mRNA, which results in a translational pause (Shalgi et al., 2013)." - This paper showed that acute HS causes ribosomal pausing on mRNAs, not ribosomal dissociation.

We corrected this.

1. Fig. 7E - size bar is missing.

It was actually there, but hard to see. We have improved that in what is now Fig. 8E (and it is now also mentioned in the legend).

Reviewer #3:

My main points are outlined in the Public Review. Only a few additional comments are included here:

1. The manuscript is quite long and there are places where it could be shortened and tightened for clarity. I'd recommend going through carefully and trying to shorten to improve readability.

We hope that our revisions to address all of the reviewers' comments (and to accommodate more data) make the text more readable. But to make it shorter would have come at the expense of clarity.

1. It wasn't clear to me that the increased luciferase folding in HSP90 KO lines was surprising. It is demonstrated that knockdown of these isoforms can activate HSF1, which increases many chaperones known to promote luciferase refolding.

We address this point in our response to point #13 of reviewer #2 (basically: we took out "surprisingly").

1. Along the same lines. HSP90 knockdown activates HSF1, but doesn't induce basal cell size. However, exogenous overexpression of HSF1 or activation of HSF1 with capsaicin increase cell size. Why are similar things not observed for HSP90 knockdown? Is it the extent of HSF1 activation? This seems a bit unlikely because it looked like activation was similar in KO and capsaicin treated cells.

This must be due to the specifics of these different assays. The levels of Hsf1 protein and activity, and the time course of Hsf1 activity may be different. Moreover, it is likely that the reporter gene readout does not accurately report on all Hsf1 activities at a genome-wide scale.

1. As noted above, does HSP90 depletion impact ISR signaling induced by other types of stress (e.g., ER or mitochondrial stress). Specifically, do you see sustained translational attenuation (and eIF2a phosphorylation) when HSP90 is depleted under these conditions. In other words, does HSP90 have a specific role in globally resolving eIF2a phosphorylation as part of the ISR or is that specific to certain types of stress.

Although we now include data to show that tunicamycin (and therefore presumably the UPR/ISR) also induces a cell size increase, comprehensively analyzing what we refer to as RSR across different types of stresses (including mitochondrial and ER stresses) in the background of different Hsp90 genotypes and cell lines goes well beyond the scope of the current study.

Author Response

Reviewer #3 (Public Review):

The authors sought to directly compare the predictions of two models of somatosensory processing: The attenuation model, which states that the sensation of touch on one hand is reduced when it is the predictable result of an active movement by the other hand; and the enhancement model, which states that the sensation of touch is actually increased, as long as the active hand does not receive touch stimultaneously with the passive hand (no double stimulation). The authors achieved their aims, with results clearly demonstrating (1) attenuation in the case of self touch, (2) that previously-observed enhancement is a consequence of the comparison condition (false enhancement), and (3) that attenuation involves predictive mechanisms and does not result simply from double stimulation. These findings, and the methodology, should particularly impact future studies of perceptual attenuation, sensory prediction error, and motor control more generally. The opposite conclusions obtainable by selecting different comparison conditions is particularly striking.

Experiment 1 affirms that a touch to the passive finger caused by the active finger tapping a force sensor is perceived as weaker (attenuated) compared to a baseline not involving the active finger, but that if double stimulation is prevented (active finger moves, but no contact), neither attenuation nor enhancement occurs. Experiment 2 includes the three original conditions, plus the no-go condition used as a comparison in these earlier studies. Results suggest that the comparisons used by previous studies would result in the false appearance of enhancement. Finally, Experiment 3 tests the hypothesis that the lack of attenuation in the no-contact condition is due to the absence of double stimulation rather than predictive mechanisms. When contact and no-contact trials were mixed in an 80:20 ratio, such that participants would form predictions about the consequence of their active finger movement even if some trials lacked contact. In this case, attenuation was observed for both contact and no-contact trials, supporting the idea that attenuation is related to predictive processes linked to moving the active finger, and is not a simple consequence of double stimulation.

The methodology and analysis plans for all three experiments were pre-registered prior to data collection. We can therefore be very confident that the results were not influenced by hypotheses developed only after seeing the data. The three experiments were each performed in a new set of participants. Experiments 2 and 3 included conditions that replicated the Experiment 1 effects, allowing us to be very confident that the results are robust.

While the study has significant strengths, some aspects of the interpretation need to be clarified. In particular, the authors' interpretation depends on the idea that attenuation is absent in the no-contact condition because this action-sensory consequence relationship is an "arbitrary mapping." It is not clear what makes it arbitrary. The self-touch contact condition could also be considered somewhat arbitrary and different from real self-touch; the 2N test force was triggered by the right finger tapping a force sensor. If participants' tapping forces were recorded, it would be useful to include this information, particularly about how variable participants' taps were. In other words, unlike real self-touch, in this paradigm the force of the active finger tap did not affect the force delivered to the passive finger.

By ‘arbitrary’, we refer to nonecological mappings between a movement and a somatosensory stimulus. In other words, a mapping that does not resemble how one touches their body (natural self-touch). Examples of such arbitrary mappings are moving the right finger in the air and receiving simultaneous touch on the other hand, as in Thomas et al. (2022), or moving a joystick or potentiometer with one hand and receiving a touch on the other hand. These joystick or potentiometer conditions are typically used as a control condition when studying somatosensory attenuation because they include an arbitrary sensorimotor mapping (Shergill et al., 2005, 2003; Teufel et al., 2010; Wolpe et al., 2016).

We understand the reviewer’s point about the relationship between the forces applied with the right hand and the forces received on the left hand. First, we would like to clarify that we recorded the forces that the participants applied to the sensor in every experiment. We have now added a figure (Figure 3 – figure supplement 3) showing the forces over time across all participants in every experiment, which is referred to in the Methods on Lines 727-730. As we wrote in the Methods (Lines 720-727), and in line with previous studies (Asimakidou et al., 2022; Kilteni et al., 2021; Kilteni and Ehrsson, 2022), we asked participants to tap, neither too weakly nor too strongly, with their right index finger, “as if tapping the screen of their smartphone”. We did so because participants do not have an intuitive sense of how strong a force of 2 N is, and this instruction allowed them to apply forces of similar magnitude from trial to trial while receiving the same touch on their left index finger. Indeed, as shown in Figure 3 – figure supplement 3 (D-F), participants showed low trial-to-trial variability in the applied forces, with an average variability (s.e.m.) of only ± 0.13 N in Experiment 1, ± 0.12 N in Experiment 2 and ± 0.11 N in Experiment 3. In other words, they generated similar forces with their right index finger across all trials while receiving the same force on their left index finger, establishing an approximately constant gain between movement and touch and a perceived causality between the two (Bays and Wolpert, 2008; Kilteni, 2023). Critically, Bays and Wolpert (Experiment 1 in that book chapter) previously showed that the magnitude of attenuation remains unaffected when halving or doubling the gain between the force applied by the active finger and the force delivered on the passive hand as long as the gain remains constant throughout the experiment (Bays and Wolpert, 2008). This should not be surprising given that when one finger transmits a force through an object to another finger, the resulting force also depends on the object's properties (e.g., shape, material and contact area) and the angle at which the finger contacts the object. This is outlined in Lines 733-736 of the manuscript.

One additional potential weakness is that participants' vision was occluded in Experiment 3, but not in Experiments 1 and 2. The authors do not discuss whether this difference could confound any of the analyses that compare results across experiments.

We thank the reviewer for the comment. We do not think that blindfolding is a weakness of our study, as we designed our experiment to take this factor into account. Specifically, we blindfolded participants to ensure that they would not know when the force sensor was retracted on (unexpected) no-contact trials. This was essential for establishing an expectation that they would contact the force sensor. Importantly, participants were blindfolded in all conditions of Experiment 3 (contact, no-contact and baseline), so any effect of blindfolding was present across all conditions of Experiment 3. Since in the analyses of Experiment 3 (Lines 342-354), we always compared between conditions, blindfolding per se could not explain any differences between conditions, as any putative effects of blindfolding are effectively removed when contrasting two conditions in which participants were blindfolded. Notably, this argument also applies to the comparisons that we made between Experiment 3 and Experiments 1 and 2, since all these analyses (Lines 362-376) compare the difference between contact and no-contact trials (e.g., PSE values) between the experiments. Once again, any putative effects from blindfolding were effectively removed. We should also emphasize that the participants’ left index finger as well as the motor that delivered the force to their left index finger were occluded from view in Experiments 1 and 2. This was done to prevent participants from using any visual cues to discriminate between the two forces. This is has been included in the Methods section (Lines 772-775).

In conclusion, blindfolding cannot explain the results of Experiment 3, and it did not alter the interpretation of any of our results derived by comparing the experiments. We have clarified this point in the manuscript (Lines 823-827).

Author Response

Reviewer #1 (Public Review):

In this manuscript the authors perform a detailed analysis of the impact of food type on reproduction in C. elegans. They find that, in comparison with the standard OP50 strain of E. coli that is ubiquitously used to maintain C. elegans in the laboratory setting, the CS180 strain results in a reduction in the number of progeny that may be a consequence of an early transition from spermatogenesis to oogenesis that reduces total sperm number. They also find that the rate of oocyte fertilization is increased in animals fed CS180 vs. OP50. Using mutants and laser ablations, the authors show that, whereas the insulin-like peptide INS-6 acts in the ASJ sensory neurons to mediate the food type effect on total progeny and early oogenesis, the increased fertilization rate phenotype does not require ASJ or insulin-like signaling and instead requires the AWA olfactory neurons.

The major strengths of the manuscript are the establishment of INS-6 as a link between food type and reproduction and the detail and rigor with which the experiments were executed. The results presented generally support the authors' model. This role of insulin-like signaling in connecting food type and reproduction makes it a plausible target for evolutionary forces that may have shaped insulin-like signaling in invertebrates. As such, this work contributes broadly to our understanding of how insulin signaling may have evolved prior to the emergence of vertebrates.

We thank the Reviewer for these nice comments.

A weakness of the work is the epistasis analysis of insulin-like pathway components, which is incomplete and at times difficult to interpret.

We conducted an epistasis analysis between ins-6 and daf-16 with regard to early oogenesis onset on the CS180 diet. Through recombination of lin-41::GFP with the daf-16 deletion mutation on chromosome I, we showed that daf-16 mutants exhibit early oogenesis at mid L4 on CS180 (Figure 5C and F), which is unlike the ins-6 deletion (null) mutants or the reduction-offunction mutations in daf-2. Both ins-6 and daf-2 mutants exhibit delayed oogenesis on CS180 (Figure 5B, D, and F). Interestingly, the delayed oogenesis phenotype of ins-6 null mutants was not rescued by loss of daf-16, suggesting that wild-type ins-6 promotes early oogenesis independent of daf-16 (Figure 5F). This is reminiscent of the Arur lab’s findings, where daf-2 promotes germline meiotic progression independent of daf-16 in response to food availability (Lopez et al., Dev Cell 2013, vol 27, pp 227-240).

Reviewer #2 (Public Review):

The manuscript by Mishra et al. examines the modulation of the nervous system by different bacterial food to influence reproductive phenotypes-specifically onset of oogenesis, fertilization rate, and progeny production. Defining how animal reproduction could be modulated by bacterial food cues through neuroendocrine signaling is a fascinating subject of study for which C. elegans is well-suited. However, the overall scope of the current study is limited, and some of the central data do not provide compelling evidence for the authors' underlying hypothesis and model.

1) Two strains of E. coli are examined, the standard C. elegans bacterial food strain OP50 and an E. coli strain that Alcedo and colleagues have previously characterized to influence aging and longevity through nervous system modulation. While the authors determine that differences in LPS structure present between the strains does not account for the food-dependent effects, there is little further insight regarding the bacterial features that contribute to the observed differences in reproductive physiology. Moreover, at least two of the phenotypes examined-total progeny and fertilization rate-are known to be affected by bacterial food quality and may be affected by bacteria in many ways, so the description of these phenotypes is somewhat less compelling than the study of the onset of oogenesis.

Our study focused on how specific sensory neurons mediate the effects of different bacterial diets on three different aspects of C. elegans reproductive physiology—total progeny, oogenesis onset and fertilization rates. We examined the effects of three different bacteria, E. coli OP50, CS180 and CS2429, on these three phenotypes and the effects of two Serratia marcescens strains, Db11 and Db1140, on oogenesis onset. Of these five bacteria, only CS180 and its derivative CS2429, promote early C. elegans oogenesis.

In the revised manuscript, we included the effects of a fourth E. coli strain, the K-12 HT115 on total progeny (Figure 2—supplement 1), oogenesis onset (Figure 2E) and fertilization rates (Figure 2F). We found that HT115 does not elicit the same response as CS180 on oogenesis onset and fertilization rates. Thus, the oogenic-inducing and fertilization-enhancing cue(s) appear to be specific to CS180 and its derivative CS2429. We started characterizing the potential nature of these CS180-derived cue(s). So far, we found that these cues are unlikely to be free, small metabolites, since they were lost upon filtration of the CS180-conditioned LB media through a nylon membrane that has a pore size of 0.45 µm (Figure 2G and H). While we agree with the Reviewer that the identification of these cues are important, we believe that it is beyond the scope of this manuscript.

More importantly, we showed that the sensory neuron ASJ does modulate the timing of oogenesis and that this involves the insulin-like peptide ins-6 (please see our responses to the Essential Revisions section and Figures 5 and 6). We also showed that ASJ (Figure 7G and K) or ins-6 (Figure 8D) does not affect the food type-dependent fertilization rates, which are modulated by a different sensory neuron, the olfactory neuron AWA (Figure 7J and K). AWA in turn has no effect on the timing of oogenesis (Figure 7L). Thus, this manuscript links specific sensory neurons and insulin-like peptides to distinct aspects of oocyte biology, which we believe is a significant advance in the field of reproductive biology.

2) The onset of oogenesis phenotype, using the lin-41::GFP reporter, seems more specific and tractable, and the authors nicely decouple this phenotype from the total progeny and fertilization rate phenotypes through experiments that shift animals to different bacterial food at specific developmental stages.

We thank the Reviewer for this comment.

However, as it stands, the data regarding the role of ins-6 and ASJ in modulating this phenotype, and the model that exposure to CS180 bacterial food causes a change in the ASJ expression of ins-6, which is sufficient to promote the earlier onset of oogenesis at the mid-L4 stage, seems somewhat incomplete and have some inconsistencies to be addressed.

a) The ins-6 mutant phenotype is rescued by genome ins-6 and partially rescued by ins-6 expressed under and ASJ-specific promoter. The lack of rescue from an ASI promoter is puzzling given the secreted nature of ins-6.

We address this in Essential Revisions, point 3. Briefly, we disagree that this is puzzling, since several labs have already shown that there are functional differences between the INS-6 produced from ASI versus the INS-6 produced from ASJ, using different experimental approaches (Chen et al., 2013; Tang et al., 2023; and this work). Indeed, the cell-specific activities of a secreted signal is not limited to INS-6, but has also been described for other secreted peptides, such as INS-1 (Kodama et al., 2006; Tomioka et al., 2006; Takeishi et al., eLife 2020, vol 9, e61167. Thus, the interesting question is why functional differences exist between the INS-6 peptides from the two neurons. This is a fascinating question, but beyond the scope of this manuscript.

b) The ins-6 mutant phenotype with regard to delaying the early expression of lin-41::GFP on CS180 appears weaker than the daf-2 mutant phenotype. This is difficult to reconcile with what is known about the relative strength of the daf-2 mutant alleles relative to ins-6 for a wide range of phenotypes.

There are evidence in the literature that the ins-6 mutant phenotype will not look exactly like that of daf-2 (Chen et al., 2013; Cornils et al., Development 2011, vol 138, pp1183-93; Fernandes de Abreu et al., PLoS Genet 2014, vol 10, e1004225). The DAF-2 insulin-like receptor is predicted to bind multiple insulin-like peptides (Pierce et al., Genes Dev 2001, vol 15, pp 672-686), some of which can act antagonistic to DAF-2 function (Pierce et al., 2001; Cornils et al., 2011; Chen et al., 2013; Fernandes de Abreu et al., 2014). Thus, the oogenic effects of the reduction-offunction mutations in daf-2 are likely the sum of multiple insulin-like peptides, some of which might also delay oogenesis. This could explain why the manipulation of an individual insulin-like peptide, INS-6, which could bind DAF-2 to promote oogenesis, does not closely resemble the phenotype of daf-2 mutants.

c) The daf-16 loss-of-function phenotype and suppression of daf-2 and ins-6 mutant phenotypes are not shown for the lin-41::GFP expression phenotype.

We address this in the Public Review comments of Reviewer 1. Briefly, we focused on the epistasis analysis between ins-6 and daf-16 and showed that ins-6 promotes early oogenesis independent of daf-16.

d) The modest difference in ins-6p::mCherry expression in the ASJ neurons (Figure 5D) make the idea that this difference causes onset of oogenesis somewhat implausible.

We disagree that this change is modest and that the oogenic effect of such a change is implausible.

First, the change in ins-6p::mCherry expression in ASJ on CS180 is comparable to other physiologically-important expression changes that have been reported for other genes (for example, Entchev et al., eLife 2015, vol 4, 4:e06259, for the tryptophan hydroxylase tph-1 and the TGF-β daf-7; and Tataridas-Pallas et al, PLoS Genet 2021, vol 17, e1009358, for the neuronally expressed NRF transcription factor skn-1b). Second, it is worth noting that we were using a single-copy reporter for ins-6 expression, where detected changes will be smaller but should be closer to physiological responses. It is possible that multiple-copy reporters will give larger changes, but that would be further from a physiological response. Third, the change in ins-6p::mCherry expression is comparable in scale to the ins-6 mutant phenotype. Our results showed that the 35% increase in ASJ expression of ins-6 is due to food type (Figure 6A; mean fluorescence on OP50 = 1526 + 94; mean fluorescence on CS180 = 2056 + 104). This change in magnitude is similar to the loss of lin-41::GFP expression in mid L4 of ins-6 mutants versus controls. About 30% to 43% of control worms express lin-41::GFP, whereas 0% of ins-6 mutants express the same reporter at mid L4 on CS180 (Figure 5 and its associated supplement).

e) The strain carrying an genetic ablation of ASJ appears to have a markedly different baseline of kinetics of lin-41::GFP expression (even at lethargus, less than half of the animals appear to express lin-41::GFP). Given this phenotype, it seems difficult to draw conclusions about bacterial food-dependent effects on expression of lin-41::GFP. Additional characterization corroborating timing of oogenesis independent of the lin-41::GFP marker may be helpful, but something seems amiss.

We address this in Essential Revisions, point 4. Briefly, we disagree that the kinetics of lin-41::GFP expression in ASJ-ablated animals is puzzling, compared to the kinetics observed in insulin signaling mutants. Besides ins-6, ASJ expresses multiple signals (Taylor et al., 2021), some of which might also regulate the multiple functions of oogenic lin-41::GFP. Thus, it should not be surprising that loss of ASJ will have a markedly different effect on oogenesis than the loss of ins-6.

Reviewer #3 (Public Review):

I very much enjoyed reading this paper by Shashwat Mishra and team from Joy Alcedo's and from Queelim Ch'ng's laboratories dissecting how sensory signals regulate reproduction in worms. The mechanisms by which sensory inputs affect the function of the germline, the balance between growth and differentiation within this tissue, are of broad interest not only to those interested in reproduction and differentiation, but also to those interested in the mechanisms of plasticity that enable organisms to adjust to changing environmental conditions. These mechanisms are only now beginning to be characterized. Here the focus is on the role of insulin signals expressed in sensory neurons. This work builds on previous findings by the Alcedo lab that sensory perception of bacterial-type dependent signals regulates C. elegans lifespan. Here their focus is on the effects on reproduction, and on the communication of that information by insulin-like signals.

We thank the Reviewer for these nice comments.

Worms have a huge family of 40 insulin-like genes, which the Alcedo and Ch'ng labs have been studying for many years. The paper starts with the interesting premise that the brood size of the worms is food type dependent. The authors show that this is due to effects on the timing of the onset of oogenesis during larval development (which constrains the size of the pool of sperm available for subsequent oocyte fertilization) as well as on effects on the rate of oocyte fertilization during adulthood. Using clever timing for food switching, they show that the effects on oogenesis onset and on fertilization rate are separable. In addition, these effects did not appear to be merely the outcome of indirect effects of food ingestion, but were, instead, at least in part, due to the perception of environmental information by specific sensory neurons. Using mutants affecting transduction of sensory information in specific neurons and genetic ablation of specific neurons, the authors show that the onset of oogenesis and the rate of reproduction were controlled by different sensory neurons, ASJ and AWA, respectively. One of these neurons, ASJ, transmitted environmental information via the ins-6 neuropeptide.

Altogether, the paper advances our understanding of how environmental determinants influence reproduction.

We thank the Reviewer for these nice comments.

Author Response

Reviewer #1 (Public Review):

However, the authors are cautioned to tone down some of the sentences with the human diabetic samples as they rely heavily on extrapolation rather experimental tests.

Thank you for this feedback. We have added an experimental test to support the CellChat results. We found that, in accordance with the CellChat analysis, more macrophage Gas6 expression is observed in diabetic wounds via IF. These data are now included in Figures 3C-D. We have additionally edited the text relating to Figure 3 to indicate that these results are not fully conclusive.

For instance, the antibody inhibition of Axl had minimal effect on the clearance of apoptotic cells in the wound and this would be expected with the redundancy endowed by other TAM receptors.

Thank you for this point. We have made a note of this in the text in lines 289-291.

For instance, in Figure 6, the number of TUNEL+ cells seem to be higher in the IgG samples compared to the anti-Timd4 treatment, but this is not the case in the quantification

Thank you for this comment. We have replaced these with more representative images, which appear in Figure 6A. We also repeated the staining with antibodies for cleaved caspase 3, which appear in Fig. 6 – Fig. supplement 1A, which showed similar results.

Reviewer #2 (Public Review):

I suggest to repeat the quantification of cells containing active caspase-3 with an anticleaved caspase-3 antibody. Here the authors use an antibody recognizing phospho S150 antibody, which is far from generally accepted to be a marker for active caspase-3. It would also be good to quantify the apoptotic cells observed in the sections (Fig 1 I and J) and compare to control treatment on sections. It is not clear from the data presented whether the number of apoptotic cells increases or not in the time frame analyzed since the controls are lacking.

Thank you for this important suggestion. We have repeated the IF staining using an antibody for cleaved caspase 3 (Cell Signaling 9661S) and quantified the apoptotic cells present. We found that apoptotic cells were rare but present at both 24h and 48h after injury, and that significantly more cleaved caspase 3+ cells were present in 48h wounds than 24h wounds. These data are now included in Figure 1H-J and Fig. 1 – Fig. supplement 1F. We have also used this antibody in IF staining in Fig. 5 – Fig. supplement 1B and Fig. 6 – Fig. supplement 1A.

In a FACS analysis (Fig S1 H), the authors show that there is no increase in dead cells in a time frame of 48 hrs. Could it be that the majority of the cells that may have died in vivo, were lost during the procedure of tissue digestions. Dead cells tend to aggregate.

Based on these comments and the inconsistency in these data due to potential technical challenges, we have removed the FACS data quantifying Annexin V. We now include the quantification of cleaved caspase 3 and an efferocytosis assay to analyze the kinetics of efferocytosis.

On line 104 the authors refer to the apoptosis-inducing activity of G0s2. Please, realize that there is little or no in vivo evidence for a role of G0s2 in apoptosis.

Thank you for this helpful comment. We have removed this gene from our analysis and text.

The authors state that Axl is uniquely expressed in DC and fibroblasts (Fig 2). Are the Axlcells positive in panel G (red, Fig 2) that do not stain for the Pdgfra marker (green) then all DCs? Please clarify or show with a triple staining that these cells are indeed DCs.

Thank you for this comment. To clarify, our intention was to show that both DCs and fibroblasts express Axl, not to say conclusively that only DCs and fibroblasts express Axl. Indeed, in Figure 5, we show that a portion of macrophages also express Axl (at day 3), so some of the Axl+ cells in 2G may be macrophages rather than DCs. We have made this more clear in the text in lines 163-166.

In addition, it is not clear to me to what reference level exactly the expression levels are compared in Fig 2A. Is this between the 24 and 48h time points after wounding (as mentioned in the legend)? If so, the analysis may indicate up or down regulation but not necessarily expression or no expression.

Thank you for making this point. The heatmaps display scaled log-normalized mRNA counts for the entire dataset, not a comparison between the two timepoints. We have clarified this in the figure legends.

2) Human diabetic wounds display increased and altered efferocytosis signaling via Axl. This conclusion is solely based on CellChat analysis and should be tuned down or validated.

Thank you for this suggestion. We have experimentally validated this conclusion using IF staining for Gas6. We found that more Gas6 staining in CD68+ macrophages in diabetic foot ulcers when compared to nondiabetic foot wounds. These data are now included in Figure 3C-D.

The authors conclude that anti-Axl treatment leads to healing defects based on lack of granulation tissue and larger scabs, a reduction of fibroblast repopulation and revascularization. The differences in the last two parameters mentioned above are obvious, however the other parameters, as granulation tissue and scabs are less clear to me. Is this quantified in any way? In Fig S4 D there is also a large scab visible in the control treatment image. Therefore, it would be good if these parameters could be better substantiated.

Thank you for this comment. We have edited the text in lines 301-304 to de-emphasize these qualitative changes.

In view of the lack of revascularization, are there differences in the mRNA expression levels of angiogenic factors such as VEGF and others at this time point? Does revascularization occur at later stages?.

Thank you for this helpful suggestion. We have used qPCR to measure Vegfa mRNA expression, and these data are now included in Figure 5I. We found no significant difference in Vegfa expression 5 days after injury.

Based on the FACS analysis the authors claim that there are no differences at the level of DCs. However, the plots shown in Fig 5C do not convincingly show the detection of DC (as boxed in the lower panel). Based on the density plots one would presume this is just the continuation of the CD11b+ population and not a separate CD11c+ population. To get a better view of that, it would be better to show dot plots instead of density plots.

Thank you for this insightful comment. We have created new plots as suggested to demonstrate that this is not exactly the case. In the wound bed, contrary to what we see in blood isolates many times the full separation of populations is elusive and to ensure that we use single stain controls to set the gates. Nonetheless, we provide in Author response image 1 the same data as dot-plots as requested to show that that is not the case, alongside the single stain control to show that the gating strategy is adequate. We do understand and acknowledge that in dissociated tissues sometimes the outlines are not as perfect as what is obtained in immunological samples.

Author response image 1.

Finally, the authors state (line 265-266) that anti-Axl treatment leads to non-significantly increased expression of IL1alpha and IL6 after one day of injury (Fig S4C). If the difference between the control-treated and the anti-Axl-treated group is statistically not significant I would not conclude there is an increase. Please adapt phrasing or include more mice in the experiment (now only 4) to substantiate the observation and clarify whether it is increased or not.

Thank you for this comment. We have altered the text in lines 286-289 to better reflect this.

The authors conclude that overall healing was not affected but that the wound beds appeared more fragile. What is meant with 'appeared more fragile' is not clear. In addition, this seems to me a quite subjective interpretation. What are the objective parameters to come this conclusion?

Thank you for this point. We have altered the text to remove this subjective language.

Similar to inhibition of Axl, inhibition of Timd4 led to a defect in revascularization as witnessed by the absence of CD31 staining. Also in this experiment one can raise similar questions as in the anti-Axl experiment: 1) does revascularization occur at a later timepoint; 2) what about the expression of angiogenic factors?

Thank you for this helpful suggestion. To further investigate the impact of Axl inhibition of angiogenesis, we have assayed for Vegfa by qPCR. We found no significant difference in Vegfa expression 5 days after injury. These data are now included in Figure 5I.

In the anti-Timd4 treated wounds the authors observe more TUNEL-positive cells and conclude that this is due to a defect in efferocytosis. However, the formal experimental proof for this in the current model is lacking. How do the authors exclude the possibility that anti-Timd4 treatment attracts more infiltrating cells that then undergo treatment, or that the treatment with anti-Timd4 leads to more apoptosis of certain cells in the wound bed. What is the nature of these apoptotic cells (neutrophils, T cells, others)? It has been shown that Timd4 can have stimulatory effects on other cells, such as T cells. Could deprivation of Timd4 signaling in certain conditions lead to more dying cells in this model?

Thank you for this insightful comment. To investigate this, we have repeated this experiment with IF staining for cleaved caspase 3 and found similar results, indicating the increase in apoptosis upon Timd4 inhibition (Fig. 6 – Fig. supplement 1A). We have also included text to acknowledge the possibility of an increase in apoptosis in lines 326-327.

Reviewer #3 (public Review)):

They never do show that there is an increase in apoptotic cells in the wounds, which then go down (which would be a sign that the cells are being cleared via efferocytosis. In addition, they are looking for apoptotic cells at very early time points (24-48 hours), times at which large numbers of apoptotic cells would not be expected. As an example, neutrophil infiltration peaks at 24-48 hours and efferocytosis of apoptotic neutrophils would be expected after that. Other types of apoptotic cells would likely be cleared even later. Finally, several of the panels showing apoptotic cells were done with a very small number of samples (1-3 per group) in some cases so it is unclear how rigorous the data are. I would recommend that the authors at the very least soften the wording related to these conclusions and discuss the limitations of their experimental design; ideally data from more samples would be included to provide clear support those statements.

Thank you for raising this important point. In order to support these claims, we have undertaken two additional experiments. Firstly, we have repeated the immunofluorescence staining with a new antibody for activated caspase 3 and quantified the number of apoptotic cells present in 24h and 48h wound beds. We found that apoptotic cells significantly increased in 48h wound beds compared to 24h wounds (Figures 1H and Fig. 1 – Fig. supplement 1F).

We have also undertaken a new experiment to show the temporal regulation of efferocytosis. We injected stained apoptotic neutrophils into 1D, 3D, and 5D wound beds and quantified the stained cells remaining after 1 hour in order to quantify the clearance of cells from the wound bed at different timepoints. We found that significantly more stained cells undergoing efferocytosis remained in 5D wounds, and that the rate of efferocytosis was approximately constant over this timeline. These data are now included in Figures 2H-M.

While we would be interested to determine the identities of cells engaging in efferocytosis of the labeled apoptotic neutrophils, we found that co-staining for additional cell markers was impossible while maintaining the fluorescent labeling on the injected neutrophils.

2) The human RNA-seq data is also quite limited, as non-diabetic wound tissue was all from one patient. Again, this limitation should be acknowledged.

Thank you for this feedback. We have analyzed new data sets that include 5 individuals with diabetic foot ulcers and 4 individuals with non-diabetic wounds. These data are now included in Figure 3.

Also, there are some important published papers by Sashwati Roy's group indicating that there are defects in efferocytosis in diabetic wounds, which may go against what the authors are showing here to some degree. Discussion of the authors' work in relation to these other studies should be discussed.

Thank you for this suggestion. We have included discussion of this work to the text in lines 192193.

3) For anti-Axl and anti-Timd4 experiments, the authors conclude that inhibition of Axl does not affect TUNEL+ cells and that Timd4 does not affect reepithelialization. However, in some cases the sample size was only 3 mice per group when measuring these parameters. That is a very small number of samples to draw conclusions about apoptotic cells or reepithelialization since these parameters are key for the overall conclusions of the experiments. Given that these are key data, it would be important to include more than n=3. Additionally, as stated above, a time point later than 24 h may be necessary to actually see changes in apoptotic cells.

Thank you for this suggestion. We have repeated the staining for apoptotic cells using a new antibody for cleaved caspase 3 and stained wound beds from additional mice. In the anti-Axl experiments, we now show data for cleaved caspase 3 staining of 3- and 5-day wound beds with N=4 (Fig. 5 – Fig. supplement 1B). In the anti-Timd4 experiments, we now have N=6-11 for the TUNEL staining at 5 days after injection and injury (Figure 6B).

4) In Fig 6, there look to be many more TUNEL+ cells in the wound bed of IgG control samples compared to anti-Timd4-treated samples, which contradicts the graph. Perhaps the authors could clarify where they were taking their measurements for panels with image analysis results.

Thank you for this helpful point. We have updated this figure to be more representative of the quantification (Figure 6A-B), as well as repeated the staining with antibodies for cleaved caspase 3 (Fig. 6 – Fig. supplement 1A).

Another question related to this experiment is how it is possible that efferocytosis is so drastically different yet there are no changes in wound healing (this is one reason why a larger sample size for reepithelialization may be critical) - this would seem to suggest that efferocytosis is not important in wound healing, which is confusing. Further discussion on this might be useful.

Thank you for this point. Indeed, we see that there is a defect to revascularization when Timd4 is inhibited (Figure 6E-F), which indicates that efferocytosis is important to normal healing. This is discussed in lines 333-335.

Author Response

Reviewer #3 (Public Review):

Comment 1: I'm having some difficulty understanding the logic of Figure 5 in determining cis processing. It is an inverse of figure 4, and in my view, provides further evidence of trans processing. A better experiment would be to use WT-citrine tagged protein with catalytic dead mcherry and image them together. This would show WT cis processing occurs faster than trans processing as citrine specks should appear earlier than the mCherry ones. Can also do colocalization and FRET-based assays with the pair.

We thank the reviewer for pointing this out. While our data demonstrate that the same molecule must be catalytically active and competent for processing at the IDL (Figure 5), we agree that the data do not rule out trans-processing as a mechanism for speck formation. We have therefore modified the interpretation of these findings accordingly (pp. 7-8). We agree that some of the quantitative assays the reviewer has suggested would strengthen this logic, and we are making efforts to carry out a kinetic FRET-based assay for our upcoming biochemistry-focused manuscript to better characterize the enzymatic affinity of Casp11 for cis- vs. trans- based autoprocessing, and how either impacts Casp11 speck assembly.

Comment 2: Do those casp11 specks still contain CARDs?- i.e. is the second cleavage necessary for speck formation? Is CARD necessary at all? Would adding the TEV site at CDL and b/w p20 and p10 rescue? i.e. trans-activate?

We are grateful to the reviewer for these insightful questions, which we also had considered. We addressed this question in two ways – first by replacing the CARD with a DmrB dimerizable domain that undergoes inducible dimerization of Casp11 in the presence of the dimerizing drug AP20187. Critically, inducible dimerization of DmrB-ΔCARD-Casp11-mCherry significantly enhances Casp11-mCherry speck formation, and this speck formation requires catalytic activity, even in the presence of dimerizer (Figure 6A-C). Moreover, we generated CARD-less Casp11-mCherry constructs containing wild-type p20-p10 and catalytically inactive p20-p10. Intriguingly, the CARD was dispensable for spontaneous Casp11-mCherry speck formation, which again was dependent on catalytic activity (Figure 6-figure supplement 2A-B). While we do not currently have data with a TEV-cleavable CDL construct, our data here demonstrate that the CARD is dispensable for speck formation in an overexpression system, implying that the p20/p10 contains all the information that is necessary and sufficient to mediate spontaneous assembly of Casp11 specks in HEK293T cells. Nonetheless, as forced dimerization enhances speck formation (Figure, we hypothesize that CARD-LPS interactions act to facilitate catalytic activity and push cooperative assembly of the Casp11 speck.

To address whether both the N-terminal CARD and C-terminal p10 domains are present in Casp11 specks, we performed a dual-fluorophore co-localization assay in which we transiently expressed C-terminal mCherry-tagged Casp11 constructs (Casp11-mCherry) in HEK293T cells that stably express N-terminal Flag-tagged Casp11 (2xFLAG-Casp11). As expected, Casp11-mCherry formed specks spontaneously in this setting (Figure 3-figure supplement 1). Critically, both the N-terminal FLAG and C-terminal mCherry were found together in these specks, indicating the presence of both Casp11 N- and C- termini within the specks. Moreover, the wild-type Casp11-mCherry also recruited catalytically inactive 2xFLAG-Casp11C254A, again supporting the finding that wild-type Casp11 can recruit a catalytic mutant to noncanonical inflammasome complexes.

Comment 3: What are the equations that fit experimental data points and R2 for? E.g. Figure 1E. What are the parameters being fitted/compared and how are those interpreted? A table of fitted values and proper interpretation should be provided.

We thank the reviewer for this request to clarify how the curves were fit to the experimental data points. We have modified our ‘Statistical Analysis’ section and all figure legends that contain dose-response curves to reflect the equations used to fit each curve. Additionally, please find a table of raw values in the corresponding source data provided for each dose-response curve (Figure 2 Source Data 5; Figure 4 Source Data 3, 6; Figure 5 Source Data 3, 4; Figure 7 Source Data 2; and Figure 4-figure supplement 1 Source Data 1).

Author Response

Reviewer #1 (Public Review):

This paper examines different signaling networks and attempts to give general results for when the network will exhibit biphasic behavior, which is the situation when the output of the network is a non-monotonic function of its inputs. The strength of the paper is in the approach it takes. It starts with the simplest network motifs that produce biphasic behavior and then asks too what happens when these motifs are parts of larger networks. Their approach is in contrast to the usual way in which this question is tackled, which tends to be within the confines of a specific signaling network, where general results like the ones that the authors are after, might be hard to spot.

We thank the reviewer for the careful reading of the manuscript and for the comments and appreciate the fact the reviewer regards the approach as the strength of the paper.

The weakness of the paper, in my opinion, is the rather formal description of the results which I am afraid will be of rather limited utility to experimental groups seeking to make use of them. The paper attempts to provide general rules for when to expect biphasic behavior and it was hard to assess to what extent such rules exist as behaviors can change depending on the context of a larger network in which the smaller biphasic one is embedded. The other thing that made assessing the generality of the results difficult is that the input-output functions shown in all the figures are computed for a specific choice of parameters and I was left wondering how different choices of parameters might change the reported behaviors. The lack of specific proposals for how their results should guide future experiments on different signaling networks is another weakness.

We address these points in a number of ways. Initially our presentation was intended to highlight unambiguously which systems (especially the substrate modification building blocks) were capable of biphasic response and which were not, and highlighting parameter dependence on intrinsic kinetic parameters. Based on both referee comments, we make a number of changes

(a) We highlight the rationale for choosing the suite of biochemical substrate modification systems: enzyme/substrate sharing is a key driver for the origins of biphasic responses and the suite of systems we employ allows us to systematically explore this (see Response to Essential Revisions). These are building blocks of many pathways,

(b) Biphasic responses emerge from a built in competing effect. In every instance of substrate modification systems, we now highlight the mechanistic underpinning which gives rise to the competing effect responsible for the biphasic response. This will help experimentalists and modellers alike obtain insights into how such behaviour may arise, and the associated ingredients which facilitate that (which may be relevant in other systems). Similarly, we highlight how altered behaviour at the network level may arise from a biphasic interaction pattern, providing the intuition therein and guide further experimental investigation (also see Response to Essential Revisions).

(c) With regard to parameters (also see Response to Essential Comments) firstly we emphasize that we completely characterize at the substrate modification level, whether biphasic responses are possible as a function of intrinsic kinetic constants. This is done for every system studied. In Fig 2, we depict this, along with sample biphasic dose responses, for pictorial depiction. However, the essential point is that the parametric dependence on intrinsic kinetic parameters is completely done. We indicate in which cases biphasic responses are impossible irrespective of intrinsic kinetic parameters, where they can be obtained for every value of the intrinsic kinetic parameters, and where there are partial restrictions in the intrinsic kinetic parameter space for obtaining this. In the revision we have performed further parametric analysis to assess the impact of species total amount providing further insights. We have also shown that in all these systems biphasic responses can be obtained in ranges of kinetic parameters similar to those found experimentally (eg Wistel et al 2018) and for reasonable species total amounts in systems and synthetic biology. This is analyzed, and depicted in Figure 2-figure supplement 3 and Figure 2-figure supplement 4.

(d) Also, in response to another comment (about behaviour changing in networks): we first emphasize that we start at the substrate modification level to uncover drivers of biphasic responses at this level. Biphasic responses arise from an inbuilt competing effect and we demonstrate different ways in which such an inbuilt competing effect arises, through sharing of enzymes or substrates. While it is true that the behaviour can change as part of a network (a) It still remains that there are these in-built competing effects which can generate biphasic responses (both substrate and enzyme) and this can manifest at a pathway or network level under suitable conditions (b) the fact that behaviour at a network level may be altered is exactly why we consider studies at the network level showing both biphasic patterns in interaction (the overall behaviour is determined by the motif and the biphasic pattern of interaction and studies involving interaction of biphasic responses at both the network and substrate modification level!! (subsection: The network level)

(e) We have also expanded on a paragraph on testable predictions in the conclusions (p10).

Taken together, we believe that these results should interest both experimentalists and modellers and have intrinsic value as well.

While I appreciate that the authors adopted a style of presenting their results such that all the mathematics is buried in the figures, I found that it made reading the paper quite difficult, and contributed to my confusion about which results are general and insensitive to parameter choices and which are not. I believe a narrative that integrated the math with some simple intuition might have been more effective. For example, when the authors say in the text that model M0 is incapable of displaying biphasic response, how general is that result? Later on, when discussing model M2, they provide a criterion for biphasic response in terms of products of rate constants satisfying an inequality, but the meaning of this condition is not described. Such things make it hard to learn from the authors' work.

This has indeed been incorporated, and we agree that presenting the intuition and mechanistic underpinning for the behaviour aids readability. In addition to the points about parameters which are now explained at length in the paper , there are a number of paragraphs providing the mechanistic underpinning and intuition for why the behaviour is obtained. Both these are discussed at length in Response to Essential Revisions. Thus, both the mechanistic intuition and the role of parameters are addressed in detail in the revision.

When M0 is mentioned to be incapable of yielding biphasic responses we mean just that: irrespective of any parameter choice in the model. The meaning of the criterion in Model M2 is now discussed. We take the point about not being able to learn from the work seriously and have made various changes both on the intuition and clarifying the impact of parameters.

The text is sprinkled with statements like "this reveals the plurality of information processing behaviors..." where the meaning is quite opaque (for this example, there is no description of "information processing" and what it might mean in this context) and therefore it makes it hard to understand what are the lessons learned from these calculations. Another example is found in the description of Erk regulation where the authors speak of "significant robustness" but what is meant by "significant" is also unclear.

Yes, we agree that these phrases are distracting and not adding much and so we have removed them.

Overall, I think this is an interesting attempt to provide a general mathematical framework for analyzing biphasic response of signaling networks, but the authors fall short for the reasons described above. I think a lot can be fixed by improving the way the results are presented.

We have indeed taken these comments on board and aimed to improve the presentation

Reviewer #2 (Public Review):

Biphasic responses are widely observed in biological systems and the determination of general design principles underlying biphasic responses is an important problem. The authors attempt to study this problem using a range of biochemical signaling models ranging from simple enzymatic modification and de-modification of a single substrate to systems with multiple enzymes and substrates. The authors used analytical and computational calculations to determine conditions such as network topology, range of concentrations, and rate parameters that could give rise to biphasic responses. I think the approach and the result of their investigation are interesting and can be potentially useful. However, the conditions for biphasic responses are described in terms of parameter ranges or relationships in particular biochemical models, and these parameters have not been connected to the values of concentrations or rates in real biological systems. This makes it difficult to evaluate how these findings would be applicable in nature or in experiments. It might also help if some general mechanisms in terms of competition/cooperation of time scales/processes are gleaned which potentially can be used to analyze biphasic responses in real biological systems.

We thank the reviewer for a careful reading of the manuscript and for the various comments and are happy to see the reviewer find the approach interesting. We address these comments in more detail below.

Reading these comments, we recognized how various analysis and algebraic equations could appear opaque to a reader both in terms of what it conveys and its import. To address this, we made a number of changes.

1. First and foremost, we provide the mechanistic underpinning and intuition for why a competing effect emerges in the first place. We do this for every substrate modification system we analyze and make further comments in the subsection focussing on the network level as well as ERK This intuition should help a reader where the result is coming from and be then able to see if it might apply in a quite different system. This is discussed in detail in Response to Essential Revisions.

2. Secondly, we have discussed many aspects of the parameters in more detail. Our goal, especially in substrate modification systems was to be able to completely characterize the role of intrinsic kinetic parameters: whether biphasic responses was impossible irrespective of parameters, whether they were possible for every value of intrinsic kinetic parameters or whether they were possible in a subset of kinetic parameter space. This has been done for every substrate modification system, and has been discussed more explicitly in the revision. Furthermore, when biphasic responses were possible, we aimed to determine the impact of species total amounts which facilitated the response. Here we performed additional analytical and semi-analytical work. Additionally with the semi-analytical work and parameters chosen in ranges very similar to those found experimentally (eg Wistel et al 2018), we are able to show that biphasic responses can indeed be obtained in experimentally feasible ranges. Further aspects of the parameters are discussed in detail in the Response to Essential Revisions. In particular, a number of new paragraphs (p2-3, p6) and plots Figure 2-figure supplement 3 and Figure 2-figure supplement 4 specifically deal with this.

Taken together these address the reviewers points.

Author Response

Reviewer #1 (Public Review):

This interesting manuscript sets out to develop for the mouse a series of important concepts and models that this group has previously developed for models of monkey brains, where they showed that in a large-scale model, anterior → posterior spatial gradients such as spine density (and thus inferred strength of local coupling) lead to a transition from transient stimulus responses to persistent responses, capable of supporting working memory (WM). No such spine density gradient is found in the mouse. Here, the authors propose and use modeling to explore the idea, that the corresponding gradient may be that of density of inhibitory PV cells in different regions of the brain.

The goal of the study - a large-scale, anatomically-constrained model of WM - is an extremely valuable one, and the authors' efforts in this direction should be supported. That said, some of the main claims in the manuscript were not, at least as currently written, clearly supported by the data, a number of important clarifications need to be made, and some claims of novelty are made in a way that, for a typical reader, may obscure the actual contribution being made.

The biggest issue is that one of the main claims, that together with cell-type specific long-range targeting, "density of cell classes define working memory representations" (abstract), is not terribly clear. For example, Figs. 2D and 2E show that a brain region's hierarchical location tightly predicts its persistent firing rate (2D), but that PV cell fraction has a far weaker correlation (2E). Is hierarchical location sufficient? If PV cell fraction were constant across model brain regions, would we still get persistent activity modes? It seems likely that the answer may be "yes", but the answer, easily within reach of the authors, is surprisingly not in the current version of the manuscript. Figure 3D, for the thalamocortical model, shows no significant correlation of firing rate with PV density.

Given the claim about PV density (in the abstract and the first main point of the discussion), this is a big concern. Yet it seems easily addressable: e.g. if indeed the authors found that hierarchy was sufficient and PV density immaterial, the model would be no less interesting. And if the authors demonstrated clearly that a PV density gradient is required, that would make the claim a solid one. If, within the model, such a causal demonstration is present, this reader at least missed it.

MAJOR CONCERNS:

(1) The model appears to be a model of a single side of the brain. Perhaps each brain region in the model could be considered an amalgam of that region across both sides of the brain. Yet given results like Li et al. Nature 2016, who show that persistent activity is robust to inhibition of one side, but not both sides of ALM, at the very least discussion of the issue is warranted.

The model is indeed a one-hemisphere model, and an expansion to a bihemispheric model is considered for future work. We have added the following sentence in the Discussion section:

“Future versions of the large-scale model may consider different interneuron types to understand their contributions to activity patterns in the cortex (Kim et al,2017; Meng et al., 2023; Tremblay and Rudy, 2016; Nigro et al., 2022), the role of interhemispheric projections in providing robustness for short-term memory encoding (Ni et al., 2016), and the inclusions of populations with tuning to various stimulus features and/or task parameters that would allow for switching across tasks (Yang et al, 2018).”

(2) The authors make an interesting attempt to distinguish core WM regions from other regions such as "readout" regions, defined as showing persistent activity yet not having an effect on persistent activity elsewhere in the network.

However, this definition seemed problematic: for example, consider a network that consists of 20 brain regions, all interconnected to each other, and all equivalent to each other, capable of displaying persistent activity thanks to mutual connectivity. Imagine that inhibition of any one of these regions is not sufficient to significantly perturb persistent activity in the other 19. Then they would all be labeled as "readout". Yet, by construction in this thought experiment, they are all equivalent to each other and are all core areas. Such redundancy may well be present in the brain. How would the authors address this redundancy issue?

We acknowledge the importance of this thought experiment. Although we initially restricted the definition of core area to how a single area contributes to working memory, we proceeded with concurrent inhibition of multiple readout areas (see Essential Revisions response 6 above).

(3) Also important to discuss would be the fact that every brain region in this model is set up as composed of two populations, and when long-range interactions are strong and the attractors strongly coupled, the entire brain is set up as a 1-bit working memory. How would results and the approach be impacted by considering WM for more flexible situations?

We have used a model of two populations as the simplest way to integrate large-scale connectivity and inhibitory gradients. Indeed, future work should consider more realistic connectivity and populations with various degrees of tuning to different task parameters. (see Reviewer 1 response 1 above)

(4) Another concern that is important yet easily addressed is the authors' use of the term "novel cell-type specific graph theory measures". Describing in the abstract and elsewhere the fact that what they mean is to take into account the sign of connections, not just their magnitude, would transmit to readers the essence of the contribution in a manner very simple to understand. Most readers would fail to grasp the essential point of the current labeling, which sounds potentially very vague and complex.

We have reworded the abstract - see also Essential reviews response 2 above.

(5) Finally, the overall significance of the study, and advances over previous work, were not entirely clear. In the discussion, the authors identify three major findings: (1) WM function is shaped by the PV cell density gradient. But as above, further work is required to make it clear that this claim is supported by the model. (2) if local recurrent excitation is insufficient to generate persistent activity, then long-range recurrent excitation is needed to generate it. I had trouble understanding why a model was needed to reach this conclusion - it seems as if it is simply a question of straightforward logic. The discussion states that in this regard, the work here "offers specific predictions to be tested experimentally", but I had trouble identifying what these specific predictions are. (3) Taking into account sign, not only magnitude, of connections, is important. This last point once again seemed a matter of straightforward logic, making its novelty difficult to assess.

We thank the reviewer, we have addressed these issues in the Essential Revisions 3) above.

Reviewer #2 (Public Review):

This paper uses the mouse mesoscale connectome, combined with data on the number and fraction of PV-type interneurons, to build a large-scale model of working memory activity in response to inputs from various sensory modalities. The key claims of the paper are two-fold. First, previous work has shown that there does not appear to be an increase in the number of excitatory inputs (spines) per pyramidal neuron along the cortical hierarchy (and this increase was previously suggested to underlie working memory activity occurring preferentially in higher areas along the cortical hierarchy). Thus, the claim is that a key alternative mechanism in the mouse is the heterogeneity in the fraction of PV interneurons. Second, the authors claim to develop novel cell type-specific graph theory.

I liked seeing the authors put all of the mouse connectomic information into a model to see how it behaved and expect that this will be useful to the community at large as a starting point for other researchers wishing to use and build upon such large-scale models. However, I have significant concerns about both primary scientific claims. With regard to the PV fraction, this does not look like a particularly robust result. First, it's a fairly weak result to start, much smaller than the simple effect of the location of an area along the cortical hierarchy (compare Figs. 2D, 2E; 3C, 3D). Second, the result seems to be heavily dependent upon having subdivided the somatosensory cortex into many separate points and focusing the main figures of the paper (and the only ones showing rates as a function of PV cell fraction) solely on simulations in which the sensory input is provided to the visual cortex. With regards to the claim of novel cell type-specific graph theory, there doesn't appear to be anything particularly novel. The authors simply make sure to assign negative rather than positive weights to inhibitory connections in their graph-theoretic analyses.

Major issues:

1) Weakness of result on effect of PV cell fraction. Comparing Figures 2D and 2E, or 3C and 3D, there is a very clear effect of cortical hierarchy on firing rate during the delay period in Figures 2D and 3C. However, in Figure 2E relating delay period firing rate to PV cell fraction, the result looks far weaker. (And similarly for Figs. 3C, 3D, with the latter result not even significant). Moreover, the PV cell fraction results are dominated by the zero firing rate brain regions (as opposed to being a nice graded set of rates, both for zeros and non-zeros, as with the cortical hierarchy results of Figures 2D), and these zeros are particularly contributed to by subdividing somatosensory (SS) into many subregions, thus contributing many points at the lower right of the graph.

Further, it should be noted that Figure 2E is for visual inputs. In the supplementary Figure 2 - supplement 1, the authors do apply sensory inputs to auditory and somatosensory cortex...but then only show the result that the delay period firing rate increases along the cortical hierarchy (as in Figure 2D for the visual input), but strikingly omit the plots of firing rate versus PV cell fraction. This omission suggests that the result is even weaker for inputs to other sensory modalities, and thus difficult to justify as a defining principle.

We have now made an effort to exhaustively compare the contributions of PV versus hierarchy in defining the firing rate activity patterns in the model - see Essential Revisions response 1 above. Moreover, we included plots of firing rate versus PV cell fraction for other sensory modalities, and the results would still support a common architecture for short-term memory maintenance.

2) Graph theoretic analyses. The main comparison made is between graph-theoretic quantities when the quantities account for or do not account for, PV cells contributing negative connection strengths. This did not seem particularly novel.

See Essential Revisions response 2 above

3) It was not clear to me how much the cell-type specific loop strength results were a result of having inhibitory cell types, versus were a result of the assumption ('counter-stream inhibitory bias') that there is a different ratio of excitation to inhibition in top-down versus bottom-up connections. It seems like the main results were more a function of this assumed asymmetry in top-down vs. bottom-up than it was a function of just using cell-type per se. That is, if one ignored inhibitory neurons but put in the top-down vs. bottom-up asymmetry, would one get the same basic results? And, likewise, if one didn't assume asymmetry in the excitatory vs. inhibitory connectivity in top-down versus bottom-up connections, but kept the Pyramidal and PV cell fraction data, would the basic result go away?

We have addressed the issue of cell-type specific loop strength in Essential Revisions response 2 above.

4) In the Discussion, there is a third 'main finding' claimed: "when local recurrent excitation is not sufficient to sustain persistent activity...distributed working memory must emerge from long-range interactions between parcellated areas". Isn't this essentially true by definition?

We have addressed this important issue in Essential Revisions response 3 above.

5) I don't know if it's even "CIB" that's important or just "any asymmetry (excitatory or inhibitory) between top-down vs. bottom-up directions along the hierarchy". This is worth clarifying and thinking more about, as assigning this to inhibition may be over-attributing a more basic need for asymmetry to a particular mechanism.

We found that this asymmetry is indeed crucial, which may be provided by CIB or, in some regimes, it is sufficient that a PV gradient is present - see Essential Revisions response 1 above.

Other questions:

1) Is it really true that less than 2% of neurons are PV neurons for some areas? Are there higher fractions of other inhibitory interneuron types for these areas, and does this provide a confound for interpreting model results that don't include these other types?

Maybe related to the above, the authors write in the Results that local excitation in the model is proportional to PV interneuron density. However, in the methods, it looks like there are two terms: a constant inhibition term and a term proportional to density. Maybe this former term was used to account for other cell types. Also, is local excitation in the model likewise proportional to pyramidal interneuron density (and, if not, why not?)?

The reviewer is correct in pointing out that the ‘constant inhibition term’, which we interpret as a minimal inhibition, accounts for other cell types. We have added the respective explanation in the Methods section. Future versions of the model may include different interneuron types - see Reviewer 1 Response 1 above.

2) Non-essential areas. The categorization of areas as 'non-essential' as opposed to, e.g. "inputs" is confusing. It seems like the main point is that, since the delay period activity as a whole is bistable, certain areas' contributions may be small enough that, alone, they can't flip the network between its bistable down and up states. However, this does not mean that such areas (such as the purple 'non-essential' area in Figure 5a) are 'non-essential' in the more common sense of the word. Rather, it seems that the purple area is just a 'weaker input' area, and it's confusing to thus label it as 'non-essential' (especially since I'd guess that, whether or not an area flips on/off the bistability may also depend on the assumed strength of the external input signal, i.e. if one made the labeled 'input area' a bit too weak to alone trigger the bistability, then the purple area might become 'essential' to cross the threshold for triggering a bistable-up state).

This is an important point, and a similar point was also raised by Reviewer 1. For simplicity, we have restricted the definition of the function of an area (e.g., input, vs core vs non essential) to how a single area contributes to working memory. The existence of ‘subnetworks’ for any of these functions is indeed plausible - and potentially important, but we have left this for future modeling work. (see Essential Revisions response 6 above). The point that distinguishes ‘input’ and ‘non-essential’ areas is simply whether inhibiting said area during the stimulus period affects stimulus-specific persistent activity. Surely some of the areas that we have classified as ‘non-essential’ have important roles, even for the contents of working memory, however they are not essential to produce the activity pattern we observe here.

3) Relation between 'core areas' and loop strength. The measure underlying 'prediction accuracy = 0.93' in Figure 6D and the associated results seems incomplete by being unidirectional. It captures the direction: 'given high cell-type specific loop strength, then core area' but it does not capture the other direction: 'given a cell is part of a core area, is its predicted cell-type specific loop strength strong?'. It would be good to report statistics for both directions of association between loop strength and core area.

Indeed the prediction accuracy refers to the direction loop strength->core area, for which we estimate how well a continuous variable (loop strength) predicts a binary variable (whether core area or not). A prediction in the reverse direction is not well defined, namely to predict a continuous variable from a binary variable, so the reverse association may be only indirectly inferred from Figure 8D.

4) More justification would be useful on the assumption that the reticular nucleus provides tonic inhibition across the entire thalamus.

Relatively little is known about how specific this inhibition may be. We have included references in the Discussion section that speak to this fact. (Crabtree 2018, Hardinger et al., 2023).

5) Is NMDA/AMPA ratio constant across areas and is this another difference between mice and monkeys? I am aware of early work in the mouse (Myme et al., J. Neurophys., 2003) suggesting no changes at least in comparing two brain regions' layer 2/3, but has more work been performed related to this?

Recent anatomical in-vitro autoradiography work in the macaque shows that NMDA/AMPA ratio (in terms of receptor density) varies across the cortical hierarchy (Klatzmann et al., 2022). Functionally NMDA receptors seem important in PFC L2/3 for persistent activity, while in V1, they contribute relatively little to the stimulus response, which is dominated by AMPA-mediated excitation. This was shown by a recent physiological study in the macaque (Yang et al., 2018). This could indeed point to a species difference, although like-for-like comparisons of equivalent experiments across species are lacking in the literature.. We have included this and other related references in our Discussion - see Essential Revision 4 above.

6) Are bilateral connections between the left and right sides of a given area omitted and could those be important?

These potentially important connections were omitted for simplicity in the model, please see Reviewer 1 Responses 1, 3 above.

Reviewer #3 (Public Review):

Combining dynamical modelling and recent findings of mouse brain anatomy, Ding et al. developed a cell-type-specific connectome-based dynamical model of the mouse brain underlying working memory. The authors find that there is a gradient across the cortex in terms of whether mnemonic information can be sustained persistently or only transiently, and this gradient is negatively correlated to the local density of parvalbumin (PV) positive inhibitory cells but positively correlated with mesoscale-defined cortical hierarchy. In addition, weighing connectivity strength by PV density at target areas provides a more faithful relationship between input strength and delay firing rate. The authors also investigate a model where cortical persistent activity can only be sustained with thalamus input intact, although this result is rather separate from the rest of the study. The authors then use this model to test the causal contributions of different areas to working memory. Although some of the in silico perturbations are consistent with existing experimental data, others are rather surprising and need to be further discussed. Finally, the authors investigate patterns of attractor states as a result of different local and long-range connections and suggest that distinct attractor states could underlie different task demands.

The importance of PV density as a predictor for working memory activity patterns in the mouse brain is in contrast to recent computational findings in the primate brain where the number of spines (excitatory synapses per pyramidal cell) is the key predictor. This finding reveals important species differences and provides complementary mechanisms that can shape distributed patterns of working memory representation across cortical regions. The method of biologically-based near-whole-brain dynamical modeling of a cognitive function is compelling, and the main conclusions are mostly well supported by evidence. However, some aspects of the method, result, and discussion need to be clarified and extended.

1) Based on existing anatomical data, the authors reveal a negative correlation between cortical hierarchy (defined by mesoscale connectivity; this concept needs to be explicitly defined in the Results session, not just in the Method section) and local PV density (Fig. 1). In the dynamical model, the authors find that working memory activity is positively (and strongly) correlated with cortical hierarchy and negatively (and less strongly) correlated with PV cell density (Fig. 2), and conclude that working memory activity depends on both. But could the negative correlation between activity and PV density simply result from the inherent relationship between hierarchy and PV density across regions? To strengthen this result, the authors should quantify the predictive power of local PV density on working memory activity beyond the predictive power of cortical hierarchy.

We have systematically compared the relationship between PV and hierarchy in generating delay-patterns of activity - see Essential Revisions response 1 above.

2) In Fig. 4, the authors find that cell-type-specific graph measures more accurately predict delay-period firing rates. Specifically, the authors weigh connections with a cell-type-projection coefficient, which is smaller when the PV cell fraction is higher in the target area. Considering that local PV cell fraction is already correlated with delay activity patterns, weighing the input with the same feature will naturally result in a better input-output relationship. This result will be strengthened if there is a more independent measure of cell-type-projection coefficient, such as the spine density of PV vs excitatory cells across regions, or even the percentage of inhibitory versus excitatory cells targeted by upstream region (even just for an example set of brain regions).

We have compared different measures of cell-type projection coefficients and how they predict delay-patterns of activity and whether an area is a core area - see Essential Revisions response 2 above.

3) The authors aim to identify a core subnetwork that generates persistent activity across the cortex by characterising delay activity as well as the effects of perturbations during the stimulus and delay period. Consistent with existing data, the model identifies frontal areas and medial orbital areas as core areas. Surprisingly, areas such as the gustatory area are also part of the core areas. These more nuanced predictions from the model should be further discussed. Also surprisingly, the secondary motor cortex (MOs), which has been indicated as a core area for short-term memory and motor planning by many existing studies is classified as a readout area. The authors explain this potential discrepancy as a difference in task demand. The task used in this study is a visual delayed response task, and the task(s) used to support the role of MOs in short-term memory is usually a whisker-based delayed response task or an auditory delay response task. In all these tasks, activity in the delay period is likely a mixture of sensory memory, decision, and motor preparation signals. Therefore, task demand is unlikely the reason for this discrepancy. On the other hand, motor effectors (saccade, lick, reach, orient) could be a potential reason why some areas are recruited as part of the core working-memory network in one task and not in another task. The authors should further discuss both of these points.

We have addressed this important point in Essential Revisions response 5 above.

4) As a non-expert in the field, it is rather difficult to grasp the relationship between the results in Fig. 7 and the rest of the paper. Are all the attractor states related to working memory? If so, why are the core regions for different attractor states so different? And are the core regions identified in Fig. 5 based on arbitrary parameters that happen to identify certain areas as core (PL)? The authors should at least further clarify the method used and discuss these results in the context of previous results in this study.

Attractor states that have a stable baseline are, by definition, related to working memory in that there is a baseline and a memory state associated with the model. Some areas, such as PL are more likely to be associated with different core subnetworks given its position in the hierarchy. In the current version of the manuscript, we provide a motivation for the different attractor states and how they may relate to cognitive function.

Author Response

Reviewer #1

While the article clearly outlines the strengths of the chosen approach, it lacks an equally clear exposition of its limitations and a more thorough comparison to established approaches. Two examples of limitations that should be stated more clearly, in my opinion: models need to be small enough to fit on a single machine (in contrast to e.g. NEURON and NEST which support distributed computation via MPI), and only single-compartment models are supported; both limitations are mentioned in passing in the discussion, but would merit a more upfront mention.

We agree that our paper could be improved by more clearly stating the limitations of our approach and comparing it to established approaches. We have revised the paper and added two new subsections in the Discussion section to address these specific concerns:

1. The Limitations subsection (L448 - L491) acknowledges restrictions of BrainPy paradigm which uses a Python-based object-oriented programming. It highlights three main categories of limitations: (a) approach limitations, (b) functionality limitations, (c) parallelization limitations. These limitations highlight areas where BrainPy may require further development to improve its functionality, performance, and compatibility with different modeling approaches.

2. The Future Work subsection (L493 - L526) outlines development enhancements we aim to pursue in the near term. It emphasizes the need for further development in order to meet the demands of the field. Three key areas requiring attention are highlighted: (a) multi-compartment neuron models, (b) ultra-large-scale brain simulations, (c) bridging with acceleration computing systems.

In addition to these changes, we have also made a number of other minor changes to the paper to improve its clarity and readability.

The study does not verify the accuracy of the presented framework. While its basic approach (time-step-based simulation, standard numerical integration algorithms) is sufficiently similar to other software to not expect major discrepancies, an explicit comparison would remove any doubt. Quantitative measures of accuracies are particularly important in the context of benchmarks (see below), since simulations can be made arbitrarily fast by sacrificing performance.

We agree that an explicit comparison would help alleviate any doubts and provide a more comprehensive understanding of our framework's accuracy. We have revised our manuscript to include a dedicated section, particularly Appendix 11. In this section, we verified that all simulators generated consistent average firing rates for the given benchmark network models (figure 1 and figure 2 in Appendix 11). These verifications were performed under different network sizes (ranging from 4e^3 to 4e^5) and different computing platforms (CPU, GPU and TPU). We also qualitatively compared the overall network activity patterns produced by each simulator to ensure they exhibited the same dynamics (figure 3 and figure 4 in Appendix 11). While exact spike-to-spike reproducibility was not guaranteed between different simulator implementations, we confirmed that our simulator produced activity consistent with the reference simulators for both firing rates and network-level dynamics. Additionally, BrainPy did not sacrifice simulation accuracy for speed performance. Despite using single precision floating point, BrainPy was able to produce consistent firing rates and raster diagrams across all simulations (see figure 3 and figure 4 in Appendix 11).

We hope these revisions can ensure that our manuscript provides a clear and robust validation of the accuracy of our simulator.

Benchmarking against other software is obviously important, but also full of potential pitfalls. The current article does not state clearly whether the results are strictly comparable. In particular: are the benchmarks on the different simulators calculating results to the same accuracy (use of single or double precision, same integration algorithm, etc.)? Does each simulator use the fastest possible execution mode (e.g. number of threads/processes for NEST, C++ standalone mode in Brian2, etc.)? What is exactly measured (compilation time, network generation time, simulation execution time, ...) - these components will scale differently with network size and simulation duration, so summing them up makes the results difficult to interpret. Details are also missing for the comparison between the XLA operator customization in C++ vs. Python: was the C++ variant written by the authors or by someone else? Does the NUMBA→XLA mechanism also support GPUs/TPUs? This comparison also seems to be missing from the GitHub repository provided for reproducing the paper results.

We have carefully considered these comments and addressed each of these concerns regarding the benchmarks and examples presented in our paper.

1. Lack of Details in Examples: In the revised version of the paper, we provide additional information and any other pertinent details to enhance the clarity and replicability of our results. Particularly, in Appendix 9, we provide the mathematical description, the number of neurons, the connection density, and delay times used in our multi-scale spiking network; in Appendix 10, we provide the detail description of reservoir models, evaluation metrics, training algorithms, and their implementations in BrainPy; in Appendix 11, we elaborate the hardware and software specifications and experimental details for benchmark comparisons.

2. Inadequate Description of Benchmarking Procedures: In the revised paper, particularly, in L328-L329 of the main text at section of "Efficient performance of BrainPy" and in Appendix 11, we elaborate on the integration methods, simulation time steps, and floating-point precision used in our experiments. We also ensure that these parameters are clearly stated and identical across all simulators involved in the benchmarking process, see "Accuracy evaluations" in Appendix 11 (L1550 - L1580).

3. Clarification on Measured Time: In the revised paper, we state that all simulations only measured the model execution time, excluding model construction time, synapse creation time, and compilation time, see "Performance measurements" in Appendix 11 (L1539 - L1548).

4. Consideration of Acceleration Modes: In the revised version, we provide the simulation speed of other brain simulators on different acceleration modes, see Figure 8. For instance, we utilize the fastest possible option --- the C++ standalone mode in Brian2 --- for speed evaluations. Furthermore, we have requested the developers of the comparison simulators for optimizing the benchmark models, ensuring a fair and accurate comparison.

5. Scaling Networks to Maintain Activity: In the revised manuscript, we adopt the suggestion of Reviewer #3 and apply the appropriate scaling techniques to maintain consistent network activity throughout our experiments. These details can be found in Appendix 11 (also see Appendix 11—figure 1 and Appendix 11—figure 2).

Regarding the comparison between XLA operator customization in C++ and Python, we utilized our self-implemented C++ version, which is accessible in the Appendix 8 Listing 2. Presently, the NUMBA→XLA mechanism does not support GPUs/TPUs; however, we are working on expanding this capability to other platforms. We have made this clarification in the revised manuscript as well (see L1278 - L1285).

While the authors convincingly argue for the merits of their Python-based/object-oriented approach, in my opinion, they do not fully acknowledge the advantages of domain-specific languages (NMODL, NestML, equation syntax of ANNarchy and Brian2, ...). In particular, such languages aim at a strong decoupling of the mathematical model description from its implementation and other parts of the model. In contrast, models described with BrainPy's approach often need to refer to such details, e.g. be aware of differences between dense and sparse connectivity schemes, online, or batch mode, etc. It might also be worth mentioning descriptive approaches to synaptic connectivity as supported by other simulators (connection syntax in Brian2, Connection Set Algebra for NEST).

We have made revisions to better acknowledge the merits of DSLs while providing a more comprehensive comparison. These revisions are incorporated in Discussion (L452 - L466) and Appendix 1 (L778 - L788).

Reviewer #2

While the results presented are impressive, publishing further details of the benchmarks in an appendix would be helpful for evaluating the claims and the overall conclusion would be more convincing if the performance benefits were demonstrated on a wider selection of test cases. Unsatisfyingly, the authors gave up on making a direct comparison to Brian running on GPUs with GeNN which would have been a fairer comparison than CPU-based simulations. The code for the chosen benchmarks is also likely to be highly optimised by the authors for running on BrainPy but less so for the other platforms - a fairer test would be to invite the authors of the other simulators to optimise the same models and re-evaluate the benchmarks.

We have carefully considered these comments and addressed each of these concerns regarding the benchmarks and examples presented in our paper.

1. Lack of Details in Examples: In the revised version of the paper, we provide additional information and any other pertinent details to enhance the clarity and replicability of our results. Particularly, in Appendix 9, we provide the mathematical description, the number of neurons, the connection density, and delay times used in our multi-scale spiking network; in Appendix 10, we provide the detail description of reservoir models, evaluation metrics, training algorithms, and their implementations in BrainPy; in Appendix 11, we elaborate the hardware and software specifications and experimental details for benchmark comparisons.

2. Inadequate Description of Benchmarking Procedures: In the revised paper, particularly, in L328-L329 of the main text at section of "Efficient performance of BrainPy" and in Appendix 11, we elaborate on the integration methods, simulation time steps, and floating-point precision used in our experiments. We also ensure that these parameters are clearly stated and identical across all simulators involved in the benchmarking process, see "Accuracy evaluations" in Appendix 11 (L1550 - L1580).

3. Clarification on Measured Time: In the revised paper, we state that all simulations only measured the model execution time, excluding model construction time, synapse creation time, and compilation time, see "Performance measurements" in Appendix 11 (L1539 - L1548).

4. Consideration of Acceleration Modes: In the revised version, we provide the simulation speed of other brain simulators on different acceleration modes, see Figure 8. For instance, we utilize the fastest possible option --- the C++ standalone mode in Brian2 --- for speed evaluations. Furthermore, we have requested the developers of the comparison simulators for optimizing the benchmark models, ensuring a fair and accurate comparison.

5. Scaling Networks to Maintain Activity: In the revised manuscript, we adopt the suggestion of Reviewer #3 and apply the appropriate scaling techniques to maintain consistent network activity throughout our experiments. These details can be found in Appendix 11 (also see Appendix 11—figure 1 and Appendix 11—figure 2).

Regarding the wider selection of test cases, we understand the importance of demonstrating the performance benefits on a broader range of scenarios. Particularly, we have designed two kinds of benchmark models:

• Sparse connection models. This category models include COBA-LIF network and COBA-HH network. The former is a standard E/I balanced network for comparing simualtion speed of a brain simulator, while the latter uses the complex computational expensive HH neuron model as the elements. Both models can be effectively to demonstrate the capability of a brain simulator for the sparse and event-driven computation.

• Dense connection models. The local circuits of a cortical column are usually connected densely (Science 366, 1093). Particularly, we use the decision making network proposed by (Wang, 2002) for evaluations.

In the revised version, we include extensive experiments on these three test cases under different kinds of computing platforms (including CPU, GPU, and TPU) to strengthen the overall conclusion and provide a more comprehensive evaluation of our approach.

Regarding the comparison to Brian running on GPUs with GeNN, we apologize for not including that in our initial submission. We have conducted the necessary experiments on all three benchmark models we have used in our evaluations and include these results in the revised version of the paper (see Figure 8). This addition will enhance the credibility of our findings and allow for a more meaningful comparison between different simulation platforms. Furthermore, we have also reached out to the authors of other simulators and invite them to optimize the same models used in our benchmarks. We believe this collaborative approach will ensure a more equitable evaluation of the simulators and provide a more robust and convincing analysis of our work.

Furthermore, the manuscript reads like an advertisement for the platform with very little discussion of its limitations, weaknesses, or directions for further improvement. A more frank and balanced perspective would strengthen the manuscript and give the reader greater confidence in the platform.

We agree that our paper could be improved by more clearly stating the limitations of our approach and comparing it to established approaches. We have revised the paper and added two new subsections in the Discussion section to address these specific concerns:

1. The Limitations subsection (L448 - L491) acknowledges restrictions of BrainPy paradigm which uses a Python-based object-oriented programming. It highlights three main categories of limitations: (a) approach limitations, (b) functionality limitations, (c) parallelization limitations. These limitations highlight areas where BrainPy may require further development to improve its functionality, performance, and compatibility with different modeling approaches.

2. The Future Work subsection (L493 - L526) outlines development enhancements we aim to pursue in the near term. It emphasizes the need for further development in order to meet the demands of the field. Three key areas requiring attention are highlighted: (a) multi-compartment neuron models, (b) ultra-large-scale brain simulations, (c) bridging with acceleration computing systems. In addition to these changes, we have also made a number of other minor changes to the paper to improve its clarity and readability.

Since simulators wax and wane in popularity, it would be reassuring to see a roadmap for development with a proposed release cadence and a sustainable governance policy for the project. This would serve to both clearly indicate the areas of active development where community contributions would be most valuable and also to reassure potential users that the project is unlikely to be abandoned in the near future, ensuring that their time investment in learning to use the framework will not be wasted.

We appreciate the reviewer raising the point for demonstrating the project's sustainability. In response to this feedback, we have made the following efforts.

Firstly, we add and maintain a "Development roadmap" section in the BrainPy GitHub homepage (https://github.com/brainpy/BrainPy). This will enable the community to have a clear understanding of the project's direction and the areas of active development. Additionally, the "Future work" section in our revised paper has also outlined a comprehensive roadmap for next stages of the BrainPy development.

Secondly, to address the concern about the sustainability of our project and the potential risk of abandonment, we have incorporated a ACKNOWLEDGMENTS.md file in the GitHub (https://github.com/brainpy/BrainPy/blob/master/ACKNOWLEDGMENTS.md) to outline our sustainable funding support. These supports demonstrates our commitment to the long-term maintenance and development of the project, thus may help to dispel doubts of users for the project abandonment.

Similarly, a complex set of dependencies, which need to be modified for BrainPy, will likely make the project hard to maintain and so a similar plan to those given for the CI pipeline and documentation generation for automation of these modifications would be a good addition. It is also important to periodically reflect on whether it still makes sense to combine all the disparate tools into one framework as the codebase grows and starts to strain under modifications required to maintain its unification.

We appreciate the reviewer's valuable suggestions on the BrainPy framework.

First, BrainPy is a self-contained package designed specifically for brain dynamics programming. It boasts minimal dependencies, relying only on fundamental packages within the Python scientific computing ecosystem. In essence, BrainPy relies on numpy for array-based computations and utilizes jax and jaxlib for JIT compilation. While we currently utilize numba to customize dedicated operators, we can also remove this dependency by rewriting these operators with C++ code. We incorporate the use of brainpylib, a package developed by ourselves, which provides dedicated operators for CPUs and GPUs in the context of brain dynamics modeling. Additionally, BrainPy leverages mature solutions within the field for certain auxiliary functions. For instance, we integrate the use of tqdm to facilitate the display of a progress bar during model execution, and employ matplotlib for visualization purposes, capitalizing on its well-established capabilities in the scientific community.

Second, we agree that there is a risk of overly complex dependencies and architectural strains. To mitigate this risk, we have taken the following changes:

• We prioritize good software engineering practices like loose coupling, high cohesion and modularity in the framework design. This will isolate dependencies and changes to specific components. For example, brainpy.visualize nodule defines abstract visualization functions in which the visualization backend can be changed anytime.

• We invest in automating aspects of the build, test, and release process to relieve manual maintenance burdens. We heavily use the GitHub actions for testing BrainPy codes and building documentations.

• We document dependencies clearly and maintain backwards compatibility when possible. New APIs will be clearly stated supported after which BrainPy version, and deprecated APIs will be deprecated over multiple release cycles.

• We continuously monitor code complexity metrics and refactor/simplify the architecture when needed.

• When new tools have significantly different requirements, we will consider spinning them off into separate projects rather than forcing them into the core framework.

Finally, a live demonstration would be a very useful addition to the project. For example, a Jupyter notebook hosted on mybinder.org or similar, and a fully configured Docker image, would each enable potential users to quickly experiment with BrainPy without having to install a stack of dependencies and troubleshoot version conflicts with their pre-existing setup. This would greatly lower the barrier to adoption and help to convince a larger base of modellers of the potential merits of BrainPy, which could be major, both in terms of the computational speed-up and ease of development for a wide range of modelling paradigms.

We appreciate the reviewer's valuable feedback and suggestion. We have hosted a Jupyter notebook and a fully configured Docker image on mybinder.org (https://mybinder.org/v2/gh/brainpy/BrainPy-binder/main). Users can easily experiment with BrainPy without the need to install multiple dependencies or troubleshoot version conflicts.

Reviewer #3

One potential issue is that the scope of the neuro-simulator is not very clearly explained and the target audience is not well defined: is BrainPy primarily intended for computational neuroscientists or for neuro-AI practitioners? The simulator offers very detailed neural models (HH, fractional order models), classical point-models (LIF, AdEx), rate-coded models (reservoirs), but also deep learning layers (Conv, MaxPool, BatchNorm, LSTM). Is there an advantage to using BrainPy rather than PyTorch for purely deep networks? Is it possible to build hybrid models combining rate-coded reservoirs or convnets with a network of HH neurons? Without such a hybrid approach, it is unclear why the deep learning layers are needed.

We appreciate the reviewer's concern regarding the scope of BrainPy and the need for clarification regarding the target audience.

BrainPy is designed to cater to both computational neuroscientists and neuro-AI practitioners by integrating detailed neural models, classical point models, rate-coded models, and deep learning models. The platform aims to provide a general-purpose programming framework for modeling brain dynamics, allowing users to explore the dynamics of brain or brain-inspired models that combines insights from biology and machine learning.

Particularly, brain dynamics models (provided in brainpy.dyn module) and deep learning models (provided in brainpy.dnn module) are closely integrated with each other in BrainPy. First, to build brain dynamics models, users should use the building blocks in brainpy.dnn module to create synaptic projections.

Second, to build brain-inspired computing models for machine learning, users could also take advantages of neuronal and synaptic dynamics have been provided in brainpy.dyn module.

To that end, BrainPy provides building blocks of detailed conductance-based models like Hodgkin-Huxley, as well as common deep learning layers like convolutions.

Regarding the advantage of using BrainPy over PyTorch for purely deep networks, we acknowledge that existing deep learning libraries like Flax in the JAX ecosystem provide extensive tools and examples for constructing traditional deep neural networks. While BrainPy does implement standard deep learning layers, our primary focus is not to compete directly with those libraries. Instead, we provide these models for the seamless integration of deep learning layers within BrainPy's core modeling abstractions, including variables and dynamical systems. This integration allows researchers to incorporate common deep learning layers into their brain models. Additionally, the inclusion of deep learning layers in BrainPy serves as examples for customization and facilitates the development of tailored layers for neuroscience research. Researchers can modify or extend the implementations to suit their specific needs.

In summary, BrainPy's scope focuses on the general-purpose brain dynamics programming. The target audience includes computational neuroscientists who want to incorporate insights from machine learning, as well as some ML researchers interested in integrating brain-like components.

In terms of plasticity, only external training procedures are implemented (backpropagation, FORCE, surrogate gradients). No local plasticity mechanism (Hebbian learning for rate-coded networks, STDP and its variants for spiking networks) seems to be implemented, apart from STP. Is it a planned feature? Appendix 8 refers to bp.synplast.STDP(), but it is not present in the current code (https://github.com/brainpy/BrainPy/tree/master/brainpy/_src/dyn/synplast). Spiking networks without STDP are not going to be very useful to computational neuroscientists, so this suggests that the simulator targets primarily neuro-AI, i.e. AI researchers interested in using spiking models in a machine learning approach.

We appreciate that the reviewer raising the limitations of BrainPy in terms of local plasticity mechanisms. We are sorry for the delay of implementing STDP models in BrainPy. Currently, we provide very general implementations of STDP. It can be compatible with any synaptic model (such as Exponential, Dual Exponential, AMPA, GABA, and NMDA dynamics), and common connection patterns (such as Dense, and Sparse connection patterns).

bp.dyn.STDP_Song2001(pre, post, delay, syn, comm, out)

It can also be easily used with the combination of short-term plasticity models. The modular design of BrainPy's framework also make the plasticity component straightforward to be implemented and integrated into existing models.

A second weakness of the paper concerns the demos and benchmarks used to demonstrate the versatility and performance of BrainPy, which are not sufficiently described. In Fig. 4, it is for example not explained how the reservoirs are trained (only the readout weights, or also the recurrent ones? Using BPTT only makes sense when the recurrent weights are also trained.), nor how many neurons they have, what the final performance is, etc. The comparison with NEURON, NEST, and Brian2 is hard to trust without detailed explanations. Why are different numbers of neurons used for COBA and COBAHH? How long is the simulation in each setting? Which time is measured: the total time including compilation and network creation, or just the simulation time? Are the same numerical methods used for all simulators? It would also be interesting to discuss why the only result involving TPUs (Fig 8c) shows that it is worse than the V100 GPU. What could be the reason? Are there biologically-realistic networks that would benefit from a TPU? As the support for TPUs is a major selling point of BrainPy, it would be important to investigate its usage further.

We appreciate the reviewer for raising the important question about the demos and benchmarks used to demonstrate the versatility and performance of BrainPy. To address these concerns, we have added more details in the revised paper, including:

• In Fig. 4, we explain how the reservoirs are trained in Appendix 10, in which only the readout weights are trained, and they are trained using backpropagation, FORCE learning, and ridge regression algorithms, respectively. We also specify the number of neurons in each reservoir (see L1397), and the final performance of the reservoirs on the task (see Figure 4).

• To enable readers to better interpret the simulator comparisons in Fig. 8, we have also added more detailed explanations of the comparison with NEURON, NEST, and Brian2 in Appendix 11.

• In the current revised paper, we provide a comprehensive analysis of BrainPy's compatibility with different hardware platforms, including TPUs, and to identify the specific conditions under which TPUs may offer advantages (see Figure 8 and Appendix 11—figure 7 ). We have also discussed the potential benefits of TPUs for biologically-realistic networks (see L514 - L521). Particularly, for the biological network with arbitrary sparsity, TPUs does not show advantage over GPUs (see Appendix 11—figure 7). TPUs are best at exploiting certain kinds of structured sparsity, for example block sparsity.

Author Response

Reviewer #1 (Public Review):

Due complicated and often unpredictable idiosyncratic differences, comparing fMRI topography between subjects typically would require extra expensive scan time and extra laborious analyzing steps to examine with specific functional localizer scan runs that contrast fMRI responses of every subject to different stimulus categories. To overcome this challenge, hyperaligning tools have recently been developed (e.g., Guntupalli et al., 2016; Haxby et al., 2011) based on aligning in a high-dimensional space of voxels of subjects' fMRI responses to watching a given movie. In the present study, Jiahui and colleagues propose a significantly improved version of hyperaligning functional brain topography between individuals. This new version, based on fMRI connectivity, works robustly on datasets when subjects watched different movies and were scanned with different parameters/scanners at different MRI centers.

Robustness is the major strength of this study. Despite the fact that datasets from different subjects watching different movies at different MRI centers with different scan parameters were used, the results of functional brain topography from between-subject hyperalignment based on fMRI connectivity were comparable to the golden standard of within-subject functional localizations, and significantly better than regular surface anatomical alignments. These results also support the claim that the present approach is a useful improvement from previous hyperalignments based on time-locked fMRI voxel responses, which would require normative samples of subjects watching a same movie.

We thank the reviewer for the appreciation of our work.

Given the robustness, this new version of hyperalignment would provide much stronger statistical power for group-level comparisons with less costs of time and efforts to collect and analyze data from large sample size according to the current stringent standard, likely being useful to the whole research community of functional neuroimaging. That said, more discussions of the limit of the present hyperalignment approach would be helpful to potential eLife readers. For example, to what extend the present hyperalignment approach would be applicable to individuals with atypical functional brain topography such as brain lesion patients with e.g., acquired prosopagnosia? Even in typical populations, while bilateral fusiform face areas can be identified in the majority through functional localizer scans, the left fusiform face area sometimes cannot be found. Moreover, many top-down factors are known to modulate functional brain topography. Due to these factors, brain responses and functional connectivity may be different even when a same subject watched a same movie twice (e.g., Cui et al., 2021).

We thank the reviewer for the suggestion and agree that it would be fascinating if the predictions can be made with high fidelity in neuropsychological populations. Although we are optimistic that our algorithm is able to generalize across diverse populations, to date, no previous literature has provided empirical evidence to illustrate the effectiveness, including optimizations and special applications beyond typical brains. Besides the neuropsychological population, it would also be valuable to study the generalization across a broad age range, for example, from infants to the elderly. The brain changes across age both anatomically and functionally, so it is a challenge to predict functional topographies based on a normative group that only includes young participants. With all these potential applications in mind, future research is needed to illustrate the efficacy, build the pipeline, and construct the representative normative groups to meet the requirements of accurate individualized predictions in diverse populations.

In typical populations, although participants have great individual variabilities in their functional topographies, for instance, some participants have distinguishable patches of activations in their left ventral temporal cortex while some participants don’t, our algorithms successfully captured these individualized differences in the prediction. The figure below shows, as an example, the face-selective topographies of two individuals that have markedly different face-selective topographies on the left ventral temporal cortex. The left participant has prominent face-selective areas on the left ventral temporal cortex that are in similar sizes as the right side, while the right participant only has a few scattered small face-selective spots on the left side. No matter what their face-selective areas look like, our algorithm accurately recovered the individualized locations, shapes, and sizes, retaining the individual variability in the functional topographies.

Functional connectivity profiles based on naturalistic stimuli are very stable across the cortex, even when participants watch different movies. In Figure 4-figure supplement 9, the mean correlations of fine-scaled connectome for most searchlights (r = 15mm) when participants watched The Grand Budapest Hotel and the Raiders of the Lost Ark were generally around 0.8. The mean correlations were about 0.9 between the first and second half of the same movie although the stimuli contents were different between the two halves. Thus, the fine-grained functional connectivity profiles remain highly stable and reliable across movie contents, which contributes to the robustness of cross-movie, time, and other parameters (e.g., scanner models, scanning parameter) predictions using our algorithms.

We added a paragraph in the discuss section to address the concerns (page 18-19):

“This study successfully illustrated that accurate individualized predictions are both robust and applicable across a variety of conditions, including movie types, languages, scanning parameters, and scanner models. Importantly, the intricate connectivity profiles remain consistent even when participants view entirely different movies, as evidenced by Figure 4-figure supplement 9, reinforcing the prediction's stability in various scenarios. However, all four datasets in this study only included typical participants with anatomically intact brains. An unanswered question is whether individualized topographies of neuropsychological populations with atypical cortical function (e.g., developmental prosopagnosics) or with lesioned brains (e.g., acquired prosopagnosics) could also be accurately predicted using the hyperalignment-based methods. Up to now, as far as we know, no previous literature has investigated this question. Beyond neuropsychological groups, it is also valuable to investigate how well the predictions will be across a wide range of age, from infants to the elderly. Future research is essential to adapt our algorithms to diverse populations.”

Reviewer #2 (Public Review):

Guo and her colleagues develop a new approach to map the category-selective functional topographies in individual participants based on their movie-viewing fMRI data and functional localizer data from a normative sample. The connectivity hyperalignment are used to derived the transformation matrices between the participants according to their functional connectomes during movies watching. The transformation matrices are then used to project the localizer data from the normative sample into the new participant and create the idiosyncratic cortical topography for the participant. The authors demonstrate that a target participant's individualized category-selective topography can be accurately estimated using connectivity hyperalignment, regardless of whether different movies are used to calculate the connectome and regardless of other data collection parameters. The new approach allows researchers to estimate a broad range of functional topographies based on naturalistic movies and a normative database, making it possible to integrate datasets from laboratories worldwide to map functional areas for individuals. The topic is of broad interest for neuroimaging community; the rationale of the study is straightforward and the experiments were well designed; the results are comprehensive. I have some concerns that the authors may want to address, particularly on the details of the pipeline used to map individual category-selective functional topographies.

We thank the reviewer for the encouragement.

1) How does the length of the scan-length of movie-viewing fMRI affect the accuracy in predicting the idiosyncratic cortical topography? Similarly, how does the number of participants in the normative database affect the prediction of the category-selective topography? This information is important for the researchers who are interested in using the approach in their studies.

To investigate the influence of movie-viewing data length and the number of participants in the normative database on prediction performance, we systematically varied these parameters. Specifically, we altered the number of runs utilized in the analysis for both the normative and target data and experimented with varying the number of participants in the normative dataset using the Budapest and the Sraiders datasets. We have included a new Figure 4-figure supplement 5 to present a summary of these findings.

The results reveal that both within-dataset and between-dataset prediction performances are positively correlated with the length of movie-viewing fMRI data used for both the normative and target groups. A similar trend was observed with respect to the number of participants included in the normative dataset. It is important to highlight, though, that, even when analyzing as little as one run of movie-viewing data—roughly 10-15 minutes, our hyperalignment-based prediction performance was significantly higher than that achieved using traditional surface alignment. This held true even when the normative dataset included as few as five participants.

In summary, our results show that prediction performance generally improves with longer movie-viewing sessions and larger normative datasets. However, it is noteworthy that even with minimal data—10 minutes of movie-viewing and a small number of participants in the normative dataset—our algorithm still outperforms traditional surface alignment methods significantly.

We also added sentences in the discussion section (page 15):

“We investigated the influence of naturalistic movie length and the size of the training group on the prediction accuracy of individualized functional topographies. By incrementally increasing both the number of movie runs in the training and target dataset and the participants in the training group in the Budapest and Sraiders dataset, we observed enhanced prediction accuracy (Figure 4-figure supplement 5). Notably, even with just one movie run in the training or target dataset, or with a mere five participants in the training group, our prediction performance (Pearson r) ranged from about 0.6 to 0.7. This accuracy significantly outperformed results obtained using surface-based alignment.”

2) The data show that category-selective topography can be accurately estimated using connectivity hyperalignment, regardless of whether different movies are used to calculate the connectome and regardless of other data collection parameters. I'm wondering whether the functional connectome from resting state fMRI can do the same job as the movie-watching fMRI. If it is yes, it will expand the approach to broader data.

We agree with the reviewer that demonstrating the applicability of the resting state data will expand the application scenarios of this approach. Most previous findings on resting state connectivity, including the comparison between the naturalistic and the resting state paradigms, focused on the macro-scale similarities and differences (e.g., Samara et al., 2023). Very few studies have investigated the fine-scaled connectome based on resting state data. The study on connectivity hyperalignment (Guntupalli et al., 2018) demonstrated a shared fine-scale connectivity structure among individuals that co-exists with the common coarse-scale structure and built the algorithm to successfully hyperalign individuals to the shared fine-scaled space. Another study from our lab (Feilong et al., 2021) revealed that the fine-scaled connectivity profiles in both resting and task states are highly predictive of general intelligence, indicating reliable and biologically relevant fine-scaled resting state connectome structures. Thus, it is highly plausible that our approach is able to be generalized to the resting state data, generating significantly better predictions of individualized functional topographies than traditional surface alignment. However, due to the limitations of the current datasets, we do not have resting state data available in the current datasets to perform this analysis. We are in the process of collecting new data to explore this hypothesis in future work.

We added sentences to the discussion section to discuss this idea (page 18):

“Studies comparing movie-viewing and resting state functional connectivity have shown that both paradigms yield overlapping macroscale cortical organizations (29), though naturalistic viewing introduces unique modality-specific hierarchical gradients. However, there remains a gap in research comparing the fine-scaled connectomes of naturalistic and resting state paradigms. Guntupalli and colleagues (14) revealed a shared fine-scale structure that coexists with the coarse-scale structure, and connectivity hyperalignment successfully improved intersubject correlations across a wide variety of tasks. Feilong et al. (13) noted that the fine-scaled connectivity profiles in both resting and task states are highly predictive of general intelligence. This suggests a reliable and biologically relevant fine-scale resting state connectivity structure among individuals. Therefore, it is plausible that individualized functional topography could be effectively estimated using resting state functional connectivity, expanding the applicability of our approach. Future studies are needed to explore this direction.”

3) The authors averaged the hyper-aligned functional localizer data from all of subjects to predict individual category-selective topographies. As there are large spatial variability in the functional areas across subjects, averaging the data from many subjects may blur boundaries of the functional areas. A better solution might be to average those subjects who show highly similar connectome to the target subjects.

We appreciate the reviewer’s insightful question about optimizing prediction performance by selecting participants most similar in functional connectivity to the target individuals. This is a promising direction and difficult problem as well. Our approach is based on fine-scale connectome to hyperalign participants, thus different groups of participants may be similar to the target participant in different searchlights. In addition, based on results discussed in the response to Q2, the more participants included in the normative dataset, the better the prediction performance. Thus, there is a trade-off between the number of participants included in the normative dataset for the prediction and the overall similarity of those participants to the target participant.

To quantitatively explore this idea, we used a searchlight in the right ventral temporal cortex, roughly at the location of posterior fusiform face area (pFFA).We sorted participants by their connectome similarity to each target participant and then examined prediction performance based on either the top nine most similar participants or the bottom nine least similar participants. Our results, presented in Figure 4-figure supplement 8, reveal that hyperalignment consistently outperforms surface alignment regardless of the subset of participants used. Notably, using the nine most similar participants did not significantly alter prediction performance (Tukey Test, z = -0.09, p = 0.996), while using the least similar participants did negatively impact it (Tukey Test, z = 2.492, p = 0.034). Interestingly, the stability of hyperalignment-based predictions remained high even when only a subset of participants was used, contrasting with the variability observed in surface-alignment-based predictions.

Overall, these findings suggest that while selecting functionally similar participants is a promising avenue for future optimization, the process will require nuanced, searchlight-specific criteria. Each searchlight may necessitate its own set of optimal participants to balance between the performance boost from having more participants and the fidelity gained from participant similarity.

We added the following to the discussion in the manuscript (page 16):

“In our study, we used fine-scale connectomes, noting that some participants are more similar to the target participant in specific searchlights. It is an interesting question whether predictions could be enhanced by exclusively selecting those more similar participants for the target participant. To explore this option, we examined a searchlight in the right ventral temporal cortex that was roughly at the location of the posterior fusiform area (pFFA) using the top and bottom nine participants similar to each target participant measured by their fine-scale connectome similarities in the budapest dataset. Generally, using all or part of the participants for the prediction generated similar results (Figure 4-figure supplement 8). Compared to using all the participants, using only the top nine participants who are the most similar to the target participants did not significantly improve the prediction (Tukey Test, z = -0.09, p = 0.996), but using only the bottom nine participants generated significantly lower prediction accuracies (Tukey Test, z = 2.492, p = 0.034). This suggests a trade-off between the number of participants included in the prediction and the similarity of the participants. Future studies are needed to explore the optimal threshold for the number of participants included for each searchlight to refine the algorithm.”

4) It is good to see that predictions made with hyperalignment were close to and sometimes even exceeded the reliability values measured by Cronbach's alpha. But, please clarify how the Cronbach's alpha is calculated.

Cronbach’s alpha calculates the correlation score between localizer-based maps across the runs, and it reflects the amount of noise in maps based on individual localizer runs. Traditionally, the reliability was estimated based on split-half correlations. For example, Guntupalli et al. (2016) used correlations of category-selectivity maps between odd and even localizer runs as the measure of reliability. The odd/even split measure underestimated reliability and necessitated recalculation of correlations between maps for only half the data to provide valid comparisons. In contrast, Cronbach’s alpha involves all localizer runs and provides a more accurate statistical estimate of the reliability of the topographies estimated with localizer runs.

Cronbach’s alpha has been used in many previously published works from our lab (e.g., Feilong et al., 2021; Jiahui et al., 2020, 2023). The code for implementing this metric is publicly accessible on the first author’s Github repository (https://github.com/GUOJiahui/face_DCNN/blob/main/code/cronbach_alpha.py).

We added the detailed explanation above to the Material and Methods section (page 24):

“Cronbach’s alpha calculates the correlation score between localizer-based maps across the runs, and it reflects the amount of noise in maps based on individual localizer runs. Traditionally, the reliability was estimated based on split-half correlations. The common odd/even split measure underestimated reliability and necessitated recalculation of correlations between maps for only half the data to provide valid comparisons. In contrast, Cronbach’s alpha involves all localizer runs and provides a more accurate statistical estimate of the reliability of the topographies estimated with localizer runs.”

5) Which algorithm was used to perform surface-based anatomical alignment? Can the state-ofthe-art Multimodal Surface Matching (MSM) algorithm from HCP achieve better performance?

We preprocessed our datasets using fMRIPrep, which employs algorithms from FreeSurfer’s recon-all for surface-based anatomical alignment. It is worth noting that different alignment methods can yield varying degrees of performance. For instance, a study by Coalson et al. (2018) compared the localization performance of multiple surface-based alignment methods, including Multimodal Surface Matching (MSM) and FreeSurfer. The study found that MSM outperformed FreeSurfer in terms of peak probabilities and spatial clustering, suggesting better overall localization.

Additionally, Guntupalli et al. (2018) evaluated intersubject correlations (ISC) of functional connectivity from movie-viewing data using both Connectivity Hyperalignment (CHA) and MSM-All with the Human Connectome Project (HCP) dataset. The study showed that although MSM-All yielded marginally better ISC than traditional surface alignment, CHA’s performance was significantly superior.

In summary, while using a more advanced alignment algorithm like MSM could marginally improve prediction performance, its advantages may not be substantial when compared to our CHA-based predictions. The combination of MSM and CHA represents an intriguing direction for future research, although it falls outside the scope of our current study.

6) Is it necessary to project to the time course of the functional localizer from the normative sample into the new participants? Does it work if we just project the contrast maps from the normative samples to the new subjects?

It is an interesting question and a practical alternative to researchers to know whether time series of the localizer runs are required to obtain reasonable predictions, as in some scenarios, contrast maps may be the only accessible data in the analysis. To quantitatively explore this possibility, we applied transformation matrices derived from the movie data to training participants’s individual pre-calculated contrast maps of all four categories, and evaluated the predictions. We found nearly similar prediction performance between the two flavors within and across datasets (Figure 4-figure supplement 7). However, it is worth noting that applying transformation matrices directly to contrast maps did not get as much improvement in the interactive steps as the other flavor in the advanced CHA, perhaps due to the scale changes when multiple iterations were implemented and the difficulty to properly normalize the t-maps compared to the regular time series.

Overall, although our algorithm is originally designed to be used on the time course of the functional localizer runs, relatively comparable results can be generated even when the contrast maps are directly projected from the normative group to the target participant. However, to derive the best results with our approach, time series are recommended when the situation permits.

We have also added the contents into the Discussion section (page 16):

“Our original algorithm is designed to apply transformation matrices to the time series of localizer data of training participants before generating contrast maps. To explore whether directly applying these matrices to pre-calculated contrast maps yields comparable results, we conducted an additional analysis across the four categories. Our findings indicate that the prediction outcomes were indeed quite similar between the two approaches for both the within- and across-datasets predictions (Figure 4-figure supplement 7). However, it is worth noting that the improvements observed with enhanced CHA were not as pronounced when applied directly to the contrast maps as opposed to the time series.”

7) Saygin and her colleagues have demonstrated that structural connectivity fingerprints can predict cortical selectivity for multiple visual categories across cortex (Osher DE et al, 2016, Cerebral Cortex; Saygin et al, 2011, Nat. Neurosci). I think there's a connection between those studies and the current study. If the author can discuss the connection between them, it may help us understand why CHA work so well.

We thank the reviewer for raising this point that provides us with the chance of clarifying how our approach differs with methods previously reported in the literature. The computational logic underlying our approach is that we derived the transformation matrices between the training and the target participants in the high-dimensional space based on functional connectivity calculated from the movie data. Then, we applied these transformation matrices to the training participant’s localizer data to accomplish the prediction. On the other hand, Saygin and colleagues directly used diffusion-weighted imaging (DWI) data and predicted participants’ functional responses based on the anatomical-functional correspondence. They evaluated the prediction by calculating the mean absolute errors (AE) of the difference between the actual and predicted contrast responses. Although AE linearly increases with the quality of the prediction, it is difficult to measure the prediction performance of the shape, size, and location of the functional areas precisely using this mean value. With our algorithm, we were able to predict the general location and size of the areas and recover the individualized shapes, generating more powerful predictions. We also used the searchlight analysis to evaluate the performance across the cortex systematically. In addition, Osher et al. (2016) and Saygin et al. (2012) always have a few participants failing to show better predictions based on the connectivity than the group averaged method. Our algorithm is more stable, as all participants across all four datasets had better predicted performance using our algorithm than using the group average. However, although we did not directly use the anatomical-functional correspondence with DWI, the relationships between individual structural connectivity and cortical visual category selectivity could be one of the biological underpinnings that contribute to this robust and accurate prediction.

The Connectivity-Based Shared Response Model (cSRM, Nastase et al., 2020) offers an alternative framework for aligning individuals through functional connectivity. While the overarching aim of cSRM and our methodology converges, substantial differences emerge in the respective implementation and application between the two methods that make our approach the more suitable for predicting individualized topographies. The most significant difference between the two is that, instead of focusing on within-individual connectivity profiles, cSRM used inter-subject functional connectivity (ISFC) in the initial step. This design requires that all participants must have time-locked time series, making the algorithm unusable for cross-content prediction and making it incompatible with resting-state data. Our approach, on the other hand, does not require time-locked stimuli, thereby offering a more flexible framework that permits generalization across different types of stimuli and experimental settings and enables bringing data across laboratories across the world together. Secondly, cSRM predominantly focuses on Region of Interest (ROI) analyses, whereas our model employs searchlight-based analyses designed to comprehensively cover the entire cortical sheet. Whole-brain coverage is needed to generate the topography that reflects the patterns across the cortex. Finally, with the optimized 1step method, our approach directly hyeraligns the training and target participants together, avoiding the accumulation of errors from the intermediate common space. cSRM, with an implementation similar to the classic connectivity hyperalignment, creates and hyperaligns all participants to a shared information space. In summary, while our approach and cSRM share a similar theoretical foundation, our approach has been specifically optimized to address the challenges and complexities in predicting individualized whole-brain functional topographies. Moreover, our approach demonstrates a remarkable ability to generalize across a variety of contexts and stimuli, offering a significant advantage in dealing with diverse experimental settings and datasets.

We have added the contents to the discussion section (page 16-17):

“By leveraging transformation matrices obtained from hyperaligning participants based on movie-viewing data, we successfully mapped these relationships to the training participants’ localizer data, enabling robust predictions. Prior work employing diffusion-weighted imaging (DWI) has underscored the link between anatomical connectivity and category selectivity across diverse visual fields (22, 23) and has established a notable congruence between structural and functional connectivities (24). These findings suggest that the unique anatomical connectivity patterns of individuals may serve as a foundational mechanism, contributing to the stable finescale functional connectome that underpins our approach. The connectivity-based Shared Response Model (cSRM) proposed by Nastase and colleagues (25) used connectivity to functionally align individuals similar to the connectivity hyperalignment algorithm. While both approaches share overarching goals, they diverge considerably in implementation and application. First and most important, cSRM used inter-subject functional connectivity (ISFC) rather than within-subject functional connectivity to initially estimate the connectome. As a result, cSRM requires participants to have time-locked fMRI time series. Therefore, unlike our algorithm, the cSRM approach does not support cross-content applications and also is not suitable for use with resting-state data. Second, cSRM is implemented based on a predefined cortical parcellation rather than the overlapping, regularly-spaced cortical searchlights applied in our method which are not constrained by areal borders. For the application, cSRM has mainly been used to do ROI analysis rather than the estimation of the whole-brain topography that requires broader coverage of the cortex with a searchlight analysis. Third, our method is specifically designed to work in each individual’s space, while cSRM decomposes data across subjects into shared and subjectspecific transformations, focusing on a communal connectivity space. In summary, although cSRM presents a promising alternative for similar aims, its current implementation precludes it from fulfilling the range of applications for which our method is optimized.”

Reviewer #3 (Public Review):

In this paper, Jiahui and colleagues propose a new method for learning individual-specific functional resonance imaging (fMRI) patterns from naturalistic stimuli, extending existing hyperalignment methods. They evaluate this method - enhanced connectivity hyperalignment (CHA) - across four datasets, each comprising between nine (Raiders) and twenty (Budapest, Sraiders) participants.

The work promises to address a significant need in existing functional alignment methods: while hyperalignment and related methods have been increasingly used in the field to compare participants scanned with overlapping stimuli (or lack thereof, in the case of resting state data), their use remains largely tied to naturalistic stimuli. In this case, having non-overlapping stimuli is a significant constraint on application, as many researchers may have access to only partially overlapping stimuli or wish to compare stimuli acquired under different protocols and at different sites.

It is surprising, however, that the authors do not cite a paper that has already successfully demonstrated a functional alignment method that can address exactly this need: a connectivitybased Shared Response Model (cSRM; Nastase et al., 2020, NeuroImage). It would be relevant for the authors to consider the cSRM method in relation to their enhanced CHA method in detail. In particular, both the relative predictive performance as well as associated computational costs would be useful for researchers to understand in considering enhanced CHA for their applications.

We thank the reviewer for raising this point that provides us with the chance of clarifying how our approach differs with methods previously reported in the literature. The computational logic underlying our approach is that we derived the transformation matrices between the training and the target participants in the high-dimensional space based on functional connectivity calculated from the movie data. Then, we applied these transformation matrices to the training participant’s localizer data to accomplish the prediction. On the other hand, Saygin and colleagues directly used diffusion-weighted imaging (DWI) data and predicted participants’ functional responses based on the anatomical-functional correspondence. They evaluated the prediction by calculating the mean absolute errors (AE) of the difference between the actual and predicted contrast responses. Although AE linearly increases with the quality of the prediction, it is difficult to measure the prediction performance of the shape, size, and location of the functional areas precisely using this mean value. With our algorithm, we were able to predict the general location and size of the areas and recover the individualized shapes, generating more powerful predictions. We also used the searchlight analysis to evaluate the performance across the cortex systematically. In addition, Osher et al. (2016) and Saygin et al. (2012) always have a few participants failing to show better predictions based on the connectivity than the group averaged method. Our algorithm is more stable, as all participants across all four datasets had better predicted performance using our algorithm than using the group average. However, although we did not directly use the anatomical-functional correspondence with DWI, the relationships between individual structural connectivity and cortical visual category selectivity could be one of the biological underpinnings that contribute to this robust and accurate prediction.

The Connectivity-Based Shared Response Model (cSRM, Nastase et al., 2020) offers an alternative framework for aligning individuals through functional connectivity. While the overarching aim of cSRM and our methodology converges, substantial differences emerge in the respective implementation and application between the two methods that make our approach the more suitable for predicting individualized topographies. The most significant difference between the two is that, instead of focusing on within-individual connectivity profiles, cSRM used inter-subject functional connectivity (ISFC) in the initial step. This design requires that all participants must have time-locked time series, making the algorithm unusable for cross-content prediction and making it incompatible with resting-state data. Our approach, on the other hand, does not require time-locked stimuli, thereby offering a more flexible framework that permits generalization across different types of stimuli and experimental settings and enables bringing data across laboratories across the world together. Secondly, cSRM predominantly focuses on Region of Interest (ROI) analyses, whereas our model employs searchlight-based analyses designed to comprehensively cover the entire cortical sheet. Whole-brain coverage is needed to generate the topography that reflects the patterns across the cortex. Finally, with the optimized 1step method, our approach directly hyeraligns the training and target participants together, avoiding the accumulation of errors from the intermediate common space. cSRM, with an implementation similar to the classic connectivity hyperalignment, creates and hyperaligns all participants to a shared information space. In summary, while our approach and cSRM share a similar theoretical foundation, our approach has been specifically optimized to address the challenges and complexities in predicting individualized whole-brain functional topographies. Moreover, our approach demonstrates a remarkable ability to generalize across a variety of contexts and stimuli, offering a significant advantage in dealing with diverse experimental settings and datasets.

We have added the contents to the discussion section (page 16-17):

“By leveraging transformation matrices obtained from hyperaligning participants based on movie-viewing data, we successfully mapped these relationships to the training participants’ localizer data, enabling robust predictions. Prior work employing diffusion-weighted imaging (DWI) has underscored the link between anatomical connectivity and category selectivity across diverse visual fields (22, 23) and has established a notable congruence between structural and functional connectivities (24). These findings suggest that the unique anatomical connectivity patterns of individuals may serve as a foundational mechanism, contributing to the stable finescale functional connectome that underpins our approach. The connectivity-based Shared Response Model (cSRM) proposed by Nastase and colleagues (25) used connectivity to functionally align individuals similar to the connectivity hyperalignment algorithm. While both approaches share overarching goals, they diverge considerably in implementation and application. First and most important, cSRM used inter-subject functional connectivity (ISFC) rather than within-subject functional connectivity to initially estimate the connectome. As a result, cSRM requires participants to have time-locked fMRI time series. Therefore, unlike our algorithm, the cSRM approach does not support cross-content applications and also is not suitable for use with resting-state data. Second, cSRM is implemented based on a predefined cortical parcellation rather than the overlapping, regularly-spaced cortical searchlights applied in our method which are not constrained by areal borders. For the application, cSRM has mainly been used to do ROI analysis rather than the estimation of the whole-brain topography that requires broader coverage of the cortex with a searchlight analysis. Third, our method is specifically designed to work in each individual’s space, while cSRM decomposes data across subjects into shared and subjectspecific transformations, focusing on a communal connectivity space. In summary, although cSRM presents a promising alternative for similar aims, its current implementation precludes it from fulfilling the range of applications for which our method is optimized.”

With this in mind, I noted several current weaknesses in the paper:

First, while the enhanced CHA method is a promising update on existing CHA techniques, it is unclear why this particular six step, iterative approach was adopted. That is: why was six steps chosen over any other number? At present, it is not clear if there is an explicit loss function that the authors are minimizing over their iterations. The relative computational cost of six iterations is also likely significant, particularly compared to previous hyperalignment algorithms. A more detailed theoretical understanding of why six iterations are necessary-or if other researchers could adopt a variable number according to the characteristics of their data-would significantly improve the transferability of this method.

In the advanced connectivity hyperalignment implementation, we gradually increased the number of targets. The six steps were not intentionally chosen but were the result of the increase to the maximum number of fine-grained targets, namely single cortical vertices.

Our datasets were resampled to the cortical mesh with 18,742 vertices across both hemispheres (approximately 3 mm vertex spacing; icoorder 5; 20,484 vertices before removing non-cortical vertices). Step 1 was the classic standard connectivity hyperalignment implementation based on the anatomically-aligned data. Since using dense connectivity targets (e.g., using all 18742 vertices on the surface) with anatomically-aligned data generates poor functional correspondence across participants (Busch et al., 2021), we used 1,284 vertices (icoorder 3, before removing the medial wall) as connectivity targets in step 1. However, it is beneficial to include more targets for calculating connectivity patterns after the first iteration of connectivity hyperalignment and repeated iterations to lead to a better solution by gradually aligning the information at finer scales. To better align across participants, we iterated the alignment for another two times (step 2 and step 3) with the same number of 1,284 coarse connectivity targets to ensure improved alignment before increasing the number of targets in the later steps. In step 4, we increased the number of targets to 5,124 (icoorder 4, before removing the medial wall), and iterated with this number of vertices for two times in total (step 4 & step 5) before using all vertices as targets. In the final step (step 6), all vertices were used as connectivity targets.

It is true that the multiple iteration steps largely increased the computational complexity compared to the classic connectivity hyperalignment, but the prediction increase was steady across all datasets and became comparable to response hyperalignment performance which requires time-locked stimuli. We did not use an explicit loss function in the algorithm, but followed the natural progression of the number of potential connectivity targets in the implementation. On the other hand, the difference between the performance of the improved and the classic connectivity hyperalignment was relatively small (difference of r < 0.05), which indicates the effectiveness of our classic algorithm. It is up to the researchers’ own options to adopt the number of iterations and the pace of increasing the number of targets in each step. If computational resources are limited or if a shorter total computational time is the primary priority, using the classic connectivity hyperalignment may be the best option to balance the trade-offs.

The Materials and Methods section had the details of the implementation (page 22-23):

“Using dense connectivity targets (e.g., using all 18742 vertices on the surface) with anatomically-aligned data usually generates poor functional correspondence across participants (33). It is, however, beneficial to include more targets for calculating connectivity patterns after the first iteration of connectivity hyperalignment and repeated iterations to lead to a better solution by gradually aligning the information at finer scales.

We used six steps to further improve the connectivity hyperalignment method. Step 1 was the initial connectivity hyperalignment step as described above that was based on the raw anatomically aligned movie data. The resultant transformation matrices were applied to those movie runs, and the hyperaligned data were then used in step 2 to calculate new connectivity patterns and calculate new transformation matrices. We repeated this procedure iteratively six times and derived transformation matrices for each step. In steps 1, 2, and 3, 642 × 2 (icoorder3, before removing the medial wall) connectivity targets were defined with 13 mm searchlights. In step 4 and 5, 2562 × 2 (icoorder 4, before removing the medial wall) connectivity targets were used with 7 mm searchlights to calculate target mean time series. In the final step 6, all 18742 vertices were included as separate connectivity targets, using each vertex’s time series rather than calculating the mean in a searchlight. Each step of this advanced connectivity hyperalignment algorithm increased the prediction performance (Figure 4-figure supplement 2).”

But to help the readers understand the logic of the advanced connectivity hyperalignment algorithm used in this study, we expanded the discussion section (page 15):

“Because using dense connectivity targets (e.g., using all vertices as connectivity targets) with anatomically-alignment data often leads to suboptimal alignment across participants (33), we started with coarse connectivity targets and gradually increased the number of connectivity targets to form a denser representation of connectivity profiles. The iterations improved the prediction performance step by step, and at the final step (step 6, all vertices were used as connectivity targets) in this analysis, the enhanced CHA generated comparable performance with RHA (Figure 4-figure supplement 4).”

Second, the existing evaluations for enhanced CHA appear to be entirely based on imagederived correlations. That is, the authors compare the predicted image from CHA with the ground-truth image using correlation. While this provides promising initial evidence, correlation-based measures are often difficult to interpret given their sensitivity to image characteristics such as smoothness. Including Cronbach's alpha reliability as a baseline does not address this concern, as it is similarly an image-based statistic. It would be useful to see additional predictive experiments using frameworks such as time-segment classification, intersubject decoding, or encoding models.

We appreciate the reviewer’s concern regarding the stability of local correlations in relation to image characteristics. To address this, we conducted additional analysis using different searchlight sizes (with radii of 10 mm, 15 mm, and 20 mm) to evaluate the predicted categoryselective maps, focusing specifically on the Budapest dataset. The local correlations between the predicted category-selective maps (obtained using enhanced CHA) and participants’ own maps based on classic localizer runs were calculated for each searchlight. We averaged these correlations across participants and plotted the resulting maps, as shown in Figure 4-figure supplement 10. Although using a larger searchlight radius is similar to employing a larger smoothing kernel, the results remained relatively stable across different searchlight sizes, particularly in regions selectively responsive to the specific category. This stability suggests that while the evaluation may be influenced by image-related features, the conclusion would remain consistent under varying parameters.

As for the use of enhanced CHA, it serves as an optimized version of the classic CHA, specifically designed for predicting individualized functional topographies. Evaluating prediction performance in our study is based on t-value contrast maps for each participant. Given this, it's unclear how time-segment classification or other decoding/encoding models could be appropriately implemented for performance evaluation. However, prior research from our lab has already established the effectiveness of classic CHA. Specifically, Guntupalli et al. (2018) showed that classic CHA significantly improved intersubject correlations (ISC) of connectivity profiles across the cortex. They also revealed that CHA captured fine-scale variations in connectivity profiles for nearby cortical nodes across participants and led to improved betweensubject multivariate pattern classification accuracies (bsMVPC) of movie segments. These findings serve as robust evidence for the effectiveness of classic CHA, laying the groundwork for our enhanced CHA approach.

We added Figure 4-figure supplement 10 to the supplementary material:

Addressing these concerns and considering cSRM as a comparison model would significantly strengthen the paper. There are also notable strengths that I would encourage the authors to further pursue. In particular, the authors have access to a unique dataset in which the same Raiders of the Lost Ark stimulus was scanned for participants within the Budapest (SRaiders) dataset as well as non-overlapping participants in the Raiders dataset. Exploring the relative performance for cross-movie prediction within a dataset as compared to a shared movie prediction across datasets is particularly interesting for methods development. I would encourage the authors to explicitly report results in this framework to highlight both this unique testing structure as well as the performance of their enhanced CHA method.

We appreciate the reviewer's suggestion to examine a shared time-series but non-overlapping participants scenario using the Sraiders and Raiders datasets. However, there are significant differences between the two datasets that preclude such direct comparison. These differences include varying scanning parameters, MRI scanners, localizer types, and data collection procedures. Due to these methodological divergences, the datasets cannot be treated as identical time-series.

Firstly, the scanning parameters vary considerably. Sraiders were scanned with TR = 1 s (TR/TE = 1000/33 ms, flip angle = 59 °, resolution = 2.5 mm3 isotropic voxels, matrix size = 96 × 96, FoV = 240 × 240 mm, multiband acceleration factor = 4, and no in-plane acceleration), and Raiders were scanned with TR = 2.5 s (TR = 2.5 s, TE = 35 ms, Flip angle = 90°, 80 × 80 matrix, FOV = 240 mm × 240 mm, resolution = 0.938 mm × 0.938 mm × 1.0 mm).

Secondly, participants in the Sraiders were scanned with a 3 T S Magnetom Prisma MRI scanner with a 32 channel head coil and the Raiders dataset, collected more than 10 years ago, used a 3T Philips Intera Achieva scanner with an eight-channel head coil.

Thirdly, the stimuli presentations were different. In the Sraiders dataset, the movie Raiders of the Lost Ark was split into eight parts (~15 min each), and the first four parts were watched outside of the scanner prior to the scanning (~56 min). The later four parts were watched in the scanner (57 min) with audio. And in the Raiders dataset, the audio-visual movie was split into eight parts (~15 min each). Participants watched all eight parts in the scanner with audio (one part / per run).

Fourthly and critically, the two datasets included two types of localizers. The Sraiders dataset included dynamic localizer runs, and the Raiders dataset only contained a static localizer that was similarly designed as in the Forrest dataset.

With all four points, it is not suitable to treat the two datasets as identical time-series. The difference in the localizer type is a further issue. The topographies generated from the two types of localizers are dissimilar in many ways. For all categories, the dynamic localizer elicited stronger and broader category-selective activations than the static localizer, and the searchlight analysis showed that the dynamic localizer had higher reliabilities across the cortex, especially in regions that were selectively responsive to the target category. Due to these differences, crossdataset predictions yielded lower correlations than within-dataset predictions. This is not indicative of methodological failure but reflects diverging topographies activated by different localizers.

In the manuscript, we have extensively analyzed cross-dataset predictions (Figure 2-figure supplement 1-Figure 4-figure supplement 4 & 6).

● Figure 2-figure supplement 1 demonstrates that, despite the limitations of cross-localizertype evaluation, both R-to-S (Raiders to Sraiders) and S-to-R (Sraiders to Raiders) predictions significantly outperformed surface alignment methods across categories.

● Figure Figure 2-figure supplement 2 confirms that the prediction performance remained stable across individual participants, underscoring the robustness of our methodology.

● Figure 3-figure supplement 1 & Figure 3-figure supplement 2 display contrast maps generated from both native and alternate localizers, revealing that the maps share similar topographies irrespective of the dataset origin.

● Figure 4-figure supplement 1 presents a correlation analysis of local similarities in R-to-S and S-to-R predictions, highlighting particularly strong correlations in the ventral face regions.

● Figure 4-figure supplement 2 employs histograms to showcase performance across major cortices and furnishes additional evidence regarding the influence of localizer types on the results.

● Figure 4-figure supplement 3 offers a searchlight analysis for other categories, enriching the scope of our investigation.

● Figure 4-figure supplement 4 affirms that the advanced CHA is effective in both R-to-S and S-to-R predictions.

● Figure 4-figure supplement 6 compares the efficacy of 1-step vs. 2-step prediction methods for R-to-S and S-to-R, showing a clear advantage for the 1-step approach.

These analyses affirmed that our approach outperforms surface alignment methods. But the inherent limitations in data collection and localizer types preclude a direct exploration of the reviewer’s hypothesis. These complexities necessitate further research to fully validate the proposed scenario.

Overall, I share the authors' enthusiasm for the potential of cross-movie, cross-dataset prediction, and I believe that methods such as enhanced CHA are likely to significantly improve our ability to make these comparisons in the near future. At present, however, I find that the theoretical and experimental support for enhanced CHA is incomplete. It is therefore difficult to assess how enhanced CHA meets its goals or how successfully other researchers would be able to adopt this method in their own experiments.

We hope our new analysis and replies addressed the reviewer’s concerns.

Author Response

Reviewer #1 (Public Review):

In this study, the authors describe an elegant genetic screen for mutants that suppress defects of MCT1 deletions which are deficient in mitochondrial fatty acid synthesis. This screen identified many genes, including that for Sit4. In addition, genes for retrograde signaling factors (Rtg1, Rtg2 and Rtg3), proteins influencing proteasomal degradation (Rpn4, Ubc4) or ribosomal proteins (Rps17A, Rps29A) were found. From this mix of components, the authors selected Sit4 for further analysis. In the first part of the study, they analyzed the effect of Sit4 in context of MCT1 mutant suppression. This more specific part is very detailed and thorough, the experiments are well controlled and convincing. The second, more general part of the study focused on the effect of Sit4 on the level of the mitochondrial membrane potential. This part is of high general interest, but less well developed. Nevertheless, this study is very interesting as it shows for the first time that phosphate export from mitochondrial is of general relevance for the membrane potential even in wild type cells (as long as they live from fermentation), that the Sit4 phosphatase is critical for this process and that the modulation of Sit4 activity influences processes relying on the membrane potential, such as the import of proteins into mitochondria. However, some aspects should be further clarified.

1) It is not clear whether Sit4 is only relevant under fermentative conditions. Does Sit4 also influence the membrane potential in respiring cells? Fig. S2D shows the membrane potential in glucose and raffinose. Both carbon sources lead to fermentative growths. The authors should also test whether Sit4 levels influence the membrane potential when cells are grown under respirative conditions, such in ethanol, lactate or glycerol. Even if deletions of Sit4 affect respiration, mutants with altered activity can be easily analyzed.

sit4Δ cells fail to grow on nonfermentable media as shown by us (Figure 2—figure supplement 1C) and others (Arndt et al., 1989; Dimmer et al., 2002; Jablonka et al., 2006). In our opinion, the exact reason is unclear, but there is an interesting observation that addition of aspartate can partially restore growth on ethanol (Jablonka et al., 2006). Despite the lack of thorough investigation on this sit4Δ defect, an early study speculated that this defect could be related to the cAMP-PKA pathway (Sutton et al., 1991). This study pointed out genetic interactions of SIT4 with multiple genes in cAMP-PKA (Sutton et al., 1991). In addition, sit4Δ cells have similar phenotypes as those cAMP-PKA null mutants, such as glycogen accumulation, caffeine resistant, and failure to grow on nonfermentable media (Sutton et al., 1991). We have not found sit4Δ mutants that could grow on nonfermentable media based on literature search.

2) The authors should give a name to the pathway shown in Fig. 4D. This would make it easier to follow the text in the results and the discussion. This pathway was proposed and characterized in the 90s by George Clark-Walker and others, but never carefully studied on a mechanistic level. Even if the flux through this pathway cannot be measured in this study, the regulatory role of Sit4 for this process is the most important aspect of this manuscript.

We now refer this mechanism as the mitochondrial ATP hydrolysis pathway.

3) To further support their hypothesis, the authors should show that deletion of Pic1 or Atp1 wipes out the effect of a Sit4 deletion. In these petite-negative mutants, the phosphate export cycle cannot be carried out and thus, Sit4, should have no effect.

The mitochondrial phosphate transport activity is electroneutral as it also pumps a proton together with inorganic phosphate. The F1 subunit of the ATP synthase (Atp1 and Atp2) is suggested among many literatures to be responsible for the ATP hydrolysis. We performed tetrad dissection to generate atp1Δ or atp2Δ in pho85Δ background. After streaking the single colony to a fresh plate, we noticed that atp1Δ mct1Δ and atp2Δ mct1Δ cells are lethal, and knocking out PHO85 rescued this synthetic lethality. It is not surprising that atp1Δ mct1Δ or atp2Δ mct1 Δ cells are lethal since the F1 subunit is important to generate a minimum of MMP in mct1 Δ cells when the ETC is absent (i.e., rho0 cells). However, knocking out PHO85 can generate MMP independent of F1 subunit of ATP synthase, which is suggested by the viable atp1Δ mct1Δ pho85Δ and atp2Δ mct1Δ pho85Δ cells. There are many ATPases in the mitochondrial matrix that could hydrolyze ATP for ADP/ATP carrier to generate MMP theoretically. However, we do not currently know exactly which ATPase(s) is activated by phosphate starvation. This data is now included as Figure 5—figure supplement 1F-G.

4) What is the relevance of Sit4 for the Hap complex which regulates OXPHOS gene expression in yeast? The supplemental table suggests that Hap4 is strongly influenced by Sit4. Is this downstream of the proposed role in phosphate metabolism or a parallel Sit4 activity? This is a crucial point that should be addressed experimentally.

To investigate the role of the Hap complex in MMP generation in sit4Δ cells, we overexpressed and knocked out HAP4, the catalytic subunit of the Hap complex, separately in wild-type and sit4Δ cells. We confirmed the HAP4 overexpression by the enriched abundance of ETC complexes as shown in the BN-PAGE (Figure 2—figure supplement 1E). However, we did not observe any rescue of ETC or ATP synthase in mct1Δ cells when HAP4 was overexpressed. The enriched level of ETC complexes by HAP4 overexpress is not sufficient to rescue the MMP (Figure 2—figure supplement 1F).

Next, we knocked out HAP4 in sit4Δ cells. Knocking out SIT4 could still increase MMP in hap4Δ cells with a much-reduced magnitude, which phenocopied ETC subunit and RPO41 deletion in sit4Δ cells (Figure 2—figure supplement 1G).

In conclusion, the Hap complex is involved in the MMP increase when SIT4 is absent. However, it is not sufficient to increase MMP by overexpressing HAP4. The Hap complex discussion is now included in the manuscript, and the data is presented as Figure 2—figure supplement 1E-G.

5) The authors use the accumulation of Ilv2 precursors as proxy for mitochondrial protein import efficiency. Ilv2 was reported before as a protein which, if import into mitochondria is slow, is deviated into the nucleus in order to be degraded (Shakya,..., Hughes. 2021, Elife). Is it possible that the accumulation of the precursor is the result of a reduced degradation of pre-Ilv2 in the nucleus rather than an impaired mitochondrial import? Since a number of components of the ubiquitin-proteasome system were identified with Sit4 in the same screen, a role of Sit4 in proteasomal degradation seems possible. This should be tested.

We thank the reviewer for pointing out this potential caveat with our Ilv2-FLAG reporter. With limited search and tests, we could not find another reporter that behaves like Ilv2FLAG. The reason Ilv2-FLAG is a perfect reporter for this study is because in wild-type cells, Ilv2-FLAG is not 100% imported. Therefore, we could demonstrate that mitochondria with higher MMP import more efficiently. Unfortunately, all of the mitochondrial proteins that we tested could efficiently import in wild-type cells. To identify other suitable mitochondrial proteins that behave like Ilv2-FLAG, we would need to conduct a more comprehensive screen.

To address the concern of the involvement of protein degradation in obscuring the interpretation of Ilv2-FLAG import, we performed two experiments. First, we measured the proteasomal activity in wild-type and our mutants using a commercial kit (Cayman). We did not observe a statistically significant difference in 20S proteasomal activity between wild-type and sit4Δ cells.

In the second experiment, we reduced the MMP of sit4 cells using CCCP treatment and measured the Ilv2-FLAG import. We first treated sit4Δ cells with different dosage of CCCP for six hours and measured their MMP. sit4Δ cells treated with 75 µM CCCP had comparable MMP to wild-type cells. When we treated sit4Δ cells with higher concentrations of CCCP, most of the cells did not survive after six hours. Next, we performed the Ilv2-FLAG import assay. We observed similar level of unimported Ilv2FLAG (marked with *) in sit4Δ cells treated with 75 µM CCCP. This result confirms that sit4Δ cells have similar Ilv2-FLAG turnover mechanism and activity as the wild-type cells, because when we lower the MMP in sit4Δ background we observe a similar level of unimported Ilv2-FLAG. We thus feel confident in concluding that the Ilv2-FLAG import results are indeed an accurate proxy for MMP level. These data are now included as Figure 1—figure supplement 1H-J in the manuscript.

Author response image 1.

Reviewer #2 (Public Review):

This study reports interesting findings on the influence of a conserved phosphatase on mitochondrial biogenesis and function. In the absence of it, many nucleus-encoded mitochondrial proteins among which those involved in ATP generation are expressed much better than in normal cells. In addition to a better understanding of th mechanisms that regulate mitochondrial function, this work may help developing therapeutic strategies to diseases caused by mitochondrial dysfunction. However there are a number of issues that need clarification.

1) The rationale of the screening assay to identify genes required for the gene expression modifications observed in mct1 mutant is not clear. Indeed, after crossing with the gene deletion libray, the cells become heterozygote for the mct1 deletion and should no longer be deficient in mtFAS. Thank you for clarifying this and if needed adjust the figure S1D to indicate that the mated cells are heterozygous for the mct1 and xxx mutations.

We updated the methods section and the graphic for the genetic screen to clarify these points within the SGA workflow overview. After we created the heterozygote by mating mct1Δ cells with the individual KO cells in the collection, these diploids underwent sporulation and selection for the desired double KO haploid. As a result, the luciferase assay was performed in haploid cells with MCT1 and one additional non-essential gene deleted.

2) The tests shown in Fig. S1E should be repeated on individual subclones (at least 100) obtained after plating for single colonies a glucose culture of mct1 mutant, to determine the proportion of cells with functional (rho+) mtDNA in the mct1 glucose and raffinose cultures. With for instance a 50% proportion of rho- cells, this could substantially influence the results of the analyses made with these cells (including those aiming to evaluate the MMP).

We agree that this would provide a more confident estimate for population-level characterization of these colonies. It is important to note that we randomly chose 10 individual subclones, and 100% of these colonies were verified to be rho+. This suggests the population has functional mtDNA, and thus felt confident in the identity of our populations.

3) The mitochondria area in mct1 cells (Fig.S1G) does not seem to be consistent with the tests in Fig. 1C. that indicate a diminished mitochondrial content in mct1 cells vs wild-type yeast. A better estimate (by WB for instance) of the mitochondrial content in the analyzed strains would enable to better evaluate MMP changes monitored with Mitotracker since the amount of mitochondria in cells correlate with the intensity of the fluorescence signal.

As this reviewer pointed out, we quantified mitochondrial area based on Tom70-GFP signal. This measurement is quantified by mitochondrial area over cell size. Cell size is an important parameter when measuring organelle size as most of the organelles scale up and down with the cell size. mct1Δ cells generally have smaller cell size than WT cells. Therefore, the mitochondrial area of mct1Δ cells was not significantly different from WT cells when scaled to cell size. We believe this is the best method to compare mitochondrial area. As for quantifying MMP from these microscopy images, we measured the average MitoTracker Red fluorescence intensity of each mitochondria defined by Tom70-GFP. This method inherently normalizes to subtract the influence of mitochondria area when quantifying MMP.

4) Page 12: "These data demonstrate that loss of SIT4 results in a mitochondrial phenotype suggestive of an enhanced energetic state: higher membrane potential, hyper-tubulated morphology and more effective protein import." Furthermore, the sit4 mutant shows higher levels of OXPHOS complexes compared to WT yeast.

Despite these beneficial effects on mitochondria, the sit4 deletion strain fails to grow on respiratory substrates. It would be good to know whether the authors have some explanation for this apparent contradiction.

We agree that this was initially puzzling. We provide a more complete explanation above (see comments to reviewer #1 - major concern #1). Briefly, the growth deficiency in non-fermentable media with sit4Δ cells was reported and studied by multiple groups (Arndt et al., 1989; Dimmer et al., 2002; Jablonka et al., 2006). These seems to indicate that sit4Δ cells contain more ETC complexes and more OCR but cannot respire on nonfermentable carbon source. However, we do not think there is yet a clear explanation for this phenotype. One interesting observation reported is the addition of aspartate partly restoring cells’ growth on ethanol (Jablonka et al., 2006). One early study speculates that this defect could be related to the cAMP-PKA pathway. Sutton et al. pointed out genetic interactions with sit4 and multiple genes in cAMP-PKA (Sutton et al., 1991). In addition, sit4Δ cells have similar phenotypes as those cAMP-PKA null mutants, such as glycogen accumulation, caffeine resistance, and failure to grow on non-fermentable media. However, to keep this manuscript succinct, we opted to stay focused on MMP.

Reviewer #3 (Public Review):

In this study, the authors investigate the genetic and environmental causes of elevated Mitochondrial Membrane Potential (MMP) in yeast, and also some physiological effects correlated with increased MMP.

The study begins with a reanalysis of transcriptional data from a yeast mutant lacking the gene MCT1 whose deletion has been shown to cause defects in mitochondrial fatty acid synthesis. The authors note that in raffinose mct1del cells, unlike WT cells, fail to induce expression of many genes that code for subunits of the Electron Transport Chain (ETC) and ATP synthase. The deletion of MCT1 also causes induction of genes involved in acetyl-CoA production after exposure to raffinose. The authors therefore conduct a screen to identify mutants that suppress the induction of one of these acetylCoA genes, Cit2. They then validate the hits from this screen to see which of their suppressor mutants also reduce expression in four other genes induced in a mct1del strain. This yielded 17 genes that abolished induction of all 5 genes tested in an mct1del background during growth on raffinose.

The authors chose to focus on one of these hits, the gene coding for the phosphatase SIT4 (related to human PP6) which also caused an increase in expression of two respiratory chain genes. The authors then investigated MMP and mitochondrial morphology in strains containing SIT4 and MCT1 deletions and surprisingly saw that sit4del cells had highly elevated MMP, more reticular mitochondria, and were able to fully import the acetolactate synthase protein Ilv2p and form ETC and ATP synthase complexes, even in cells with an mct1del background, rescuing the low MMP, fragmented mitochondria, low import of Ilv2 and an inability to form ETC and ATP synthase complexes phenotypes of the mct1del strain. Surprisingly, the authors find that even though MMP is high and ETC subunits are present in the sit4del mct1del double deletion strain, that strain has low oxygen consumption and cannot grow under respiratory conditions, indicating that the elevated MMP cannot come from fully functional ETC subunits. The authors also observe that deleting key subunits of ETC complex III (QCR2) and IV (COX5) strongly reduced the MMP of the sit4del mutant, which would suggest that the majority of the increase in MMP of the sit4del mutant was dependant on a partially functional ETC. The authors note that there was still an increase in MMP in the qcr2del sit4del and cox4del sit4del strains relative to qcr2del and cox4del strains indicating that some part of the increase in MMP was not dependent on the ETC.

The authors dismiss the possibility that the increase in MMP could have been through the reversal of ATP synthase because they observe that inhibition of ATP synthase with oligomycin led to an increase of MMP in sit4del cells. Indicating that ATP synthase is operating in a forward direction in sit4del cells.

Noting that genes for phosphate starvation are induced in sit4del cells, the authors investigate the effects of phosphate starvation on MMP. They found that phosphate starvation caused an increase in MMP and increased Ilv2p import even in the absence of a mitochondrial genome. They find that inhibition of the ADP/ATP carrier (AAC) with bongkrekic acid (BKA) abolishes the increase of MMP in response to phosphate starvation. They speculate that phosphate starvation causes an increase in MMP through the import and conversion of ATP to ADP and subsequent pumping of ADP and inorganic phosphate out of the mitochondria.

They further show that MMP is also increased when the cyclin dependent kinase PHO85 which plays a role in phosphate signaling is deleted and argue that this indicates that it is not a decrease in phosphate which causes the increase in MMP under phosphate starvation, but rather the perception of a decrease in phosphate as signalled through PHO85. Unlike in the case of SIT4 deletion, the increase in MMP caused by the deletion of pho85 is abolished when MCT1 is deleted.

Finally they show an increase in MMP in immortalized human cell lines following phosphate starvation and treatment with the phosphate transporter inhibitor phosphonoformic acid (PFA). They also show an increase in MMP in primary hepatocytes and in midgut cells of flies treated with PFA.

The link between phosphate starvation and elevated MMP is an important and novel finding and the evidence is clear and compelling. Based on their experiments in various mammalian contexts, this link appears likely to be generalizable, and they propose and begin to test an interesting hypothesis for how MMP might occur in response to phosphate starvation in the absence of the Electron Transport Chain.

The link between phosphate starvation and deletion of the conserved phosphatase SIT4 is also interesting and important, and while the authors' experiments and analysis suggest some connection between the two observations, that connection is still unclear.

Major points

Mitotracker is great fluorescent dye, but it measures membrane potential only indirectly. There is a danger when cells change growth rates, ion concentrations, or when the pH changes, all MMP indicating dyes change in fluorescence: their signal is confounded Change in phosphate levels can possibly do both, alter pH and ion concentrations. Because all conclusions of the manuscript are based on a change in MMP, it would be a great precaution to use a dye-independent measure of membrane potential, and confirm at least some key results.

Mitochondrial MMP does strongly influence amino acid metabolism, and indeed the SIT4 knockout has a quite striking amino acid profile, with histidine, lysine, arginine, tyrosine being increased in concentration. http://ralser.charite.de/metabogenecards/Chr_04/YDL047W.html Could this amino acid profile support the conclusions of the authors? At least lysine and arginine are down in petites due to a lack of membrane potential and iron sulfur cluster export.- and here they are up. Along these lines, according to the same data resource, the knock-outs CSR2, ASF1, SSN8, YLR0358 and MRPL25 share the same metabolic profile. Due to limited time I did not re-analyse the data provided by the authors- but it would be worth checking if any of these genes did come up in the screens of the authors.

We tested the mutants within the same cluster as SIT4 shown in this paper from the deletion collection and measured their MMP. yrl358cΔ cells have similar high MMP as observed in sit4Δ cells. However, this gene has a yet undefined function. Beyond YRL358C, we did not observe similar MMP increases in other gene deletions from this panel, which does not support the notion that amino acids such as histidine, lysine, arginine, or tyrosine play a determining effect in driving MMP.

The media condition and strain used in the suggested paper is very different from what we used in our study. Instead of growing prototrophic cells in minimal media without any amino acids, we used auxotrophic yeast strains and grew them in media containing complete amino acids. So far, none of the other defects or signaling associated with SIT4 deletion could influence MMP as much as the phosphate signaling. We interpret these data to support the hypothesis that the MMP observation in sit4Δ cells is connected with the phosphate signaling as illustrated by the second half of the story in our manuscript.

Author reponse image 2.

One important claim in the manuscript attempts to explain a mechanism for the MMP increase in response to phosphate starvation which is independent of the ETC and ATP synthase.

It seems to me the only direct evidence to support this claim is that inhibition of the AAC with BKA stops the increase of mitotracker fluorescence in response to phosphate starvation in both WT and rho0 cells (Figs 4B and 4C). It would strengthen the paper if the authors could provide some orthogonal evidence.

This is a similar comment as raised by reviewer #1 - major concern #3. We refer the reviewer to our discussion and the new data above. Briefly, we do not think F1 subunit is responsible for the ATP hydrolysis activity to generate MMP in phosphate depleted situation. We believe there are additional ATPase(s) in the mitochondrial matrix that can be utilized to couple to ADP/ATP carrier for MMP generation during phosphate starvation. However, we have not identified the relevant ATPase(s) at this point, and it is likely that multiple ATPases could contribute to this activity.

Introduction/Discussion The author might want to make the reader of the article aware that the 'reversal' of the ATP synthase directionality -i.e. ATP hydrolysis by the ATP synthase as a mechanism to create a membrane potential (in petites), has always been a provocative idea - but one that thus far could never be fully substantiated. Indeed some people that are very familiar with the topic, are skeptical this indeed happens. For instance, Vowinckel et al 2021 (PMID: 34799698) measured precise carbon balances for peptide cells, and found no evidence for a futile cycle - peptides grow slower, but accumulate the same biomass from glucose as peptides that re-evolve at a fast growth rate . Perhaps the manuscript could be updated accordingly.

We thank the reviewer for pointing out this additional relevant study. We have rephased the referenced sentence in the introduction. The MMP generation in phosphate starvation is independent of the F1 portion of ATP synthase. Therefore, our data neither supports or refutes either of these arguments.

In the introduction and conclusion there is discussion of MMP set points. In particular the authors state:

"Critically, we find that cells often prioritize this MMP setpoint over other bioenergetic priorities, even in challenging environments, suggesting an important evolutionary benefit."

This does not seem to be consistent with the central finding of the manuscript that MMP changes under phosphate starvation. MMP doesn't seem so much to have a 'set point' but rather be an important physiological variable that reacts to stimuli such as phosphate starvation.

The reviewer raises a rational alternative hypothesis to the one that we have proposed. In reality, both of these are complete speculations to explain the data and we can’t think of any way to test the evolutionary basis for the mechanisms that we describe. We recognize that untested/untestable speculative arguments have limitations and there are viable alternative hypotheses. We have softened our language to ensure that it is clear that this is only a speculation.

The authors suggest that deletion of Pho85 causes an increase in MMP because of cellular signaling. However, they also state in the conclusion:

"Unlike phosphate starvation, the pho85D mutant has elevated intracellular phosphate concentrations. This suggests that the phosphate effect on MMP is likely to be elicited by cellular signaling downstream of phosphate sensing rather than some direct effect of environmental depletion of phosphate on mitochondrial energetics."

The authors should cite the study that shows deletion of PHO85 causes increased intracellular phosphate concentrations. It also seems possible that the 'cellular signaling' that causes the increase in MMP could be a result of this increase in intracellular phosphate concentrations, which could constitute a direct effect of an environmental overload of phosphate on mitochondrial energetics.

We now cited the literature that shows higher intracellular phosphate in pho85Δ cells (Gupta et al., 2019; Liu et al., 2017). Depleting phosphate in the media drastically reduced intracellular phosphate concentration, which is the opposing situation as pho85Δ cells. Nevertheless, we observed higher MMP in either situation. We concluded from these two observations that the increase in MMP is a response to the signaling activated by phosphate depletion rather than the intracellular phosphate abundance.

Related to this point, in the conclusion, the authors state:

"We now show that intracellular signaling can lead to an increased MMP even beyond the wild-type level in the absence of mitochondrial genome."

In sum, the data shows that signaling is important here- but signaling alone is only the message - not the biophysical process that creates a membrane potential. The authors then could revise this slightly.

We have rephrased this sentence as suggested, which now reads “We now show that intracellular signaling triggers a process that can lead to an increased MMP even beyond the wild-type level in the absence of mitochondrial genome”.

The authors state in the conclusion that

"We first made the observation that deletion of the SIT4 gene, which encodes the yeast homologue of the mammalian PP6 protein phosphatase, normalized many of the defects caused by loss of mtFAS, including gene expression programs, ETC complex assembly, mitochondrial morphology, and especially MMP (Fig. 1)"

The data shown though indicates that a defect in mtFAS in terms of MMP, deletion of SIT4 causes a huge increase (and departure away from normality) whether or not mct1 is present (Fig 1D)

We changed the word “normalized” to “reversed”. In the discussion section, we also emphasized that many of these increases are independent of mitochondrial dysfunction induced by loss of mtFAS.

The language "SIT4 is required for both the positive and negative transcriptional regulation elicited by mitochondrial dysfunction" feels strong. SIT4 seems to influence positive transcriptional regulation in response to mitochondrial dysfunction caused by MCT1 deletion (but may not be the only thing as there appears to be an increase in CIT2 expression in a sit4del background following a further deletion of MCT1). In terms of negative regulation, SIT4 deletion clearly affects the baseline, but MCT1 deletion still causes down regulation of both examples shown in Fig 1B, showing that negative transcriptional regulation can still occur in the absence of SIT4. The authors might consider showing fold change of expression as they do in later figures (Figs 4B and C) to help the reader evaluate the quantitative changes they demonstrate.

We now displayed the fold change as suggested. This sentence now reads “These data suggest that SIT4 positively and negatively influences transcriptional regulation elicited by mitochondrial dysfunction”.

The authors induce phosphate starvation by adding increasing amounts of potassium phosphate monobasic at a pH of 4.1 to phosphate dropout media supplemented with potassium. The authors did well to avoid confounding effects of removing potassium. The final pH of YNB is typically around 5.2. Is it possible that the authors are confounding a change in pH with phosphate starvation? One would expect the media in the phosphate starvation condition to have a higher pH than the phosphate replacement or control media. Is a change in pH possibly a confounding factor when interpreting phosphate starvation? Perhaps the authors could quantify the pH of the media they use for the experiment to understand how much of a factor that could be. One needs to be careful with Miotracker and any other fluorescent dye when pH changes. Albeit having constraints on its own, MitoLoc as a protein rather than small molecule marker of MMP might be a good complement.

We followed the protocol used by many other studies that depleted phosphate in the media. The reason we and others adjusted the media without inorganic phosphate to a pH of 4.1 is because that is the pH of phosphate monobasic. From there, we could add phosphate monobasic to create +Pi media without changing the media pH. Therefore, media containing different concentrations of phosphate all have the exact same pH. We now emphasize that all media containing different levels of inorganic phosphate have the same pH to the manuscript to eliminate such concern (see page 18).

Even though all media have the similar pH, we also provided complementary data using a parallel approach to measure the MMP by assessing mitochondrial protein import as demonstrated previously with Ilv2-FLAG, which shares the same principle as mitoLoc.

Reference

Arndt, K. T., Styles, C. A., & Fink, G. R. (1989). A suppressor of a HIS4 transcriptional defect encodes a protein with homology to the catalytic subunit of protein phosphatases. Cell, 56(4), 527–537. https://doi.org/10.1016/00928674(89)90576-X

Dimmer, K. S., Fritz, S., Fuchs, F., Messerschmitt, M., Weinbach, N., Neupert, W., & Westermann, B. (2002). Genetic basis of mitochondrial function and morphology in Saccharomyces cerevisiae. Molecular Biology of the Cell, 13(3), 847–853. https://doi.org/10.1091/mbc.01-12-0588

Gupta, R., Walvekar, A. S., Liang, S., Rashida, Z., Shah, P., & Laxman, S. (2019). A tRNA modification balances carbon and nitrogen metabolism by regulating phosphate homeostasis. ELife, 8, e44795. https://doi.org/10.7554/eLife.44795

Jablonka, W., Guzmán, S., Ramírez, J., & Montero-Lomelí, M. (2006). Deviation of carbohydrate metabolism by the SIT4 phosphatase in Saccharomyces cerevisiae. Biochimica et Biophysica Acta (BBA) - General Subjects, 1760(8), 1281–1291. https://doi.org/10.1016/j.bbagen.2006.02.014

Liu, N.-N., Flanagan, P. R., Zeng, J., Jani, N. M., Cardenas, M. E., Moran, G. P., & Köhler, J. R. (2017). Phosphate is the third nutrient monitored by TOR in Candida albicans and provides a target for fungal-specific indirect TOR inhibition. Proceedings of the National Academy of Sciences, 114(24), 6346–6351. https://doi.org/10.1073/pnas.1617799114

Sutton, A., Immanuel, D., & Arndt, K. T. (1991). The SIT4 protein phosphatase functions in late G1 for progression into S phase. Molecular and Cellular Biology, 11(4), 2133–2148.

Author Response

Reviewer #2 (Public Review):

Weaknesses:

1)The authors demonstrate that Isw1 has a role in responding to antifungals in Cryptococcus. However, it is not clear if changes in Isw1 stability represent a general response to stress. This study would have benefited from experiments to test: (1) if levels of Isw1 change in response to other stressors (e.g., heat, osmotic, or oxidative stress) and (2) if loss of Isw1 impacts resistance to other stressors.

A series of experiments were conducted to illustrate and measure phenotypic traits associated with virulence. These traits encompassed capsule formation, melanin synthesis, cell proliferation under stressful conditions, and Isw1 expression levels in response to diverse environmental stimuli. Please see Figure 3a, 3b, 3c, Figure 3-figure supplement 1 and line 237-241.

2) The authors demonstrate a critical role in the acetylation of K97 and ubiquitination of K441 in regulating Isw1 stability. Additionally, this study shows that K113 is also likely involved in this process. However, it appears that K113 can be either acetylated or ubiquitinated, and it is, thus, less clear if one of the two modifications or both modifications is critical at this residue. Additional experiments may be required to answer this question. This study would have benefited from an additional discussion on the results related to the modification of K113.

We express our genuine gratitude for this insightful critique pertaining to the K113 site. In our study, we observed the presence of acetylation and ubiquitination changes at the K113 site in our mass spectrometry data. This finding suggests that a proportion of Isw1 is acetylated, while another proportion of Isw1 is ubiquitinated. In order to analyze the K113 function, a series of experiments were conducted, involving the production of triple, double, and single mutations at positions K89, K97, and K113. In addition, the utilization of K-to-R (mimicking deacetylation) and K-to-Q (mimicking acetylation) methodologies was implemented. To elucidate the significance of the acetylation modification of K113, a series of mutants were created. The K-to-R mutation was employed to indicate the deacetylation and deubiquitylation status, while the K-to-Q mutation was utilized to represent the acetylation and deubiquitylation status. In our dataset, it was shown that neither the single mutation of K113 K-to-R nor K-to-Q exhibited any discernible drug resistance phenotype. This finding suggests that, within the physiological context of the Isw1 protein, both post-translational modifications (PTMs) of K113 had minimal or no impact on the regulation of drug resistance. The reason for this phenomenon is because the acetylation modification of K97 imitates the process of ubiquitination of Isw1, hence reducing the interaction between Isw1 and Cdc4, which is an E3 ligase. Hence, the ubiquitination of K113 does not play a crucial role in the regulation of Isw1 protein stability under conditions where K97 is completely acetylated. Nevertheless, upon deacetylation of K97, we observed a notable increase in the abundance of Isw1 protein when K113 is substituted with R. This finding strongly supports the notion that ubiquitination of K113 plays a crucial role in maintaining the stability of the Isw1 protein. Hence, in the case of K97 acetylation, the PTM modifications of K113 are not required for maintaining Isw1 protein levels. However, in the event of K97 deacetylation, the ubiquitination of K113 becomes crucial in regulating protein stability. Considering the intricate post-translational modification (PTM) regulation observed at the K113 site, it would be advantageous to generate antibodies specific to K113ac and K113ub in order to comprehensively investigate the functional role of K113 in the regulatory processes. Nevertheless, the presence of antibodies targeting site-specific ubiquitination is infrequent in scientific literature. We regret any confusion that may have arisen from the previous remark and have made revisions to the manuscript to address this issue. Please refer to line 485-500.

3)The authors demonstrate that overexpression of ISW1 in select clinical isolates of Cryptococcus increases sensitivity to antifungals. However, these experiments would have benefited from additional controls, such as including overexpression of ISW1 in the wild-type strain (H99) and antifungal-sensitive isolate (CDLC120).

In response to your concern, we successfully generated the strains as required. In the revised manuscript, we demonstrated that the overexpression of the stable variant of Isw1 in H99 and CDLC120 strains induces heightened susceptibility to antifungal drugs. Please see Figure 8e, 8i and line 404-413.

Reviewer #3 (Public Review):

1) ISWI chromatin remodellers are well-characterised in many organisms. How many ISWI proteins does Cryptococcus contain? Why did the authors focus on ISWI?

We express our gratitude for this criticism. The identification of Isw1 was conducted as a further investigation building upon the findings presented in our previously published data (Li Y, 2019). In prior research, the acetylome in C. neoformans was comprehensively analyzed, and a series of knockout strains were created to investigate the relationship between fungal pathogenicity and acetylation. The Isw1 mutant has been discovered as a modifier of drug resistance. The identification of fungal paralogs of ISW genes was initially observed in Saccharomyces cerevisiae, a species of yeast that has experienced genome duplication. This process involves two paralogs, Isw1 and Isw2, which emerged as a result of the whole genome duplication event (Kellis M, 2004; Tsukiyama T, 1999; Wolfe KH, 1997). Because C. neoformans has not gone through the complete genome duplication event, its genome only encodes one copy of ISW gene. Please see line 129-134..

2) What is the ISWI protein complex(es)? The Mass-Spec analysis should reveal this.

Prior research conducted on Saccharomyces cerevisiae has provided evidence that the ISWI complex is comprised of several subunits, namely Isw1, Ioc genes, Itc1, Chd1, and Sua7 (Mellor J, 2004; Smolle M, 2012; Sugiyama and Nikawa, 2001; Vary JC Jr, 2003; Yadon AN, 2013). Upon a thorough examination of the C. neoformans genome, we have not been able to identifying a similar the IOC gene family. This absence likely suggests an evolutionary loss of the IOC gene family in C. neoformans, as suggested on the FungiDB website. However, C. neoformans has Itc1, Chd1, and Sua7. While we concur with the aforementioned statement on the capability of Mass-Spec data to elucidate potential protein-protein interactions and aid in the identification of subunits within the ISWI complex, it is important to acknowledge that the PTM Mass-Spec methodology is solely employed for the purpose of identifying potential sites of protein modification. In order to comprehensively investigate the cryptoccocal ISWI complex, we conducted a standardized Isw1-Flag protein immunoprecipitation procedure, followed by Mass-Spec analysis. In the present study, a total of 22 proteins that interact with Isw1 were found in our experimental data. Among these proteins, 11 have been previously reported to be associated with the regulatory networks including Isw1. In the mass spectrometry results, the protein Itc1 was found to be co-immunoprecipitated with the protein Isw1. Although the Mass-Spec analysis did not reveal the presence of Chd1 and Sua7, our study demonstrated that Chd1 can be coimmunoprecipitated with Isw1 through the utilization of co-IP and immunoblotting techniques. However, no interaction between Isw1 and Sua7 was shown utilizing any of these methods. In brief, cryptococcal ISWI regulatory machinery is distantly related to that from S. cerevisiae. Please see Figure 2 and line 206-219.

3) Is Cryptococcus ISWI a transcriptional activator or repressor?

We regret the erroneous representation of Isw1 in the prior iteration of the manuscript. The misclassification of Isw1 as a transcriptional regulator has been identified, since it has been determined to function as a chromatin remodeler instead. The text has been suitably revised in accordance with academic standards. In the revised publication, we have presented a comprehensive transcriptome analysis of the isw1 Δ strain under both FLC treatment and no treatment conditions. This analysis offers valuable insights into the gene regulatory patterns associated with Isw1. In our dataset, we observed that Isw1 exerts a negative regulatory effect on the expression of genes that encode drug pumps, while simultaneously exerting a positive regulatory effect on the expression of genes that are essential for 5-FC resistance. Moreover, the ChIP-PCR study demonstrated the binding of Isw1 to the promoter regions of genes of interest. Hence, the chromatin remodeler Isw1 has a dual role, wherein it both facilitates the activation of certain genes and suppresses the expression of others, in response to varying forms of drug resistance. Please see line 142-153.

4) Is ISWI function in drug resistance linked to its chromatin remodelling activity?

In order to investigate the potential role of Isw1 on chromatin activity in the modulation of multidrug resistance, we have conducted protein truncation experiments. Specifically, we deleted the DNA binding domain, the helicase domain, and the SNF2 domain, which have been previously shown to regulate Isw1 chromatin activity in the model organism S. cerevisiae (Grune T, 2003; Mellor J, 2004; Pinskaya M, 2009; Rowbotham SP, 2011). The new data demonstrated that all truncation variants of Isw1 mutants had a growth phenotype consistent with that of the deletional strain isw1Δ. In addition, the levels of gene expression observed in these strains were also similar to those observed in the deletion strain isw1Δ. This finding provides evidence that the regulation of the drug resistance mechanism is influenced by these critical domains involved in modifying chromatin activities. Moreover, the Isw1-Flag strain was utilized to conduct chromatin immunoprecipitation and PCR experiments, which revealed that Isw1 exhibits the ability to directly bind to the promoter regions of target genes. The new findings added evidence substantially supporting the hypothesis that the Isw1 chromatin activity plays a crucial role in modulating its protein function, and acting as a central regulator of drug resistance in C. neoformans. Please see revised Figure 1g, 1h, 1i and line 186-199 in the revised manuscript text.

5) Does ISWI interact with chromatin? If so, which are ISWI-target genes? Does drug treatment modulate chromatin binding?

To effectively tackle this concern, we have pursued two distinct approaches to demonstrate the chromatin regulatory effects of Isw1. In this study, the DNA binding domain was deliberately removed through genetic manipulation. The data presented indicates that the Isw1 mutants with shorter variations exhibited a growth phenotype that was characterized by multidrug resistance. This growth phenotype correlates with the growth phenotype obtained in the isw1Δ deletion strain. Additionally, it was observed that the levels of gene expression in the strain were comparable to those detected in the deletion strain isw1Δ. This discovery offers empirical support for the notion that the control of the drug resistance mechanism is indeed impacted by the DNA binding capability of Isw1. Furthermore, the Isw1-Flag strain was employed to perform chromatin immunoprecipitation and PCR assays, demonstrating the direct binding capacity of Isw1 to the promoter regions of target genes. The results obtained from this comprehensive analysis of the revised data offer significant evidence for the proposition that Isw1 interacts with chromatin and that its chromatin activity plays a pivotal role in modulating its protein function. This interaction serves as a central regulatory mechanism for drug resistance in C. neoformans. Furthermore, a transcriptome analysis was performed on both wildtype and isw1 deletion strains in the absence of FLC therapy. Upon comparing the results obtained from two unique experimental settings, specifically those with and without FLC administration, a notable disparity in the control of gene expression between these two situations was identified. In the context of the isw1 deletion strain exposed to FLC treatment, a set of 21 genes, including those belonging to the ABC/MFS family and efflux pumps, displayed significant changes in their gene expression patterns. In particular, a total of 9 genes exhibited downregulation, whilst 12 genes displayed upregulation. In contrast, in the absence of FLC supplementation, a total of 9 genes exhibited alterations in gene expression, with 3 genes showing downregulation and 6 genes showing upregulation. Therefore, the Isw1 protein plays a crucial role in the activation of certain genes, while simultaneously having a suppressive effect on other genes. Hence, the Isw1 undergoes a reconfiguration of its regulatory apparatus in response to drugs. Despite that the performance of ChIP-seq analysis was necessary in this study, it was observed that the treatment of fungal cells resulted in a notable decrease in the abundance of the Isw1 protein. This decrease can be attributed to the activation of Isw1 protein degradation. Consequently, there was an insufficient amount of Isw1 protein available for successful enrichment and subsequent ChIP-seq analysis (please see Figure 4a and 4c). However, the data collected collectively have demonstrated the idea that Isw1 serves as a crucial master regulator of drug resistance in C. neoformans. The text has undergone revisions in order to present our findings in a precise and thorough manner. Please see Figure 1c, 1g, Supplementary File 2, and line 145-153, 186-188.

Author Response

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

eLife assessment:

Multimodal experiences that for example contain both visual and tactile components are encoded as associative memories. This manuscript is a valuable contribution supporting structural and functional brain plasticity following associative training protocols that pair together different types of sensory stimuli. The results provide solid support for this plasticity being a basis for cross-modal associative memories.

We appreciate eLife assessments to our discovery about the recruitment of associative memory neurons in cerebral cortices as a hub for the fulfillment of the first order and the second order of associative memory. Synapse interconnections among associative memory neurons mediate the reciprocal retrieval, the conversion and the translation of associated signals learnt in life span.

Reviewer #1 (Public Review):

This manuscript by Xu and colleagues addresses the important question of how multi-modal associations are encoded in the rodent brain. They use behavioral protocols to link stimuli to whisker movement and discover that the barrel cortex can be a hub for associations. Based on anatomical correlations, they suggest that structural plasticity between different areas can be linked to training. Moreover, they provide electrophysiological correlates that link to behavior and structure. Knock-down of nlg3 abolishes plasticity and learning. This study provides an important contribution as to how multi-modal associations can be formed across cortical regions.

We sincerely thank Reviewer one’s comments, which is a great driving force for us to move forward to reveal the specific roles of neural circuits in associative memory and its relevant cognitive activities and emotional reactions.

Reviewer #2 (Public Review):

This manuscript by Xu et al. explores the potential joint storage/retrieval of associated signals in learning/memory and how that is encoded by some associative memory neurons using a mouse model. The authors examined mouse associative learning by pairing multimodal mouse learning including olfactory, tactile, gustatory, and pain/tail heating signals. The key finding is that after associative learning, barrel neurons respond to other multi-model stimulations. They found these barrel cortical neurons interconnect with other structures including piriform cortex, S1-Tr and gustatory cortical neurons. Further studies showed that Neuroligin 3 mediated the recruitment of associative memory neurons during paired stimulation group. The authors found that knockdown Neuroligin 3 in the barrel cortex suppressed the associative memory cell recruitment in the paired stimulation learning. Overall, while the findings of this study are interesting, the concept of associative learning involving multiple functionally connective cortical regions is not that novel. While some data presented are convincing, the other seems to lack rigor. In addition, more details and clarification of the experimental methods are needed.

Thank you so much for your comments on our studies in terms of the recruitment of associative memory neurons as the hub for the joint storage and reciprocal retrieval of multi-modal associated signals. You are right about that the concept of associative memory neuron and the new established interconnection among cerebral cortices for the formation of associative memory are not novel. The original finding has been reported by senior author’s lab many years ago, which has also been presented in a book by Jin-Hui Wang “Associative Memory Cells: Basic Units of Memory Trace” published by Springer-Nature 2019. In addition, we have made certain clarifications in our revision, but the detailed information about experimental approaches and concepts are expected to be seen in our previous publications and this book as well.

Reviewer #1 (Recommendations For The Authors):

I have two points that I find would strengthen the manuscript further:

1. Associative memories are also based on specificity, which is not addressed in this manuscript. The authors could discuss this and also the magnitude of plasticity. In general, I would suggest also testing plasticity in response to a non-linked stimulus to prove specificity.

This a good point. In terms of the specificity of associative memory in our model, we have shown this point in our previous studies, such as Wang, et al. “Neurons in the barrel cortex turn into processing whisker and odor signals: a cellular mechanism for the storage and retrieval of associative signals”. Frontiers in Cellular Neuroscience 9-320:1-17 2015, and Jin-Hui Wang “Associative Memory Cells: Basic Units of Memory Trace” published by Springer-Nature 2019.

1. Nlg3 knock-down is a strong intervention. The authors could discuss the implications of interfering with synapse assembly and mechanistic implications at the synaptic level. It could help to compare the consequences of this intervention to a post-training lesion.

This is a good point. To prevent the possibility of post-training lesion by the intervention of Nlg3 knockdown, we have conducted the use of shRNA-scramble control. In addition, the discussion about the intervention of Nlg3 knockdown at synapse level has been added in our discussion.

1. In general, the clarity of the wording in some sections/sentences could be improved.

The rewording of certain sentences has been done in our revision.

Reviewer #2 (Recommendations For The Authors):

1. The writing of the manuscript needs major editing, there are grammatical errors even in the title. The extremely long introduction and discussion section with repeated details can be distracting from the main focus of the work.

This point has been taken during our revision.

1. Many bar graphs, such as Figure 5C and 5G, Figure 6C-6G, have low-resolution images, meaning that the axis titles and labels are unreadable.

The resolution of Figures have been improved in our revision.

1. The bar graph with data points and illustration in Figure 1E and 1G are misplaced.

This mistake has been corrected in our revision.

1. On page 23, Figure 2B, which layer(s) of the PC, S1Tr and GC were the images taken from? In the PSG group, why is there no red axon terminal signal observed in the three regions? does it indicate that there is no significant projection from the BC axon to PC, S1Tr, or GC neurons? Given that Thy1-YFP labeled glutamatergic neurons at PC, S1Tr, and GC and there is no discernable co-localization of yellow and green cells, can we assume that the glutamatergic neurons at PC, S1Tr, and GC are not involved in the associative learning after PSG paradigm? Lastly, the number of synapse contacts in Figure 2E is only 1-2 per 100um dendrite, but this is not quite consistent with the confocal images in Figure 2D. In Figure 2D, there are at least three tdTomato boutons on the cropped dendrite which is ~16um according to the scale bar.

If we magnify Figure 2B, we are able to see red boutons, which can be seen in Figure 2C with a higher magnification. In addition, the distribution of synapse contacts is variable, we have demonstrated the averaged values of synapse contacts over dendrites in Figure 2E, such that the single original image may not exactly same as the statistical data.

1. Figure 4C and Figure 8C, how were the percentages of associative neurons calculated after LFP recording? More details are needed on the method of this in vivo LFP/single unit recordings, including the spike sorting algorithm.

In the section of Results, the total number of neurons recorded in each of groups has been given. For instance, the neurons recorded from PSG mice (Figure 4) were 70, which was used as denominator. With the number of neurons that responded to two or more signals, the percentage of associative memory neurons recruited in associative learning was calculated. This information has been added in our revision (please see the section of Results).

1. The rationale for the authors choosing Neuroligin 3 as the target for investigating the formation of new synapse interconnections between BC, PC, S1Tr, and GC after PSG should be more clearly spelled out. Synaptic CAMs include SynCAM, NCAM, Neurexin, Cadherin et al all play a role in new synapse formation. Neuroligin 1 is expressed specifically in the CNS at excitatory synapses. Why did the authors choose to study Neuroligin 3 instead of Neuroligin 1?

This is a good point. Based on our previous data, miRNA-324 is upregulated during the associative learning by our mouse model, which degrades neuroligin-3 mRNA. The role of neuroligin-3 in the formation of new synapses and the recruitment of associative memory neurons is studied in this paper.

1. The behavioral results in Figure 5B-5G indicated that after pair-stimulation of WS-OS, WS-TS, or WS-GS, the memory learned in piriform, S1-Tr and gustatory cortical neurons can be retrieved from each other, by jumping over the barrel cortex. Is it possible that there is some direct interconnection formed between piriform, S1-Tr, and gustatory cortical neurons? Maybe they can try to do barrel cortical lesion or chemogenetic inhibition after PGS training and then repeat the behavioral tests as in Figure 5B-5G.

We have done experiments to examine the potential direct interconnection among piriform, S1-Tr and gustatory cortical neurons, after the associative learning about twelve days. We have no convincing data to support this possibility at this moment.

1. Some of the images showing the location of virus injections look VERY similar, such as Figure 3A left and right, Figures 7A and 7D. Larger variability of different animals/injection sites is definitely expected.

The injected viruses in Figure 3 and Figure 7 are different, since AAV-carried fluorescent proteins in different cortical areas are different. In addition, if we carefully enlarge the images in the right and left panels of Figure 3A, we will see that the areas of AAV transfection in morphology are different. The similarity of injection areas as Reviewer two claimed indicates the more precision of our virus-injection sites.

1. On page 49, are the green neurons in Figure 9B the BC cells? Just to be consistent, the authors should use the same color for BC cells as in Figure 9A. Also, label the primary and the secondary associative memory cells in Figure 9.

Figure 9 has been thoroughly changed in our revision.

Author Response

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

Reviewer #1 (Public Review):

Soudi, Jahani et al. provide a valuable comparative study of local adaptation in four species of sunflowers and investigate the repeatability of observed genomic signals of adaptation and their link to haploblocks, known to be numerous and important in this system. The study builds on previous work in sunflowers that have investigated haploblocks in those species and on methodologies developed to look at repeated signals of local adaptations. The authors provide solid evidence of both genotype-environment associations (GEA) and genome-wide association study (GWAS), as well as phenotypic correlations with the environment, to show that part of the local adaptation signal is repeatable and significantly co-occur in regions harboring haploblocks. Results also show that part of the signal is species specific and points to high genetic redundancy. The authors rightfully point out the complexities of the adaptation process and that the truth must lie somewhere between two extreme models of evolutionary genetics, i.e. a population genetics view of large effect loci and a quantitative genetics model. The authors take great care in acknowledging and investigating the multiple biases inherent to the used methods (GEA and GWAS) and use a conservative approach to draw their conclusions. The multiplicity of analyses and their interdependence make them slightly hard to understand and the manuscript would benefit from more careful explanations of concepts and logical links throughout. This work will be of interest to evolutionary biologists and population geneticists in particular, and constitutes an additional applied example to the comparative local adaptation literature.

Some thoughts on the last paragraph of the discussion (L481-497): I think it would be fine to have some more thoughts here on the processes that could contribute to the presence/absence of inversions, maybe in an "Ideas and Speculation" subsection. To me, your results point to the fact that though inversions are often presented as important for local adaptation, they seem to be highly contingent on the context of adaptation in each species. First, repeatability results are only at the window/gene level in your results, the specific mutations are not under scrutiny. Is it possible that inversions are only necessary when sets of small effect mutations are used, opposite to a large effect mutation in other species? Additionally, in a model with epistasis, fitness effects of mutations are dependent on the genomic background and it is possible that inversions were necessary in only certain contexts, even for the same mutations, i.e. some adaptive path contingency. Finally, do you have specific demographic history knowledge in this system that maps to the observations of the presence of inversions or not? For example, have the species "using" inversions been subject to more gene flow compared to others?

Thank you for the great suggestions and helpful comments. Regarding the question of demography, each of the species actually harbours quite a large number of haploblocks (13 in H. annuus spanning 326Mb, 6 in H. argophyllus spanning 114 Mb, and 18 in H. petiolaris spanning 467 Mb; see Todesco et al. 2020 for more details) so there does not seem to be any clear association with demography. We agree about the complexities that might underly the evolution of inversions that you outline above, and have refined some of the text where we discuss their evolution in the Discussion.

Reviewer #2 (Public Review):

In this study the authors sought to understand the extent of similarity among species in intraspecific adaptation to environmental heterogeneity at the phenotypic and genetic levels. A particular focus was to evaluate if regions that were associated with adaptation within putative inversions in one species were also candidates for adaptation in another species that lacked those inversions. This study is timely for the field of evolutionary genomics, due to recent interest surrounding how inversions arise and become established in adaptation.

Major strengths

Their study system was well suited to addressing the aims, given that the different species of sunflower all had GWAS data on the same phenotypes from common garden experiments as well as landscape genomic data, and orthologous SNPs could be identified. Organizing a dataset of this magnitude is no small feat. The authors integrate many state-of-the-art statistical methods that they have developed in previous research into a framework for correlating genomic Windows of Repeated Association (WRA, also amalgamated into Clusters of Repeated Association based on LD among windows) with Similarity In Phenotype-Environment Correlation (SIPEC). The WRA/CRA methods are very useful and the authors do an excellent job at outlining the rationale for these methods.

Thank you!

Major weaknesses

The study results rely heavily on the SIPEC measure, but I found the values reported difficult to interpret biologically. For example, in Figure 4 there is a range of SIPEC from 0 to 0.03 for most species pairs, with some pairs only as high as ~0.01. This does not appear to be a high degree of similarity in phenotype-environment correlation. For example, given the equation on line 517 for a single phenotype, if one species has a phenotype-environment correlation of 1.0 and the other has a correlation of 0.02, I would postulate that these two species do not have similar evolutionary responses, but the equation would give a value of (1+0.02)10.02/1 = 0.02 which is pretty typical "higher" value in Figure 4. I also question the logic behind using absolute values of the correlations for the SIPEC, because if a trait increases with an environment in one species but decreases with the environment in another species, I would not predict that the genetic basis of adaptation would be similar (as a side note, I would not question the logic behind using absolute correlations for associations with alleles, due to the arbitrary nature of signing alleles). I might be missing something here, so I look forward to reading the author's responses on these thoughts.

The reviewer makes a very good point about the range of SIPEC, and we have changed our analysis to reflect this, now reporting the maximum value of SIPEC for each environment (across the axes of the PCA on phenotypes that cumulatively explain 95% of the variance), in Figure 4 and Supplementary Figures S2 and S13. For consistency among manuscript versions and to illustrate the effect of this change, we retain the mean SIPEC value in one figure in the supplementary materials (S12), which shows the small effect of this change on the qualitative patterns. Figure 4 now shows that the maximum SIPEC value is regularly quite strong, which should address the reviewer’s concern that this is not being driven by anomalous and small values. We appreciate this point and think this change now more closely reflects how we are trying to estimate the biological feature of interest – that some axis of phenotypic space is strongly (or not) responding to selection from the environmental variable.

With respect to the logic behind using absolute value, we still feel this is justified for traits, because if a trait evolves to be bigger or smaller, it may still use the same genes. For example, flowering time may change to be later or earlier, which would result in opposite correlations with a given environment, but might use the same gene (e.g. FT) for this. As such, we think keeping absolute value is more representative as otherwise species with strong but opposite patterns of adaptation would look like they were very different. We have added a statement on line 584 in the methods section to further clarify the reason for this choice.

An additional potential problem with the analysis is that from the way the analysis is presented, it appears that the 33 environmental variables were essentially treated as independent data points (e.g. in Figure 4, Figure 5). It's not appropriate to treat the environmental variables independently because many of them are highly correlated. For example in Figure 4, many of the high similarity/CRA values tend to be categorized as temperature variables, which are likely to be highly correlated with each other. This seems like a type of pseudo replication and is a major weakness of the framework.

This is a good point and we fully agree. It is for this reason that we didn’t present any p-values or statistical tests of the overall patterns that are shown in these figures (i.e. the linear relationship between SIPEC and number of CRAs in figure 4 and the tendency for most points to fall above the 1:1 line in figure 5). But to make sure this is even more clear, we have added statements to the captions of these figures to remind readers that points are non-independent. We still feel that in the absence of a formal test, the overall patterns are strongly consistent with this interpretation. A smaller number of non-pseudo-replicated points in Figure 4 would still likely show linear patterns. Similarly, there are almost no significant points falling below the 1:1 line in Figure 5, and it seems unlikely that pseudoreplication would generate this pattern.

Below I highlight the main claims from the study and evaluate how well the results support the conclusions.

"We find evidence of significant genome-wide repeatability in signatures of association to phenotypes and environments" (abstract)<br /> Given the questions above about SIPEC, I did not find this conclusion well supported with the way the data are presented in the manuscript.

We have changed the reporting of the SIPEC metric so that it more clearly reflects whichever axis of phenotypic space is most strongly correlated with environment in both species (using max instead of mean). This shows similar qualitative patterns but illustrates that this happens across much higher values of SIPEC, showing that it is in fact driven by high correlations in each species (or non-similar correlations resulting in low values of SIPEC). While we agree about the pseudo-replication problem preventing formal statistical test of this hypothesis, the visual pattern is striking and seems unlikely to be an artefact, so we think this does still support this conclusion.

"We find evidence of significant genome-wide repeatability in signatures of association to phenotypes and environments, which are particularly enriched within regions of the genome harbouring an inversion in one species. " (Abstract) And "increased repeatability found in regions of the genome that harbour inversions" (Discussion)<br /> These claims are supported by the data shown in Figure 4, which shows that haploblocks are enriched for WRAs. I want to clarify a point about the wording here, as my understanding of the analysis is that the authors test if haploblocks are enriched with WRAs, not whether WRAs are enriched for haploblocks. The wording of the abstract is claiming the latter, but I think what they tested was the former. Let me know if I'm missing something here.

We are actually not interested in whether WRAs are enriched for haploblocks; we want to know if WRAs tend to occur more commonly within haploblocks than outside of them. We have tried to clarify that this is our aim in various places in the manuscript. Our analysis for Figure 5 is the one supporting these claims, and it uses the Chi-square test statistic to assess the number of WRAs and non-WRAs that fall within vs. outside of inversions, and a permutation test to assess the significance of this observation, for each environmental variable and phenotype. We don’t think that this test has any direction to it – it’s simply testing if there is non-random association between the levels of the two factors. Thus, we think the wording we have used is consistent with the test result and our aims. Perhaps the confusion arose from the two methods that we present in the Methods (one is used for Figure 5, the other for Figure S6C & D), so we have added clarifications there.

Notwithstanding the concerns about highly correlated environments potentially inflating some of the patterns in the manuscript, to my knowledge this is the first attempt in the literature to try this kind of comparison, and the results does generally suggest that inversions are more likely capturing, rather than accumulating adaptive variation. However, I don't think the authors can claim that repeated signatures are enriched with haploblock regions, and the authors should take care to refrain from stating the relative importance of different regions of the genome to adaptation without an analysis.

Actually, we don’t have a strong feeling about whether inversions are capturing vs. accumulating adaptive variation, as these results could be consistent with either. As described above, we do not understand why we can’t claim that repeated signatures are enriched within haploblocks. We thought the reviewer is perhaps referring to the fact that the points are pseudo-replicated in the figures due to environment? We note that a very large number of points are significantly different from random in terms of the distribution of WRAs within vs. outside of haploblocks (light- vs. dark-shaded symbols), and that almost all of them fall above the 1:1 line. While there may be pseudo-replication preventing a test of the bigger multi-environment/multi-species hypothesis across all phenotypes and environments, there is almost a complete lack of significant results in the other direction. This seems like quite strong evidence about enrichment of WRAs within haploblocks, across many environments/species contrasts. We have added some text to the description of patterns in figure 5 to try to clarify this.

"While a large number of genomic regions show evidence of repeated adaptation, most of the strongest signatures of association still tend to be species-specific, indicating substantial genotypic redundancy for local adaptation in these species." (Abstract)<br /> Figure 3B certainly makes it look like there is very little similarity among species in the genetic basis of adaptation, which leaves the question as to how important the repeated signatures really are for adaptation if there are very few of them. (Is 3B for the whole genome or only that region?). This result seems to be at odds with the large number of CRAs and the claims about the importance of haploblock regions to adaptation, which extend from my previous point.

Figure 3B is for the whole genome, we have added text to the figure caption to clarify this. We think that both interpretations are possible: that most of the regions of the genome that are driving adaptation are non-repeated, but that a small but significant proportion of regions driving adaptation are repeated above what would be expected at random. Thus, it seems that there is high redundancy, coupled with adaptation via some genes that seem particularly functionally important and non-redundant, and therefore repeated. We added clarifying text on lines 541-548.

"we have shown evidence of significant repeatability in the basis of local adaptation (Figure 4, 5), but also an abundance of species-specific, non-repeated signatures (Figure 3)"<br /> While the claim is a solid one, I am left wondering how much of these genomes show repeated vs. non-repeated signatures, how much of these genomes have haploblocks, and how much overlap there really is. Finding a way to intuitively represent these unknowns would greatly strengthen the manuscript.

We agree, and really struggled to find the best way to communicate both the repeated patterns and the large amount of non-repeated signatures. Unfortunately, we have more confidence in the validity of repeated patterns because for the non-repeated patterns, a strong signature of association to environment in only one species could just be the product of structureenvironment correlation, as we didn’t control for population structure. Thus, trying to quantify the proportion of non-repeated signatures is difficult to do with any accuracy and we preferred to avoid putting too much emphasis on the simple calculation of the proportion of top candidate windows that were also WRAs.

Overall, I think the main claims from the study, the statistical framework, and the results could be revised to better support each other.

Although the current version of the manuscript has some potential shortcomings with regards to the statistical approaches, and the impact of this paper in its present form could be stifled because the biology tended to get lost in the statistics, these shortcomings may be addressed by the authors.

With some revisions, the framework and data could have a high impact and be of high utility to the community.

Thank you for your very helpful comments and suggestions on our paper, we really appreciate it.

Recommendations for the authors: please note that you control which revisions to undertake from the public reviews and recommendations for the authors

Editor's comments:

The reviewers make a series of reasonable suggestions that I echo. I found the paper quite hard to follow, and got fairly lost in the various layers of analyses done. Partially, this represents the complexity of empirical genomic data, which rarely deliver simple stories of convergence at a few genes. However, the properties of the various statistics used to detail local adaptation and convergence are not particularly clear and the figures presented were not intuitive representations of the data. This leaves the reader with an incomplete view of how much weight to put in the various lines of evidence marshaled. I would suggest simplifying the presentation of the results considerably. I add a few additional comments below.

Great suggestion, we’ve added a schematic overview of the methods and main research questions to Figure S1 in the supplementary materials.

A figure would help showing some of the signals of SNPs with putative signals of convergent environmental correlations across species, e.g. frequencies plotted against climate variables. This would help readers get a sense of how strong these signals were. These could be accompanied by the statistics calculated for these SNPs, that would allow the reader to start to get some intuitive sense of what the numbers mean.

Great suggestion, we have added a schematic overview of the methods to Figure S1 that shows some of the values and illustrates how the methods work using visual examples from our data.

In general, the introduction and some of the discussion of the inversion results feel oddly framed:<br /> Abstract line 36: "This shows that while inversions may facilitate local adaptation, at least some of the loci involved can still make substantial contributions without the benefit of recombination suppression."

We have changed “some of the loci involved can still make substantial contributions without the benefit of recombination suppression” here to “some of the loci involved can still harbour mutations that make substantial contributions without the benefit of recombination suppression in species lacking a segregating inversion” as it hopefully clarifies that we’re not talking about individual alleles that are present in both species.

Models of the role of local adaptation in the establishment of inversions (Kirkpatrick & Barton) assume that there are multiple locally adapted alleles already present. It is the load created by these alleles being constantly maintained in the face of migration and subsequent recombination that allow an inversion to be selected for because it keeps together locally adapted alleles. Thus these models predict that there could well be standing local adaptation at these loci in the absence of the inversion in other species, and that these locally adapted alleles while not fixed may be at high frequency. (After establishment, inversions housing locally adapted alleles, can shield more weakly, locally beneficial alleles from migration allow other alleles to build up.) Empirically it's interesting to find signals of local adaptation in other species that don't contain putative inversions. But the logic of the different predictions is not particularly clear from the introduction, and only becomes somewhat clearer in the discussion.

Thank you for pointing out this murkiness, we have re-written portions of both the Introduction and Discussion to clarify this aspect.

From the introduction: Inversions have been implicated in local adaptation in many species (Wellenreuther and Bernatchez 2018), likely due to their effect to suppress recombination among inverted and noninverted haplotypes, and thereby maintain LD among beneficial combinations of locally adapted alleles (Rieseberg 2001; Noor et al. 2001; Kirkpatrick and Barton 2006). This has been approached by models studying the establishment of inversions that capture combinations of locally adapted alleles present as standing variation (e.g., Kirkpatrick and Barton 2006), as well as models examining the accumulation of locally adapted mutations within inversions (e.g., Schaal et al. 2022). If there is variation in the density of loci that can potentially contribute to local adaptation, inversions would be expected to preferentially establish and be retained in regions harbouring a high density of such loci (and this expectation would hold for both the capture and accumulation models). We would also expect to see stronger signatures of repeated local adaptation in such high density regions. Despite mounting evidence of their importance in adaptation, it is unclear how inversions may covary with repeatability of adaptation among species. A fundamental parameter of importance in these models is the relationship between migration rate and strength of selection on individual alleles, which may not make persistent contributions to local adaptation without the suppressing effects of recombination if selection is too weak (Yeaman and Whitlock 2011; Bürger and Akerman 2011). If most alleles have small effects relative to migration rate and can only contribute to local adaptation via the benefit of the recombination-suppressing effect of an inversion, then we would expect little repeatability at the site of an inversion – other species lacking the inversion would not tend to use that same region for adaptation because selection would be too weak for alleles to persist. On the other hand, if some loci are particularly important for local adaptation and regularly yield mutations of large effect, with these patterns being conserved among species, repeatability within regions harbouring inversions may be substantial. Thus, studying whether adaptation at the same genomic region harbouring an inversion is observed in other species lacking the inversion can give insights about the underlying architecture of adaptation, and the evolution and maintenance of inversions.

From the Discussion: The observed repeatability associated with inversions further supports the local adaptation model as an explanation for the long-term persistence of segregating inversions (at least in sunflowers, rather than mechanisms based on dominance or meiotic drive (Rieseberg 2001). If there is variation across the genome in the density of loci with the potential to be involved in local adaptation, then the establishment and maintenance of inversions would be biased towards regions harbouring a high density such loci under this model. If the genomic basis for local adaptation is conserved amongst species, then these same regions are more likely to have high repeatability. Thus, our observation of genomic regions harbouring inversions also being enriched for WRAs is consistent with this general model for inversion evolution. Unfortunately, our observations do not provide much insight into whether inversions evolve through the capture (e.g. Kirkpatrick and Barton 2006) or accumulation (e.g. Schaal et al. 2022) type of model, as either model would be consistent with our results. Most of the sunflower inversions are >1 My old, and therefore predate any current local adaptation patterns, but likely do not predate the genes underlying local adaptation (which appear to be shared among the species we studied). As for the alleles underlying local adaptation, they may be younger than the inversions, but as our work suggests, these regions are prone to harbouring locally adaptive alleles so it is possible that they also harboured other ancestral locally adaptive alleles.

As a minor comment, there's a fair number of places where a more nuanced view of the field is needed, e.g.:<br /> "Models in evolutionary genetics tend to focus on extremes: population genetic approaches explore cases where strong selection deterministically drives a change in allele frequency" --This seems like a strange strawman. Population genetic models span a huge parameter range. The empirical approaches of looking for sweeps by detecting genome-wide statistical outliers is predicated on strong selection, but there are numerous papers that have looked for signals of weak selection genome-wide.

Good point, we have changed our wording here.

Reviewer #1 (Recommendations For The Authors):

Comments

My main comment on the manuscript is that the different levels and diversity of analyses are slightly hard to follow on the first, and even second, read. As there are several layers of correlations and comparisons, as well as some independent analyses, I wonder if it might be helpful to have a summary schematic figure of how all analyses fit together.

Great idea, we have added Figure S1 that summarizes the main flow of the methods and research questions.

• L169-171: Would it be more accurate to say that SIPEC is maximized when both species have strong correlations for an environmental variable across the same phenotypes? But maybe I misunderstood the index.

Good point, we have now simplified SIPEC, reporting the max instead of the mean, which we think better reflects when similar patterns are happening in both species for some phenotype.

• L191: Given the discussion in the introduction and elsewhere about the correction for population structure, which version is used here? Same for Figure 3.

We have added clarification there.

• L348: One [environmental] variable?

Added

• L353: Maybe add a percentage indication for 387 so that it is comparable to the following 23.3%.

Good point, added

-> L388 and paragraph: You mention "significant repeatability" but it is hard from the results at this point to have a broad idea of the amount of signal that is repeatable. Would it be possible to add here some quantitative measure of the proportion of signal repeatable or not, even if approximated?

I wish we could, but I think the precision implied by such an approximation would involve a huge amount of uncertainty and likely inaccuracy. Because it is so hard to conclusively identify how many loci are significant but non-repeated, we really don’t have a good handle on the denominator here. We are pretty confident that the repeated loci are strongly enriched for true positives, but the non-repeated loci are also almost certainly strongly enriched for false positives. While we really want to be able to quantify this explicitly, we don’t think it’s possible given our data.

-L415-418: "If there is variation [...] involved in local adaptation", I do not follow this argument, could you rephrase?

Changed

-L447-450: As you say in the supplementary methods, your analyses exclude 3/4 of the genome. Do you think this choice has a large impact on the number of outliers observed here as the genome-wide baseline would change?

This is a very good question, but one that is quite complex and without a clear answer – we chose not to delve into it in the paper to keep the discussion streamlined. My (SY) feeling is that it is unlikely that regions harbouring transposable elements would contribute much to adaptation, but I think we really don’t know if that is true. Even excluding ¾ of the genome harbouring TEs, ¼ of the genome still constitutes a huge amount of sequence and a very large number of genes and it seems plausible that most genes and genic regions would not contribute to adaptation for a given trait, so I don’t think this would change the results too much in a qualitative way – but would almost certainly change the number of windows that are significant, etc.

• L455-457: "As we are unable [...] potentially important drivers" Could you provide the logical link here between loci of small effect and them being important drivers. I presume you mean that the large effect loci found here only account for a small proportion of the heritability?

Yes that’s what we meant here, so we’ve added some clarification.

• L482: "enriched within inversions" should that be 'in genomic regions where there exist inversions in at least one species'? Thanks for catching that, yes. Changed.

• Methods/SIPEC L512: Compared to the Results section it is unclear here what is referred to as an "environment" Is it a variable or a set of environment variables?

This is done per environmental variable.

I find the presence of the PCA for environment variables in Figure 2 misleading as my first interpretation was that PCs for environment were also used.

Good point, we have clarified this on line 190-193.

Maybe one potential addition to the formula would be to add an environment variable $j$ notation such that it reads "$SIPEC_j = \sum_i (|r_{ij,1}| + ...) ...$ where ... between environment variable $j$". I had initial difficulties to understand how this SIPEC was computed relating to environmental variables and this might help.

Given the other changes we made to SIPEC, we felt it was simpler to just present it as a single calculation on a given combination of phenotype and environment for a pair of species, and then discuss taking the mean and maximum of this later.

Finally, PCA axes explaining 95% of the variance are used, I would find it interesting to see how many PCs are used in comparison to the number of traits being measured.

We have added the following sentence to the methods describing this:

"For comparisons including H. argophyllus, 95% of the variance was typically explained by 8-10 PC axes (out of 28 or 29 phenotypes), whereas for comparisons among other taxa this included 21 or 22 PC axes (out of 65 or 66 phenotypes."

Typos

L52: --

Changed

L254: portions [of] their

Changed

L399: additional closing parenthesis

Changed

L458: signatures [of] repeated association

Changed

L554: performed [on]

Changed

L578: 5 ~~kp~~/kb windows

Changed

L601: ~~casual~~/causal SNPs

Changed

L615: ~~widow~~/window

Changed

L732: ~~Banding~~/Banting Postdoctoral Fellowship

Changed

L1002 & L960: [Supplementary] Figure

Changed

Supplementary: Some figure titles are in bold and others are not.

Changed

Reviewer #2 (Recommendations For The Authors):

Overall I found the writing to be very clear and easy to follow. Despite my comments, it was clear that a lot of thought went into how to conduct the tests and visualize the results. I recommend ending the Discussion on a positive note, rather than an impossible test.

Thanks for the positive suggestion, we have done this.

In Figure 5, is the temperature variable missing in the legend and in the plot?

No, for this plot we just combined the temperature/precipitation variables into one variable called “climate”.

Author Response

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

Reviewer #1 (Public Review):

The first major issue is related to the imaging and tracking experiment to examine the formation and migration of F-actin foci as illustrated in figure 3. The formation and centripetally migration of F-actin foci is a significant finding of this MS for the promotion of B cells to switch from spreading to contraction response. Thus, I may suggest to recommend the authors to conduct one more rigorous fluorescent molecular tracking experiment to confirm this phenomenon. Molecular tracking usually requires low labeling density, and the lifeact-GFP labeling here do not meet this requirement which may cause misidentification of the moving molecules. Permeable dye-based fluorescent speckle microscopy is recommended here to track the actin foci if applicable (P. Risteski, Nat. Rev. Mol. Cell Biol., 2023, DOI: 10.1038/s41580-023-00588w & K. Hu, et al, Science, 2007, 315, 111-115).

We thank the reviewer for the suggestion. We conducted the suggested experiment using membrane-permeable SiR-actin to track B-cell actin dynamics. Unfortunately, two significant issues prevented us from confirming the LifeAct-GFP results using fluorescent speckle microscopy. First, the concentration of SiR-actin required to visualize F-actin in the contact zone of mouse primary B-cells was relatively high due to their smaller sizes (~6 µm diameter) and non-adherent nature. With such a relatively high concentration of SiR-actin, we could not perform fluorescent speckle microscopy. Second, we observed that SiR-actin appeared to stabilize actin structures and reduce actin dynamics, further limiting its use in studying actin dynamics in B-cells.

Additionally, kymograph is used for foci tracking in figure3 and figure4. Kymograph is indeed a powerful tool for tracking cell protrusion and retraction but is not fairly suitable here, since a Factin focus is a concentrated point which may not move strictly along the selected eight lines generating kymograph. Other imaging processing method should be used to track the foci, for example, time series max projection is recommended if applicable.

We thank the reviewer for the suggestion and have tried the time series max projection. Unfortunately, it did not provide the resolution to identify individual actin foci, again probably due to the small size of primary mouse B-cells. While kymographs may not track the entire paths of these moving foci, we believe that the conclusions drawn from the kymography analysis in Figure 3 and 4 are reasonable. We generated eight kymographs for each cell in Figure 3 and three kymographs for each cell in Figure 4 to follow as many actin foci as possible within the spreading to contraction transition time window. Our analysis in Figure 3 identifies the fraction of actin foci originating from lamellipodia. In Figure 4, we used the kymographs to trace the path of putative clusters and used these to calculate their relative lifetimes and speed. While this is not what was suggested by the reviewer, our analysis provides qualitatively similar information to the time series max projection and reasonable comparisons between contracted and noncontracted cells, inhibitor-treated and untreated cells, and wild-type and WASP KO cells.

The second major issue is about the relationship between actin foci formation and NMII recruitment in figure 5. The author concludes that 'N-WASP and Arp2/3 mediated branched actin polymerization promotes the recruitment and the reorganization of NMII ring-like structures by generating inner F-actin foci in the contact zone'. However, there is a lack of strong evidence to directly show the mechanism by which myosin is recruited and the up and down stream relationship between actin foci migration and myosin recruitment. Since myosin-induced actin retrograde flow is a classical model in adherent cells, is it possible that, here also in activated B cells, the recruited myosin driven the formation and migration of actin foci? This reviewer may recommend the author to investigate whether Myosin blocking (e.g., using Y27632) can eliminate the F-actin foci formation and migration.

This is an excellent suggestion! In the revised manuscript, we have included new data showing that treatment with the non-muscle myosin II motor inhibitor blebbistatin, which is known to inhibit B-cell contraction but not spreading on Fab’-PLB (Seeley-Fallen et al. 2022. Frontiers in Immunology), interferes with the formation of inner actin foci ring-like structures, which are associated with B-cell contraction. These results together suggest that the generation of inner actin foci ring-like structure depends on the coordination between N-WASP-mediated actin polymerization and myosin contractile activity. We chose to use blebbistatin rather than Y27632 to inhibit non-muscle myosin II because in addition to the ROCK pathway, myosin light chain kinase can also activate myosin II, and Y27632 may have additional effects besides inhibiting myosin activity. The new data are shown in Figure 5G and H and discussed in the revised manuscript.

Reviewer #2 (Public Review):

Weaknesses: Minor as listed below. The working hypothesis of molecular crowding as a way to push out signalling molecules from the BCR dense foci is interesting. The authors provide evidence for that this is an active process mediated by N-WASP - Arp2/3 induced actin foci. Another possibility is that BCR dense foci formation is an indirect consequence of lamellipodia retraction. Future works should define the specific role of N-WASP, Arp2/3 and actin in the process to form BCR dense foci, especially as the BCR continue to signal in the cytoplasm.

We thank the reviewer for the comments. We have included the possibility that lamellipodial retraction may be involved in increasing the molecular density of BCR clusters and suggested future studies on the potential roles of N-WASP-dependent inner actin foci and actomyosin structures in BCR internalization and intracellular signaling in the Discussion section.

Reviewer #3 (Public Review):

The author prove their claims by mean of thorough image analysis, mainly observing and quantifying the fluorescence and the dynamics of single clusters of antigen and actin foci and analyzing two-colors dynamical images. They perform their observation in control cells, on pharmacologically perturbed cells where the action of Arp2/3 or N-WASP is inhibited, and on modified primary cells (primary derived from genetically engineered mice) to silence N-WASP or WASP. The work is sound and complete, the experiments technically excellent and well explained. Some experiments and discussions are objectively harder to describe, and given the length of the work, the reader might find itself lost some times. A graphical abstract/summary of the main way N-WASP ultimately control signal attenuation would solve this minor point.

We greatly appreciate the reviewer’s confirmation of our data quality and are delighted to accept the reviewer’s suggestion. In the revised manuscript, we have included a new figure (Figure 10) in the Discussion section, summarizing the results presented in the manuscript as a working model.

Reviewer #1 (Recommendations For The Authors):

Some minor points: Figure 1C, E, G and I shows three individual symbols, indicating three independent experiments described in legend. Please double check for accuracy.

It is better to show statistical data with representative repeat, not the merged means of independent experiments. For example, figure 1C even indicates three "0" data in CK-666 treated cells, meaning no contracting cell was found in ~75 cells, while there are other repeats showing 45% - 50% contracting cells. This applies to all figures involving individual cell imaging data, such as figure 2D, in which 30 cells from three independent experiments were pooled. The authors shall clearly state that those independent experiments are statistically indistinguishable before pooling the data.

We agree with the reviewer’s comments that these data have variability from individual mice, the quality of isolated primary B-cells, and the lateral mobility of planar lipid bilayers. To show the variability, we displayed the data from each experiment as individual data points. In the revised manuscript, we have utilized three colors of dots to represent three independent experiments in Figure 1C, E, G, and I, Figure 2B-G, and new Figure 5H, which show that the data from the three experiments have the same trend despite the variability.

In figure 7B-C, figure 8 and figure 9. The significant test results were hard to understand in which groups they compared. Please describe it in more detail in the figure legend or the method section.

In the legend, the authors claimed blue points in Figure 7B represented individual pCD79a clusters within an equal number of BCR clusters from each time points. The authors used means to qualify the change of blue points distribution. These shall be clearly stated in the Methods. Total BCR cluster numbers shall be shown also. This applies to Figure 7B, 7C, 7D and all figures in figure 8 and figure 9.

We thank the reviewer for pointing it out. We have revised Figures 7-9, where we utilized square braces to indicate groups of clusters (blue points) being compared. We have also provided additional information in the figure legend and Method sections.

Reviewer #2 (Recommendations For The Authors):

199-200: What is the consequence of increased WASP activation in N-WASP knockout B cells? Is this evaluated as increased pWASP activity and/or increased actin polymerization of WASP knockout B cells. Does WASP and N-WASP have an additive or counteractive effect on each other during spreading and contraction?

Indeed, the relationship between WASP and N-WASP, which are co-expressed in B-cells and other immune cells, is fascinating. Our previous studies, using WASP germline knockout, B-cellspecific N-WASP knockout, WASP and N-WASP double knockout mice, showed that WASP and N-WASP have both additive and counteractive effects during B-cell spreading, but B-cell contraction only depends on N-WASP (Liu et al. 2013. PLoS Biol). Double knockout B-cells fail to spread, and WASP knockout B-cells show reduced spreading but still contract, showing their additive effects. However, WASP and N-WASP suppress each other for activation, as detected by their phosphorylation. Phosphorylated WASP increases in the B-cell contact zone first, and phosphorylated N-WASP increases later when the phosphorylated WASP level decreases. Knocking out one of them enhances the phosphorylation of the other. Consequently, N-WASP knockout B-cells show increased spreading, probably due to enhanced activation of WASP, but exhibit delayed contraction. The revised manuscript has expanded the discussion on this area to relate it to the results presented in this manuscript.

560-563: Was Syk and SHIP-1 measured in the same cell? If not, the conclusion should be tempered.

Unfortunately, antibodies specific for Syk and SHIP-1 were from the same host, which did not allow us to stain them in the same cells. The revised manuscript has discussed this as a shortcoming of our work.

1204-1205: Explain better "three randomly positioned kymographs were generated" - how were they selected?

We apologize for this unclear sentence. The three kymographs were positioned to track as many inner F-actin foci as possible.

328: Change "abolished" to "reduced" to describe the data. 354-356: Unclear sentence, please edit. 1171: (H) should be (G). 1325: "PI" should be "FI".

We thank the reviewer for finding these typos and unclear sentences. We have made the corrections accordingly.

Methods: The description of the TIRF microscopy method is good. Regarding the image analysis, it is somehow difficult to have a good understanding of what was analyzed just by reading the text. Please show an example of the pipeline for the analysis from a raw image and the processing steps.

Figure 6-figure supplement 2 shows the image analysis process for tracking Fab’ clusters. We utilized the same approach for the image analysis of Figures 7-9.

Discussion: Add a paragraph to state the limitations of the study. How do the findings here translate into in vivo activation of B cells and how can this be addressed based on the data presented in this study.

We thank the reviewer for the suggestion. In several paragraphs of the revised Discussion section, we have brought up the limitations of the study and how these limitations affect the data interpretation. In addition, we have added Figure 10 and the associated text to present our working model, which explains how our findings reveal the cellular mechanism by which BCR surface signaling amplification transitions into attenuation, likely occurring in vivo.

Figure 2: Add an example of the image analysis for foci determination. From the images, it is not always clear what is a foci and what is not which makes the "number of foci" data difficult to evaluate.

We have added arrows to Figure 2A to indicate all identified inner F-actin foci in images.

Figure 3: add a kymograph for the WKO analysis.

In the revised Figure 4, we have provided a kymograph of a WKO B cell.

Figure 4M: the analysis of the "relative speed" of the "WT" samples is lower compared to the other control samples "DMSO" and "CK-689". The conclusion is that WKO have similar "relative speed" as "WT" cells, but in fact the "WT" cells may have responded poorly in this experiment. What is the author's experience and explanation?

We agree that the relative speeds of inner actin foci in the contact zone of WT and WKO B-cells are relatively low compared to DMSO and CK-689. Based on our experience, this parameter is very sensitive to the lateral mobility of planar lipid bilayers. We could only perform one pair of conditions using live cell images each time. The WT and WKO experiments were done at the end and might use relatively aged liposomes. However, it did not affect the number of inner actin foci formed and their relative lifetime, consistent with their similar relative speeds. Unfortunately, we lost the LifeAct-GFP-expressing WKO mouse colony and cannot redo this experiment using freshly made liposomes within a reasonable time.

Figure 7B-D: Add a more detailed legend for the black and brown lines in the dot plots.

We have expanded the legend for Figure 7B-D to provide additional details.

Figure 8-9: Show representative images for SYK, pSYK, SHIP-1 and pSHIP-1. Add a more detailed legend for the black and brown lines in the dot plots.

We have provided representative images for Syk, pSyk, SHIP-1, and pSHIP-1 in revised Figure 8 and 9.

Reviewer #3 (Recommendations For The Authors):

From the paper one understands that NMII is recruited by the actin foci and this recruitment pushes the foci towards the center of the synapse, in what resembles a positive feedback. Could the authors better elucidate this point? What happen at the peak of NMII recruitment? Could this be a mechanism used by the cell to end the contact and detach (which probably cannot be observed in this experimental setup)?

This is an excellent comment! We have recently shown that NMIIA recruitment peaks right before B-cell contraction occurs, and inhibition of NMII by inhibitors or B-cell conditional knockout blocks B-cell contraction and enhances signaling (Seeley-Fallen et al. 2022. Frontiers in Immunology). In the revised manuscript, we have included new data showing that treatment with the NMII motor inhibitor blebbistatin, which is known to inhibit B-cell contraction but not spreading on Fab’-PLB (Seeley-Fallen et al. 2022. Frontiers in Immunology), interferes with the formation of inner actin foci associated with B-cell contraction. These results together suggest that the generation of inner actin foci depends on the coordination between N-WASP-activated actin polymerization and myosin contractile activity, supporting the reviewer’s comment. The new data are shown in Figure 5G and H and discussed in the revised manuscript.

Whether the recruited NMII pulls B-cells away from antigen-presenting surfaces remains an interesting question. We have previously shown that high-affinity interaction of surface BCRs with membrane-anchored antigen can cause NMII-dependent B-cell membrane permeabilization, which triggers lysosome exocytosis and lysosomal enzyme-mediated antigen cleavage, allowing antigen internalization and presentation to T-cells (Maeda et al. 2021. eLife). Furthermore, NMII is required for B cells to internalize surface antigens (Natkanski et al. 2013. Science). These results support the possibility that actomyosin structures formed during B-cell contraction may further drive B-cells to internalize antigen. We have discussed this interesting point in the revised manuscript.

Some experiments/quantification are a bit more complex than others and a reader might find hard to follow them (in particular figs 7,8 and 9). The comprehension could be improved by providing a guide to read them. E.g. it is not clear what the population distribution represents (and it is not particularly affected by any manipulation. How were the group for test chosen? It seems they are based on intensity categories taken every 100 units: is it the case? even if arbitrary, this should be stated it in the legend.

We thank the reviewer for understanding the complexity of image analysis and pointing out the unclear points. Based on the reviewer’s comments, we have revised Figures 7-9 and the figure legend. We utilized square brackets to indicate groups of clusters (blue points) being compared. The comparison groups were chosen arbitrarily based on Fab’ peak fluorescence intensity every 90 units for Figure 7 and 8 and every 100 units for Figure 9.

Can the author speculate on how the actin organization passes from actin foci to recruitment of NMII and arc formation? Is it a rearrangement of the actin network (percolation) or simply recruitment of monomers?

Our previous and new results show that both N-WASP-activated Arp2/3 and NMII are required to form inner F-actin foci. Based on these results, we speculate that N-WASP and Arp2/3mediated actin polymerization may initiate the process and recruit NMII, and recruited NMII coordinates with actin polymerization to reorganize actin structures, promoting inner actin foci maturation and arc formation. We have included these possibilities in the revised discussion.

The role of SHIP recruitment as way to inhibit the signal downstream of the BCR is an interesting finding. Is this related to the termination of the synapse? Could we relate the time scales (accurately measured in this work) to contact times observed in vivo?

The reviewer raises an interesting question. In the discussion section, we have speculated that the actomyosin structures responsible for B-cell contraction are potentially the precursor cytoskeleton structures for antigen internalization. However, the relationship of B-cell contraction and signaling attenuation with the termination of the synapse remains unclear.

The BCR has been shown to be internalised mechanically: do these new data suggest a mechanisms for force generation in antigen internalization at the actin foci? Related to that, how do the dynamics of N-WASP recruitment relate to the force measurement highlighted in Traction Force Microscopy experiments (see for example Wang Sci.Signal. 2018, Kumari Nat.Comm.2019)? What happens in situation when the actin foci are unable to get transported, e.g. as on the more classical antigen on coverslip configuration?

Indeed, our results allow us to speculate that the actomyosin structures responsible for B-cell contraction potentially contribute to antigen internalization by mechanical forces. We previously showed that the B-cell-specific N-WASP knockout drastically reduced BCR internalization of soluble antigen (Liu et al. 2013. PLoS Biol), and that NMII is required for BCR internalization of membrane-associated antigen (Maeda et al. 2021. eLife and Natkanski et al. 2013. Science). The effect of N-WASP knockout on the internalization of membrane-associated antigen and traction forces generated at the contact membrane and whether traction forces are generated from the inner F-actin foci have not been determined but will be pursued in the future.

Our previous publication compared the BCR and actin dynamics of B-cells interacting with Fab’ tethered to planer lipid bilayers (Fab’-PLB) and cover glass (Fab’-G) (Ketchum et al. 2014. Biophys J). B-cells interacting with Fab’-G do not contract and generate inner F-actin foci and exhibit less dynamic BCR clusters and actin cytoskeleton than B-cells interacting with Fab’-PLB. Actin foci remain coincident with Fab’ clusters on glass rather than being positioned behind Fab’ clusters on PLB, thus driving their centripetal movement.

Minor remarks: When several experiments (mice) are presented in dot plots (e.g. fig 2D-G 4J-M), color dot plot (so called "smart plot") where each experiment is identified by a color, could be used to highlight the sample-to-sample variability.

This is an excellent suggestion. In the revised manuscript, we have utilized three shades of dots to represent the data points from three independent experiments.

Fig 6A: the fluorophore should be indicated in the picture (Fab'-AF546)

The suggested correction has been made.

Fig 6D: how is the contraction phase (purple rectangle) determined? Curve by curve or on the average curve? Please specify this in the legend.

The contraction phase (purple rectangle) was determined using the average curve of the contact area by IRM over time. We have added this sentence to the revised figure legend.

Minor typos in the material and methods: in some case C56BL/6 is written instead of C57BL/6 Corrected.

Author Response

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The investigators sought to determine whether Marco regulates the levels of aldosterone by limiting uptake of its parent molecule cholesterol in the adrenal gland. Instead, they identify an unexpected role for Marco on alveolar macrophages in lowering the levels of angiotensin-converting enzyme in the lung. This suggests an unexpected role of alveolar macrophages and lung ACE in the production of aldosterone.

Strengths:

The investigators suggest an unexpected role for ACE in the lung in the regulation of systemic aldosterone levels. The investigators suggest important sex-related differences in the regulation of aldosterone by alveolar macrophages and ACE in the lung. Studies to exclude a role for Marco in the adrenal gland are strong, suggesting an extra-adrenal source for the excess Marco observed in male Marco knockout mice.

Weaknesses:

While the investigators have identified important sex differences in the regulation of extrapulmonary ACE in the regulation of aldosterone levels, the mechanisms underlying these differences are not explored. The physiologic impact of the increased aldosterone levels observed in Marco -/- male mice on blood pressure or response to injury is not clear. The intracellular signaling mechanism linking lung macrophage levels with the expression of ACE in the lung is not supported by direct evidence.

Reviewer #2 (Public Review):

Summary:

Tissue-resident macrophages are more and more thought to exert key homeostatic functions and contribute to physiological responses. In the report of O'Brien and Colleagues, the idea that the macrophage-expressed scavenger receptor MARCO could regulate adrenal corticosteroid output at steady-state was explored. The authors found that male MARCO-deficient mice exhibited higher plasma aldosterone levels and higher lung ACE expression as compared to wild-type mice, while the availability of cholesterol and the machinery required to produce aldosterone in the adrenal gland were not affected by MARCO deficiency. The authors take these data to conclude that MARCO in alveolar macrophages can negatively regulate ACE expression and aldosterone production at steady-state and that MARCO-deficient mice suffer from secondary hyperaldosteronism.

Strengths:

If properly demonstrated and validated, the fact that tissue-resident macrophages can exert physiological functions and influence endocrine systems would be highly significant and could be amenable to novel therapies.

Weaknesses:

The data provided by the authors currently do not support the major claim of the authors that alveolar macrophages, via MARCO, are involved in the regulation of a hormonal output in vivo at steady-state. At this point, there are two interesting but descriptive observations in male, but not female, MARCO-deficient animals, and overall, the study lacks key controls and validation experiments, as detailed below.

Major weaknesses:

1) According to the reviewer's own experience, the comparison between C57BL/6J wild-type mice and knock-out mice for which precise information about the genetic background and the history of breedings and crossings is lacking, can lead to misinterpretations of the results obtained. Hence, MARCO-deficient mice should be compared with true littermate controls.

2) The use of mice globally deficient for MARCO combined with the fact that alveolar macrophages produce high levels of MARCO is not sufficient to prove that the phenotype observed is linked to alveolar macrophage-expressed MARCO (see below for suggestions of experiments).

3) If the hypothesis of the authors is correct, then additional read-outs could be performed to reinforce their claims: levels of Angiotensin I would be lower in MARCO-deficient mice, levels of Antiotensin II would be higher in MARCO-deficient mice, Arterial blood pressure would be higher in MARCO-deficient mice, natremia would be higher in MARCO-deficient mice, while kaliemia would be lower in MARCO-deficient mice. In addition, co-culture experiments between MARCO-sufficient or deficient alveolar macrophages and lung endothelial cells, combined with the assessment of ACE expression, would allow the authors to evaluate whether the AM-expressed MARCO can directly regulate ACE expression.

Recommendations for the authors: please note that you control which revisions to undertake from the public reviews and recommendations for the authors

Reviewer #1 (Recommendations For The Authors):

1. Corticosterone levels in male Marco -/- mice are not significantly different, but there is (by eye) substantially more variability in the knockout compared to the wild type. A power analysis should be performed to determine the number of mice needed to detect a similar % difference in corticosterone to the difference observed in aldosterone between male Marco knockout and wild-type mice. If necessary the experiments should be repeated with an adequately powered cohort.

We thank the reviewer for their comments. We are prepared to carry out these power calculations and repeat the experiment if necessary.

1. All of the data throughout the MS (particularly data in the lung) should be presented in male and female mice. For example, the induction of ACE in the lungs of Marco-/- female mice should be absent. Similar concerns relate to the dexamethasone suppression studies. Also would be useful if the single cell data could be examined by sex--should be possible even post hoc using Xist etc.

We are prepared to measure the levels of Ace, biosynthetic enzyme expression in female mice by qPCR, and ACE protein expression by IF. Additionally, we will test females using the dexamethasone suppression study. The single cell RNA seq analysis was used primarily to inform our model, not for experimental readout. We will explore the dataset as the reviewer suggests and will add additional plots if the analysis substantively changes our previous findings.

1. IF is notoriously unreliable in the lung, which has high levels of autofluorescence. This is the only method used to show ACE levels are increased in the absence of Marco. Orthogonal methods (e.g. immunoblots of flow-sorted cells, or ideally CITE-seq that includes both male and female mice) should be used.

We have negative controls for antibody staining. Additionally, we also used qPCR to show an increase in Ace mRNA expression in the lung.

1. Given the central importance of ACE staining to the conclusions, validation of the antibody should be included in the supplement.

The vendor of this antibody has verified by cell treatment to ensure that the antibody binds to the antigen stated .We are prepared to additionally validate the antibody using other tissues as control, though we point out that ACE is expressed, albeit at lower levels, in endothelial cells throughout the body and so some signal is to be expected in most if not all tissues.

1. The link between alveolar macrophage Marco and ACE is poorly explored.

We are prepared do co-culture experiments of alveolar macrophages and endothelial cells and measure ACE/Ace expression as a consequence.

1. Mechanisms explaining the substantial sex difference in the primary outcome are not explored.

We argue that this would be outside the scope if this project, though we would consider exploring such experiments in future studies.

1. Are there physiologic consequences either in homeostasis or under stress to the increased aldosterone (or lung ACE levels) observed in Marco-/- male mice?

We are prepared to measure blood electrolytes and blood pressure in Marco-deficient and Marco-sufficient mice.

Reviewer #2 (Recommendations For The Authors):

Below is a suggestion of important control or validation experiments to be performed in order to support the authors' claims.

1) It is imperative to validate that the phenotype observed in MARCO-deficient mice is indeed caused by the deficiency in MARCO. To this end, littermate mice issued from the crossing between heterozygous MARCO +/- mice should be compared to each other. C57BL/6J mice can first be crossed with MARCO-deficient mice in F0, and F1 heterozygous MARCO +/- mice should be crossed together to produce F2 MARCO +/+, MARCO +/- and MARCO -/- littermate mice that can be used for experiments.

We thank the reviewer for their comments. We recognise the concern of the reviewer but due to limited experimenter availability we are unable to undertake such a breeding programme to address this particular concern.

2) The use of mice in which AM, but not other cells, lack MARCO expression would demonstrate that the effect is indeed linked to AM. To this end, AM-deficient Csf2rb-deficient mice could be adoptively transferred with MARCO-deficient AM. In addition, the phenotype of MARCO-deficient mice should be restored by the adoptive transfer of wild-type, MARCO-expressing AM. Alternatively, bone marrow chimeras in which only the hematopoietic compartment is deficient in MARCO would be another option, albeit less specific for AM.

We recognise the concern of the reviewer. We have access to an AM cell line which we plan to use to do co-culture experiments with an ACE-expressing endothelial cell line. In this way we will test whether this effect is linked to AMs.

3) If the hypothesis of the authors is correct, then additional read-outs could be performed to reinforce their claims: levels of Angiotensin I would be lower in MARCO-deficient mice, levels of Antiotensin II would be higher in MARCO-deficient mice, Arterial blood pressure would be higher in MARCO-deficient mice, natremia would be higher in MARCO-deficient mice, while kaliemia would be lower in MARCO-deficient mice. Similar read-outs could also be performed in the models proposed in point 2).

We are prepared to measure blood electrolytes and blood pressure (via tail cuff method) in Marco-deficient and Marco-sufficient mice.

4) Co-culture experiments between MARCO-sufficient or deficient alveolar macrophages and lung endothelial cells, combined with the assessment of ACE expression, would allow the authors to evaluate whether the AM-expressed MARCO can directly regulate ACE expression.

To address this concern, we plan to do a co-culture experiment as outlined above.

Broadly, we thank the reviewers for taking the time to critically appraise this manuscript. The reviewers primary concern seems to be the lack of direct evidence of an effect of AMs on endothelial Ace expresion, which we plan to address as outlined above. We will adjust our conclusions as appropriate based on the results of the experiments outlined above.

Author Response

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

Our comments on the initial eLife assessment

“This study presents a useful inventory of the joint effects of genetic and environmental factors on psychotic-like experiences, and identifies cognitive ability as a potential underlying mediating pathway. The data were analyzed using solid and validated methodology based on a large, multi-center dataset. The claim that these findings are of relevance to psychosis risk and have implications for policy changes are partially supported by the results”

We sincerely appreciate the editor and reviewers for their valuable feedback and their willingness to accommodate our perspectives in the first revision. In this revision, the comments from the reviewers have allowed us to further improve our manuscript. Regarding the eLife assessment, we would like to discuss two points.

Firstly, regarding your point of our “findings are of relevance to psychosis risk…partially supported…”, we want to address that our study is closely related to psychosis risk. Childhood psychotic-like experiences (PLEs) are closely linked to psychotic risk and have been shown to increase the risk of general psychopathology, as mentioned in our Introduction and Discussion.

The reviewers asked for clearer differentiation between PLEs and schizophrenia, which we incorporated in this revision (line 100~111; line 419~430). So, this revised version now clearly points out that findings are relevant primarily to psychosis risk, and only partially relevant to schizophrenia risk.

Secondly, regarding “…implications for policy changes are partially supported…”, we have revised our study’s social contribution more clearly and specifically. Incorporating the comments, we have revised that our study offers an insight to the future studies by showing the importance of integrative approaches, considering multi-factorial neurocognition and psychopathology ranging from genes to environment (line 503~512), rather than offers direct policy implications.

Our collaboration with eLife and the reviewers has proven satisfactory and enriching. The community, coupled with the innovative system and culture established around eLife, has significantly advanced the progression of scientific research. We are privileged to contribute to this endeavor.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I am happy with the revisions provided by the authors and I think most of my concerns have been addressed satisfactorily. One remaining concern is the authors' conflation of PLEs and schizophrenia. They stated, for example, that it is necessary to adjust for schizophrenia PGS. Even though studies have found a statistical relationship between schizophrenia PGS and PLEs, this relationship is not very strong (although statistically significant) and other studies have found no relationship. Similarly, having PLEs increases the risk of developing psychosis, but that does not necessarily mean that this risk is substantial or specific. I think this needs more nuance in the manuscript and the term 'schizophrenia' should be used sparsely and very carefully as the paper has focused on PLEs. Otherwise, great work on the revisions, thank you.

Thank you for your comment on the use of PLEs and schizophrenia. We clearly understand the differences between the two and we made relevant corrections throughout the manuscript. In particular, we added that PLEs are not a direct predictor of schizophrenia and corrected any expressions that may imply that PLEs are closely related to schizophrenia in the Introduction.

“Psychotic-like experiences (PLEs), which are prevalent in childhood, indicate the risk of psychosis (van der Steen et al., 2019; Van Os & Reininghaus, 2016). Although they are not a direct precursor of schizophrenia, children reporting PLEs in ages of 9-11 years are at higher risk of psychotic disorders in adulthood (Kelleher & Cannon, 2011; Poulton et al., 2000). PLEs also point towards the potential for other psychopathologies including mood, anxiety, and substance disorders (van der Steen et al., 2019), are linked to deficits in cognitive intelligence (Cannon et al., 2002; Kelleher & Cannon, 2011) and show a stronger association with environmental risk factors during childhood than other internalizing/externalizing symptoms (Karcher, Schiffman, et al., 2021).

Maladaptive cognitive intelligence may act as a mediator for the effects of genetic and environmental risks on the manifestation of psychotic symptoms (Cannon et al., 2000; Keefe et al., 2006; Reichenberg et al., 2005).” (line 100~111)

We also revised any expressions that could be perceived as implying relevance to schizophrenia in the Discussion. “Prior research identifying the mediation of cognitive intelligence focused on either genetic (Karcher, Paul, et al., 2021) or environmental factors (Lewis et al., 2020) alone. Studies with older clinical samples have shown that cognitive deficit may be a precursor for the onset of psychotic disorders (Eastvold et al., 2007; Fett et al., 2020; Vorstman et al., 2015). Our study advances this by demonstrating the integrated effects of genetic and environmental factors on PLEs through the cognitive intelligence in 9-11 years old children. Such comprehensive analysis contributes to assessing the relative importance of various factors influencing children's cognition and mental health, and it can aid future studies designed for identifying health policy implications. Considering the directions and magnitudes of the effects, though the effects of PGS remain significant, aggregated effects of environmental factors account for much greater degrees on PLEs.” (line 419~430)

Reviewer #2 (Recommendations For The Authors):

I thank the authors for addressing most of my comments. I feel the manuscript has already greatly improved.

I have a few more comments.

1) Although I did not make this comment, I find the authors' reply to the following comment by Reviewer #1 unclear: Original comment 'I like that the assessment of CP (cognitive performance) and self-reports PLEs is of good quality. However, I was wondering which 4 items from the parent-reported CBCL (Child Behavior Checklist) were used and how did they correlate with the child-reported PLEs? And how was distress taken into account in the child self-reported PLEs measurement? Which PLEs measures were used?'

The authors' response refers to correlation coefficients, but I think Reviewer #1's inquiry was on more than these correlations.

Thank you for your concern. We think that this comment was referring to our previous manuscript submitted elsewhere. In our initial submission to eLife, we already added the details about the four items from the parent-reported CBCL and how distress was considered in the child self-reported PLEs measurement (Appendix S1, page 48).

2) Regarding the authors' reply that they have 'standardized the use of 'cognitive capacity' - I do not understand what this means. How exactly was this term standardized? In fact, I can find the term 'cognitive capacity' only once and it seemed to have been deleted from the manuscript. This is fine, but it doesn't clearly align with the statement that this term has been standardized.

We apologize for causing such confusion. What we meant was that throughout our revised manuscript, we used the term “cognitive phenotypes” instead of “cognitive capacity”.

3) Regarding my initial comment that 'it needs to be described how cognitive performance was defined in Lee 2018.' - I believe this is still not clarified. The authors write 'CP was measured as the respondent's score on cognitive ability assessments', but it remains unclear what exactly these assessments were.

Thank you for pointing this out. We added that “CP, measured as the respondent's score on cognitive ability assessments of general cognitive function and verbal-numerical reasoning, was assessed in participants from the COGENT consortium and the UK Biobank” (line 204~206).

4) Regarding the authors' reply to my comment 'In the 'Path Modeling' section, please explain what 'factors and components' concretely refer to. How is this different from a standard SEM with latent factors?'

I can see that the authors explained 'components' (=the weighted sum of observed variables), but please also add what you mean by 'factors' - and how these are different from 'components' (line 284). Furthermore, I don't think it is correct that SEMs can only model latent factors, but not components (=measured variables). I also cannot see how using a weighted sum of observed variables controls more effectively for bias in estimation than latent factors. However, even though I do have some knowledge on this method, I'm not an expert and would appreciate the authors, other reviewer and/or editor to weigh in on this point.

Thank you for pointing this out. We added that latent factors are indirectly measured indicators that explain the covariance among observed variables (line 263~271). We also added that standard SEM method using latent factors assumes that observed variables within each construct share a common underlying factor, but if this assumption is not met, then the standard SEM method cannot effectively control for biases. This is the reason why the IGSCA method, which addresses this limitation by allowing for use of both composite and latent factors as constructs.

“Standard SEM using latent factors (i.e., indirectly measured indicators that explain the covariance among observed variables) to represent indicators such as PGS or family SES relies on the assumption that observed variables within each construct share a common underlying factor. If this assumption is violated, standard SEM cannot effectively control for estimation biases. The IGSCA method addresses this limitation by allowing for the use of composite indicators (i.e., components)—defined as a weighted sum of observed variables—as constructs in the model, more effectively controlling bias in estimation compared to the standard SEM. During estimation, the IGSCA determines weights of each observed variable in such a way as to maximize the variances of all endogenous indicators and components.” (line 263~271)

5) I overall disagree with the authors' following statement 'It has been suggested from prior studies that these variables (PGS, family SES, neighborhood SES, positive family and school environment, and PLEs) are less likely to share a common factor', but I appreciate the authors' argument.

Thank you for your comment. To make clarify our statement in the manuscript, we changed the sentence to “Considering that the observed variables of the PGSs, family SES, neighborhood SES, positive family and school environment, and PLEs are evaluated as a composite index by prior research, the IGSCA method can mitigate bias more effectively by representing these constructs as components” (line 274~277).

6) Regarding 'genetic ethnicity': please describe your methods on how this was defined.

Genetic ethnicity was defined as the genetic ancestry of participants, which is included as one of observations in the original ABCD Study data. To avoid further confusion, we corrected ‘genetic ethnicity’ to ‘genetic ancestry’ throughout the manuscript.

7) Regarding 'a more direct genetic predictor of PLEs' - I still don't understand what the contrast is here. More direct than what else?

The description was unclear; we removed it from our manuscript.

8) Regarding the factor loadings in Figure 3: I don't understand how deprivation loads positively on 'low neighborhood SES', but poverty loads negatively. Shouldn't they both show the same direction of effect/loading on neighbourhood SES, while 'years of residency' should show the opposite direction (i.e., deprivation and poverty = risk, while years of residency = protective)? Are these unexpected loadings?

The authors did not yet respond to this point: 'Please also add the autocorrelations between the 3 PLE measures. I assume these were also modelled statistically, given the strong correlations between time points?' Were these correlations not modelled? Why not?

Figure 3B is still unclear. Was intelligence included here? What is the difference between Figure 3A and B? The legend suggests that 3B shows the indirect effects, but figure 3B looks like a direct effect, while 3A seem to show the indirect effect.

The reviewer’s confusion resulted from our incorrect description. The factor loadings of low neighborhood SES were marked incorrectly. The loading for ‘years of residence’ and ‘poverty’ should be switched: -0.3648 for ‘years of residence’ and +0.877 for ‘poverty’. This was a mistake when we were applying factor loadings in the Figure. We thank you for pointing this out.

We apologize for missing your point on autocorrelation. Adding autocorrelations between the three PLEs is unrelated to our research goal. In this paper, we investigated how genetic and environmental factors explain the variations in PLEs between participants, regardless of changes over time. Since we used PLEs of multiple follow-ups to ensure that the results are robust irrespective of the timing of PLE measurements, taking autocorrelation into account is not necessary.

The decision to add autocorrelation, which involves using the outcome variable at time (t-1) as a predictor for the outcome variable at time t, depends on the research focus. If your interest lies in explaining inter-individual variation in the rate of change in PLEs over a one-year period, then autocorrelation should be controlled for (typically, predictors measured at different time points are used in such cases). However, this was not the focus of this paper, which is why we did not apply autocorrelation in the SEM analysis.

We apologize for the confusion between Figure 3A and 3B. To clarify, we added titles in the figure images as “Direct effects” and “Indirect effects”. We also changed the legend as well.

“A. Direct pathways from PGS, high family SES, low neighborhood SES, and positive environment to cognitive intelligence and PLEs. Standardized path coefficients are indicated on each path as direct effect estimates (significance level *p<0.05). B. Indirect pathways to PLEs via intelligence were significant for polygenic scores, high family SES, low neighborhood SES, and positive environment, indicating the significant mediating role of intelligence.” (line 968~973)

Figure 3A shows direct effects: i.e., the coefficients of paths from PGS, family SES, neighborhood SES, and positive environment to intelligence and PLEs, as well as the coefficient of paths from intelligence to PLEs. This is why Figure 3A shows colored arrows starting from PGS, family and neighborhood SES, and positive environment towards intelligence and PLEs, as well as the arrows from intelligence to PLEs. On the other hand, in Figure 3B, the colored arrows staring from PGS, family and neighborhood SES, and positive environment goes through intelligence, and heads towards PLEs. This was meant to show that the indirect effects shown in Figure 3B indicate the specific effects of PGS, family SES, neighborhood SES, and positive environment on PLEs mediated by intelligence.

In short, Figure 3 can be seen as a diagram drawn from Table 2: direct effects of the genetic and environmental variables on intelligence and PLEs, and direct effects of intelligence on PLEs are shown in Figure 3A; indirect effects of genetic and environmental variables on PLEs mediated by intelligence are shown in Figure 3B.

9) Regarding Supporting Information tables: to make these more digestible, I suggest using Excel and adding one table per sheet with a clear title and legend, indicating what each table shows. For example, Table S1 has 9(?) different subsections, all called the same (Linear Mixed Model: Multiethnic). It is not clear how each subsection differs from the others. Separate tables in separate excel sheets might be easier.

Also, I think two decimal points might be good enough, enhancing readability of these tables.

Thank you for your suggestion. We moved the supplementary tables into an external Excel file, with each sheet showing different tables, as well as titles, legends, and clear subsections.

10) Regarding reporting exact p-values in Table 2: I don't understand. At the moment, categorical significance statements are reported. Were these not based on exact p-values (or how else was it decided if a finding was significant at a 0.05 (?) significance level).

Either remove the significance column completely (as p-values cannot be estimated due to non-normality) or specify exactly/clarify what this column shows and this was derived.

We apologize for the confusion. In Table 2, we checked the significance of each path using 95% confidence intervals with 5,000 bootstrapping iterations. Since 95% confidence intervals that does not include zero is equivalent to p-values below 0.05 significance level, we believe this is an appropriate alternative for reporting the significance of each path in the SEM model.

We specified the reason why we were not able to calculate exact p-values (clean copy: line 299~303). “As a trade-off for obtaining robust nonparametric estimates without distributional assumptions for normality, the IGSCA method does not return exact p-values (Hwang, Cho, Jung, et al., 2021). As a reasonable alternative, we obtained 95% confidence intervals based on 5,000 bootstrap samples to test the statistical significance of parameter estimates.”

Author Response

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

We would first like to thank the reviewers for their time and effort in their critical review of our manuscript, and appreciate the opportunity to address these comments. We thank the reviewers for appreciating that our experimental design is well crafted, and contributes to the broader understanding of dietary exercise recommendations for metabolic health and muscle development. We have revised the figures and text in accordance with the reviewer’s recommendations, and hope that they appreciate the revised version.

Reviewer #1:

1) A significant limitation of this study pertains to the absence of a detailed exploration into the mechanistic underpinnings of the interaction between high protein intake and resistance exercise at the molecular level. The authors should provide a comprehensive discussion on potential avenues or prospective research directions to address this gap in understanding.

We agree and have added some theories in the discussion on page 14.

2) Figure 4 and Figure 7 can be moved to supplementary and text in the description can be arranged accordingly to make a better flow of the story.

We agree with this suggestion and have made adjustments.

3) The authors have used a high protein diet (36% calorie from protein) and a low protein diet (7% calorie from protein) for this study. The authors should explain whether this mouse diet is practically comparable to the human's high protein (2% of BW) and low protein diet (less than 0.8% BW) or not. The high protein diet is comparable to a human diet of 180 grams of protein ((0.36x2000 calories)/4 calories per gram=180 g), which is in a range that some people consume, particularly bodybuilders and athletes. The low protein diet is equivalent to 35 grams of protein per day ((0.07x2000 calories)/4 calories/gram=35g), and a diet of just 7% protein is not recommended for humans per the Acceptable Macronutrient Distribution Range (AMDR) of 10-35% dietary protein set by the Institute of Medicine (IOM). We have addressed this on page 14.

4) The color coding of the error bar and lines does not match with the group description in almost every figure. Maybe the authors could choose more contrasting colors.

Thanks, we have adjusted the coloring of the error bars and lines in all figures.

5) In Figure 3C-E it seems like the number of biological samples is not consistent in the LP+WP group. If the authors have excluded any outlier from the analysis, that should be included in the methodology.

We did list outliers in the methodology in the statistics section (page 19): “Outliers were determined using GraphPad Prism Grubbs’ calculator (https://www.graphpad.com/quickcalcs/grubbs1/).”

Reviewer #2:

Very nice work! I do not have a whole lot to say in terms of experiments, analysis, or data to present other than what is in my public review (and you cannot really provide it as it was not in the experimental design). The manuscript is also very well written. My only question is about the following two sentences in the introduction:

"Both exercise and amino acids activate the mechanistic target of TOR (mTOR) protein kinase, which stimulates the protein synthesis machinery needed to stimulate skeletal muscle hypertrophy (Schiaffino et al., 2021). Therefore, The Academy of Nutrition and Dietetics recommends consuming 1.2-2.0 grams of protein per kg of body weight (BW) per day in physically active individuals (Thomas et al., 2016)." I am not sure how the second sentence follows from the first, so I am not convinced that "therefore" is the right adverb in the right place.

Thanks for pointing this out. We have added a clarifying transition to the text (page 3).