Author Response:

Reviewer #1 (Public Review):

This is an excellent paper with extensive data and important results. The authors present convincing data that resurgent sodium current from Nav1.8 and Nav1.9 channels is mediated, at least in part, by FHF proteins. [...] Altogether, the results in the paper make a major contribution to understanding the molecular events involved in generating resurgent current in Nav1.8 and Nav1.9 channels. The paper contains an impressive amount of data building on an equally impressive foundation of techniques developed in previous work and the results are clear and convincing.

We thank the reviewer for the positive comments.

There are some aspects of the presentation that could be improved. Line 74 "…and show for the first time that INaR can be reconstituted in heterologous systems by coexpressing full-length A-type FHFs with VGSC α-subunits." It seems debatable whether the expression of Nav1.8 in ND7/23 cells constitutes truly "heterologous" expression. After all, ND7/23 cells are an immortalized DRG cell line. At the least, the authors need to explain why ND7/23 cells were used for the Nav1.8 expression and to acknowledge that ND7/23 cells may express proteins in addition to the transfected Nav1.8 and FHF that could be important for the generation of resurgent current. Did they ever attempt to express Nav1.8 and FHF4A in HEK or CHO cells? There should also be a reference to the literature (I suppose Lee et al PLoS One, 14:e0221156y, 2019) showing that ND7/23 cells do not express endogenous Nav1.8 currents.

We agree with the reviewer that ND7/23 cells are not the typical heterologous cell line. While ND7/23 cells are partly derived from rat DRG neurons, multiple reports have shown that they express Nav1.8. We now cite the paper from John et. Al, 2004 “Heterologous expression and functional analysis of rat Nav1.8 (SNS) voltage-gated sodium channels in the dorsal root ganglion neuroblastoma cell line ND7-23” along with Lee et al., 2019, which as the reviewer points out showed that these cells do not express Nav1.8 message but do express mouse Nav1.6 and Nav1.7. Based on these published studies, we believe that “heterologous expression” is appropriate, but we have clarified the use of the cell line in several places and We have attempted to transiently express Nav1.8 and FHF4A in Hek293 cells, but no Nav1.8 currents were elicited under whole-cell recording configuration. We have not attempted to express Nav1.8+FHF4A in CHO cells because the literature indicates that transient transfection of recombinant Nav1.8 in CHO cells has yielded no or low-level functional currents (Zhou et al., 2019; John et al., 2004). We now explicitly acknowledge state that “ND7/23 cells are derived from the fusion of rat DRG neurons with the N18Tg2 mouse neuroblastoma cell lines, and thus may express proteins in addition to the transfected VGSCs and FHF that could be important for the differential effects on resurgent currents and long-term inactivation that we observed with Nav1.8 and Nav1.6.” in the discussion.

Author Response

Reviewer #2 (Public Review):

Suggestions to improve the paper:

Major Issues

1) I do not think that the introduction accurately reflects the state of the field with respect to single cell omics and nerve injury. The CCI model is different than the SNI model, which has been used in most previous studies, in terms of the nature of the injury, and the resolution of pain after the injury. I do not think it is accurate to claim that the CCI model is somehow more relevant clinically, because both models are just that. It is also not really true that co-mingling, un-injured neurons have not been profiled before. The Renthal paper did this, but using a different model. There is value in what the authors have done here, but they can state it more clearly in the introduction. In particular, most published studies have only used male mice, so the sex differences aspect of this work is important. In that regard, the authors did not cite any of the growing literature on sex differences in neuropathic pain mechanisms.

We revised the introduction and discussion to address the comments. Specifically, we revised the related information about animal models (Page 4-5). Although Renthal et al. examined co-mingling, “un-injured” neurons using a sciatic crush injury model, they did not find cell-type specific changes in uninjured neurons. The reason for this is unclear, but we speculate that it may be partially due to differences in the techniques (e.g., tissue processing, cell sorting, sequencing depth) and animal models (CCI versus crush injury). Compared to sciatic CCI induced by loose ligation of the sciatic nerve, crush injury would injure most nerve fibers (~50% of L3-5 DRG neurons are axotomized in this model). Therefore, the remaining “uninjured’ neurons for sequencing may be much less than that in the CCI model. In addition, we used Pirt-EGFPf mice to establish a highly efficient purification approach to enrich neurons for scRNA-seq and therefore largely increased the number of genes detected in DRG neurons. Comparatively, the neuronal selectivity and number of genes detected were lower in the previous study, which may have resulted in fewer DEGs and decreased ability to detect aforementioned changes. We include a brief discussion (Page 24).

We appreciate the reviewer’s good suggestion, and cited sex differences studies in neuropathic pain mechanisms (Pages 5, 25). Although our findings suggest that peripheral neuronal mechanisms may also underlie sexual dimorphisms in neuropathic pain, Renthal et al. reported no differences in subtype distributions or injury-induced transcriptional changes between males and females after sciatic nerve crush injury (Renthal et al., 2020). We also discussed the differences between current findings and previous work and also emphasized the sex differences aspect of this work in the discussion (Page 25).

2) I am curious about the choice to only use samples from 7 days after CCI. One of the advantages of the CCI model is that pain resolves at about 35-60 days, depending on how the ligations are done, and this allows one to look at how transcriptional programs change in DRG neurons after pain resolves. This would give some new insight, at least in comparison to the very comprehensive profiling done in the sciatic nerve crush model by Renthal and colleagues.

We thank the reviewer for this comment. We provided the rationale for day 7 post-CCI (Page 22). It is the time point when neuropathic pain-like behavior is fully developed in most animals, and the post-injury time point examined in many previous studies. The reviewer is correct, an advantage of the CCI model is that pain resolves at about 35-60 days. Although meaningful, it was not our intention to conduct a time course study to fully characterize time-dependent transcriptional changes using scRNA-seq, which is costly and requires a great effort for data analysis, etc., and is beyond the scope of the current study. We will address this in a future study, and provided a brief discussion (Page 22).

3) An alternative interpretation of the ATF3 expression is that the dissociation protocol causes this upregulation. ATF3 induction may be rapid and could occur due to the technique the authors chose to use. This could be acknowledged.

We agree and acknowledged this in our original discussion (Page 22).

4) I think the authors are a bit over-confident in their call of "injured" and "un-injured" neurons based on Sprr1a expression. This is really the only grounds for calling these neurons injured or uninjured. The fact is that the CCI model does not provide a clear way to determine injured and uninjured neurons contributing to neuropathic pain. This is an advantage of the SNL model, as shown in many classic papers from the Chung lab.

We included a brief discussion about Sprr1a (Page 22). Although Atf3 is a classic marker of injured neurons in some previous studies, a recent study suggested that Sprr1a may be a better standard to define “injured” neurons (Nguyen et al., 2017). Although injured and uninjured neurons can be readily separated in the SNL model, they are mostly from different DRGs, but not intermingled in the same DRG. Since glia-neuron interaction and neuron-neuron interaction may occur between cells within the same DRG after injury, these interactions may profoundly affect neuronal excitability and gene expression. Accordingly, we choose the CCI model for the current study to determine whether injured and uninjured neurons contribute to neuropathic pain. We included a brief discussion (Page 5, 23, 24).

5) There are now two papers on human DRG neurons that are available. One was recently published in eLife, and the other is available on Biorxiv, and has been there since Feb 2021. I expected the authors to make some comparisons of cell types that are changing in CCI with populations that are found in humans. Would similar effects be expected? Are these cell types represented in the human DRG?

Study of human DRG is important, and recent studies elegantly characterized neurochemical and physiological properties. Previous findings have suggested some notable difference between human and rodent DRGs. Importantly, many markers and methods used for classifying subpopulations of rodent DRG neurons do not apply well to human DRG neurons. In addition, data from human DRG came from patients with different etiologies, but not due to peripheral nerve injury as in the animal study. Due to these differences, we feel that it is difficult to make direct compassion of cell types that are changing in CCI with corresponding human DRG neurons.

Minor Issues

1) Does the 40 um cell strainer eliminate some larger diameter cells from the analysis?

We think this is unlikely, as large-diameter cells such as NF1 and NF2 clusters were also observed in our dataset. Importantly, we examined the cell strainer by washing it out inversely and did not find single cells. In addition, all subtypes identified in other studies were also found in our study. Nevertheless, an underrepresentation of the amount of NF neurons may be a result of the fact that not all NF neurons are GFP-positive in Pirt-EGFPf mice. In Pirt-EGFPf mice, expression of the knockin EGFPf was under the control of the endogenous Pirt promoter. Anti-GFP antibody staining revealed that GFP is widely expressed in 83.9% of all neurons. However, Pirt-negative neurons are mainly NF200+ and have large-diameter cell bodies. In addition, compared to small neurons, large neurons are also easier to lose during FACS sorting. We included a brief discussion of this potential limitation, as the NF population may be underrepresented in our sample set (Page 21).

Author Response

Reviewer #2 (Public Review):

Zhong et al conducted a scRNA-seq analysis to uncover the features in multiple myeloma (MM) based on the Revised International Staging System (R-ISS) stage. They contributed 11 scRNA-seq datasets, including 9 MM samples and 2 healthy BMMC. And validated their findings using the deconvolution method in large cohorts.

In addition, the newly identified and validated a subset of GZMA+ cytotoxic multiple myeloma cells. The experiments were nicely conducted and the datasets generated in this study might benefit many other studies. Major comments:

1) Several studies on scRNA-seq in MM have been reported, but different from that reported in this study. The authors might discuss the insight gained from their study.

Thanks for your comments. Several studies on scRNA-seq in MM have been disclosed some heterogeneity of MM. For example, Jang JS et al identified the molecular pathways during MM progression (MGUS, SMM, NDMM, and RRMM) [Blood Cancer J. 2019 Jan 3;9(1):2.]. Jean Fan et al devised a computational approach called HoneyBADGER to identify copy number variation and loss of heterozygosity in individual cells from single-cell RNA-sequencing data [Genome Res. 2018 Aug; 28(8):1217-1227.]. These studies verified the high heterogeneities existed in MM. But the specific the mechanism was not clear. Furthermore, these studies didn’t specify the heterogeneity among different stages in R-ISS staging system, which has been an international wide used prognostic stratification system. Therefore, we focused on the specific cluster, marker, and cross-talk pattern among the three stages of MM to reveal the potential mechanism of heterogeneity.

2) The author claimed Proliferating plasma cells were increased in EBV-positive MM patients. It would be interesting to examine the abundance of EBV RNA levels in the scRNA-seq datasets. Several tools, such as viral-track or PathogenTrack, might be used to conduct such analysis.

Thanks for the reviewer’s great suggestions and comments. According to your suggestion, we used PathogenTrack to identify pathogens in MM patients and added this analysis results in the file ‘Data for reviewers-1(PathogenTrack).xlsx’. However, the algorithm did not identify EBV reads in the scRNA-seq datasets. In order to verify our conclusion, we collected more MM patients’ samples and examined EBV, MKI67, and PCNA. Our result showed that EBV positive samples had significantly higher MKI67 and PCNA expression, compared with EBV negative samples on Lines 193 to 195, Page 6 (in Figure 5B and 5C).

3) Methods used for deconvolution are missing.

We thank the reviewer’s comments and suggestions. In our study, we didn’t use an analytical tool named CIBERSORT, thus we didn’t use deconvolution either in the manuscript. It may cause you a misunderstanding because of our unclear description.

Reviewer #3 (Public Review):

The authors constructed a single-cell transcriptome atlas of bone marrow in normal and R-ISS-staged MM patients. A group of malignant PC populations with high proliferation capability (proliferating PCs) was identified. Some intercellular ligand receptors and potential immunotargets such as SIRPA-CD47 and TIGIT-NECTIN3 were discovered by cell-cell communication. A small set of GZMA+ cytotoxic PCs was reported and validated using public data.

For scRNA-seq data analysis, the authors did QC and filtering and removed low quality cells, including some doublets and followed by batch effect correction. Malignant PC populations were identified using the copy number analysis tool "inferCNV".

The authors have done lots of analysis. But I think the results can be improved if they can do more analyses. I would recommend to 1) analyze doublets; 2) remove cell cycle effect; 3) GO and pathway analysis for genes with copy number change; 4) do cell-cell communication with more cell type/clusters.

Thanks for your suggestion and comment.

1) We applied Scrublet to computationally infer and remove doublets in each sample individually, with an expected doublet rate of 0.06 and default parameters used otherwise. The doublet score threshold was set by visual inspection of the histogram in combination with automatic detection. Information about this description was added to material and methods section as ‘We applied Scrublet [74] to computationally infer and remove doublets in each sample individually, with an expected doublet rate of 0.06 and default parameters used otherwise. The doublet score threshold was set by visual inspection of the histogram in combination with automatic detection.’ accordingly in Lines 731-734, Page 27.

2) As we focused on the differences in proliferative capacity of myeloma cells, the cell cycle could reflect the difference well. Therefore, the cell cycle data was provided accordingly. Information about this description was added into main text as ‘Next, we analysed the cell cycle of six PC clusters, and distinguished them from other clusters, PCs in cluster 6 (PCC6) were presumably enriched in G2/M stage (Figure. 3B)’ in Lines 142-144, Page 5.

3) We have analyzed the GO and pathway analysis for genes with copy number changes, and provided the file ‘Data for reviewers-2 and 3 (InferCNV for PCC4 and PCC6)’. Based on this, we found that oxidative phosphorylation was the most significant enriched pathways for PCC4 and PCC6, respectively. Cell-cell communication with more cell type/clusters was provided with the supplementary data in the file ‘Data for reviewers-3 (Overall T cells interaction ligand-receptor pairs dotplot, Overall T cells interaction ligand-receptor, Overall T cells interaction map)’.

Data analysis of public data was sufficient to prove the small set of GZMA+ cytotoxic PCs. More data analysis or wet experiment proof is required.

Thanks for your suggestion. The subset of cytotoxic PCs was identified in this study. These PCs exhibited NKG7 and GZMA. Furthermore, NKG7 showed the higher expression level than NKG7. Therefore, we validated it using Multi-parameter Flow Cytometry (MFC) and Immunofluorescence in MM samples. We identified a new subset of NKG7+ cytotoxic PCs and found that the percentage of NKG7+ PCs displayed obvious diversities among stage I, II and III groups. Information about this description was added in the main text as ‘In another MM single-cell dataset focusing on PC heterogeneity of symptomatic and asymptomatic myeloma (dataset GSE117156) [19], one cluster, C21, exclusively expressing NKG7 corresponded to PC18 in our dataset (Fig 2C-2D). In GSE117156 of all 42 samples, the cell proportion varied from 0% to 30.95% of all PCs, with an average percentage of 4.28% (Figure. 2E).Next, immunofluorescence confirmed the expression of NKG7 in cytoplasm of PCs (CD138 positive) from patients with MM (Figure. 2F). Finally, twenty MM patients (stage I: three patients, stage II: 10 patients and stage III: seven patients) were enrolled for multi-parameter flow cytometric (MFC) analysis. The results showed that the percentage of NKG7+ PCs displayed obvious diversities among stage I, II and III groups (Figure. 2G and Figure. S2). The average percentage of NKG7+ population was 2.73% in stage I, 8.89% in stage II and 0.58% in stage III (Figure. 2G and Figure. S3). In summary, we characterized a NKG7+ PC population (PC18), which may provide a novel perspective for the cytotherapy of MM.’ in Figure 2 and S3 and Lines 118-130, Page 4-5.

Author Response

Reviewer #2 (Public Review):

The authors argue that xgO secretes Spi and Col4a1 to induce MAPKdependent L5 differentiation. However, no loss-of-function condition for these putative ligands was tested. Since they speculated that expression of Spi and Col4a1 alone may not lead to a sufficient level of MAPK activity, the results of their loss of function conditions have to be included in the paper.

We agree with Reviewer #2 completely. Our manuscript now includes spi and Col4a1 loss-of-function data specifically in xgO, which has strengthened our manuscript considerably and allows us to draw stronger conclusions as to the roles of Spi and Col4a1.

The authors found ectopic L5 neurons when apoptosis was repressed (Fig. 1). It is likely that cells that fail to differentiate to L5 are removed by apoptosis, but this link was not clearly demonstrated in the paper. As a result, there is a gap between the data in Fig. 1 (section 1 in the text) and the other part of the paper. The relationship between Fig. 1 and the other data should be carefully discussed. In my opinion, the first section of Results should be moved after the last section so that the results of Fig. 1 are explained as a potential mechanism to remove cells that failed to differentiate to L5.

We have restructured the manuscript as suggested.

Reviewer #3 (Public Review):

There is considerable overlap with Fernandes et al 2017 Science paper: (1) That EGFR signalling is required for L5 neuron survival had been shown in their Fernandes et al 2017 Science paper, as over-expression of p35 rescued apoptosis caused by EGFRDN. Now, using Dronc mutants in the current manuscript is an equivalent experiment. (2) In Fernandes et al 2017 Science, they over-express activated MAPK in lamina neurons (Fig.1G), and in the current, they over-express its target Pnt-P1 (Fig.1I) - equivalent experiment. (3) Figure S1 reports Lamina>MAPKACT rescues Bsh and Spl2 positive neurons. These data are similar to those reported in Fernandes et al 2017 Science, where they showed the rescue of lamina neurons with this same genotype. (4) rho3 mutants cannot secrete Spi and L1-4 cannot differentiate and only a few L5 do (Fernandes et al 2017 Science), they then rescued this phenotype including L5s by over-expressing EGFRACT or Ras in wrapping glia (Figure 2F-I). With the submitted manuscript, they rescue with rho3 overexpression in photoreceptors - genetically different, but rather similar, as together they demonstrate that rescue of L5 requires rho or spi. These close similarities reduce the appeal and novelty of the current manuscript.

We agree with the reviewer that our previous work established that MAPK signalling was necessary and sufficient to drive premature neuronal differentiation in the lamina. Therefore, we have removed the data related to this point, which were previously contained in Figure S3A-C of our prior submission; namely laminats>AopACT and DroncI24; UAS-AopACT MARCM clones.

However, this manuscript makes substantially different points from the previous paper regarding the roles of EGFR activity and survival. Although Fernandes et al., (2017) did show that lamina neurons differentiated prematurely in lamina>MAPKACT, here we evaluate apoptosis and lamina neuron sub-type identities and show that the ‘extra’ LPCs do not die but differentiate into L5s under these conditions. This is a key message of our manuscript and was not evaluated nor reported before. Additionally, the Dronc mutants used here reveal that preventing apoptosis is not sufficient to drive differentiation of the additional LPC in each column, addressing a different point and not simply reproducing prior data showing the EGFR promotes LPC survival.

Similarly, we previously established that photoreceptor-derived Spi was received by wrapping glia, the involvement of photoreceptor-Spi and L5 differentiation had not been thoroughly explored and the involvement of xgO is novel.

Establishing the cells expressing spi, argos, Col41a and Ddr is key to supporting the hypothesis. The authors claim that they confirmed the best screen candidates by testing their expression using enhancer trap lines. What is the evidence that these enhancer trap reporters reproduce the endogenous expression patterns of these genes? A description of their location in the loci and potential drawbacks should be provided and discussed.

We now clarify whether enhancer traps used in our study were validated previously and provide in situ hybridization chain reaction data where enhancer traps were not previously validated.

Fig.4A and Fig.S3K do not demonstrate that aos-lacZ and Ddr-lacZ are in L5 neurons, and showing this with Bsh and Spl2 as they do for other data would support the claim that L5 neurons receive Col4a1 and distal L5 neurons can receive aos.

We use L5 specific markers with aoslacZ. For Ddr-Gal4>UAS-lacZ the entire lamina was labelled, and we provide new data showing Ddr expression by in situ hybridization chain reaction to show that it is expressed throughout the lamina.

Fig.S3M uses HCR in situ to show that spi mRNA is found in xg{degree sign} glia. However, the given images are not convincing. Since in situs detect mRNA, wouldn't the nuclear signal correspond to two sites of transcription, whereas a more abundant signal would be expected in the cytoplasm? Instead, the nucleus contains as many spots as the surrounding background and there is no clear signal in the cytoplasm. The authors must provide separate channels and convincing evidence that spi mRNA is present in xg{degree sign} glia or remove/weaken the claim (ie use only the GAL4 evidence).

We have understood that the main concern around the spi HCR included in our manuscript relates to the fact that the signal detected in the nucleus was more abundant than just two puncta as would be expected from two sites of transcription.

The reviewers are correct that only two puncta corresponding to active sites of transcription would be expected in the nucleus when detected by single molecule FISH (smFISH). However, here we are not using smFISH but HCR with maximal amplification. This results in signal proportional to the relative abundance of transcripts (Choi et al., 2018; Trivedi et al., 2018) and as such all transcripts, including those moving away from the transcription site in the nucleus, are also detected by this method. Other groups who have used this method also report the same (Andrews et al., 2020; Duckhorn et al., 2022; Schwarzkopf et al., 2020; Zhuang et al., 2020). We used this form of HCR over single molecule HCR (smHCR or digital-HCR), which uses limited amplification (Trivedi et al., 2018), as these other methods require diffraction-limited spot detection, which would be very challenging in our system.

We apologise for not explaining the HCR protocol sufficiently and have included more details in the Materials and Methods.

In addition to using HCR to detect spi expression in xgO in controls and when EGFR signalling is blocked in xgO, we now also provide new data to show Col4a1 and Ddr expression using HCR, to lend support to enhancer traps that were not validated previously. We found that both spi and Col4a1 expression in xgO decreased when EGFR signalling was blocked in xgO and provide single channel images in Figure 3 – figure supplement 1.

With this clarification, we hope the reviewers will reconsider the inclusion of these data as we feel it is important to show that xgO express these ligands in an EGFR signalling-dependent manner, especially in light of the spi and Col4a1 loss-of-function data detailed above. Nonetheless, if the reviewers still feel that these data should be removed from the manuscript, we will be happy to do so.

Involvement of Spi does not seem to have been entirely unresolved. They show that over-expression of rho3 in photoreceptors in rho 3 mutants rescued L5 neurons, suggesting that Spi from photoreceptors can rescue L5 neurons. As this is slightly different from what they saw before, what is the penetrance of these phenotypes? These phenotypes have not been quantified (other than providing sample size) and the incomplete penetrance of phenotypes could explain both observations.

Spi secreted from photoreceptor axons is insufficient to induce L5 neuronal differentiation directly as it is unable to do so when EGFR signalling is blocked in xgO (Figure 1F,H, Figure 1 – figure supplement 1N). Therefore our results argue that xgO are a critical mediator of photoreceptor signals. Since restoring rho3 expression in photoreceptors in rho3 background rescues neuronal differentiation of all lamina neurons, these results imply that the signalling relays through both wrapping glia and xgO have been reactivated.

We have quantified of the number of L5s per column in rho3 heterozygotes, rho3 homozygotes and in rho3 homozygotes when rho3 expression was restored in photoreceptors only (Figure 3C). Importantly, compared to rho3 heterozygotes, the number of L5s per column in rho3 homozygotes was significantly reduced (Figure 3C; one-way ANOVA with Dunn’s multiple comparisons test with rho3/-; GMR as control; P****<0.0001), whereas they were fully rescued in rho3; GMR>rho3 (Figure 3C; one-way ANOVA with Dunn’s multiple comparisons test with rho3/-; GMR as control; P>0.05).

They claim that whereas L5 neurons are lost in xg{degree sign}>EGFRDN over-expressing glia, concomitant over-expression of Spi rescues L5 neurons. Also, over-expression of spi with xg{degree sign}>spi clearly results in ectopic L5 neurons. However, in Fig.3P they show rescue with membrane-tethered m.spi and not secreted s.spi. Why was secreted s.spi not used instead? How does membrane-tethered spi from glia reach to rescue distal L5 neurons?

Spi is initially produced as an inactive transmembrane precursor (mSpi) that needs to be cleaved into its active secreted form (sSpi) (Tsruya et al., 2002). This requires the intracellular trafficking protein Star and Rhomboid proteases (Tsruya et al., 2002; Urban et al., 2002; Yogev et al., 2008). mSpi thus represents wild-type (unprocessed) Spi. Whereas misexpression of sSpi results in secretion of active Spi from any cell type, misexpression of mSpi results in secretion of active Spi only from cells capable of processing mSpi to sSpi.

Thus, mis-expressing mSpi to rescue L5 neurons in the xgO>EGFRDN background also demonstrates that xgO are capable of processing mSpi into sSpi, which is a more stringent experimental condition and gives us more confidence in our results. We also performed these experiments with sSpi and observed an equivalent and statistically significant rescue (included in the quantifications in Figure 3 – figure supplement 1C). We have also clarified the use of these reagents in the text as follows:

Page 6, lines 166-168:

“Spi is initially produced as an inactive transmembrane precursor (mSpi) that needs to be cleaved into its active secreted form (sSpi) (Tsruya et al., 2002). This requires the intracellular trafficking protein Star and Rhomboid proteases (Tsruya et al., 2002; Urban et al., 2002; Yogev et al., 2008).”

And Page 8, lines 221-223:

“Note that expressing either sSpi or wild-type (unprocessed) mSpi (referred to as Spiwt) in xgO rescued L5 numbers (Figure 3 – Figure supplement 1C), indicating that xgO are capable of processing mSpi into the active form (sSpi).”

To support the involvement of spi in promoting survival of proximal L5 in wildtype, a loss of function experiment would be required e.g. xg{degree sign}>spi-RNAi, and visualise apoptosis with Dcp1 and remaining L5 neurons.

We knocked down spi and Col4a1 simultaneously in xgO and observed a statistically significant decrease in the number of L5 neurons relative to controls (Figure 3T-W and Figure 3 – figure supplement 2A-B). Under these conditions we also observed Dcp1 positive cells in the most proximal row of the lamina, which were never observed in controls. Thus, suggesting that Spi and Col4a1 promote L5 neuronal differentiation and survival.

Quantifications are incomplete in places and statistical analysis is incorrect in places. For genotypes that are not quantified in graphs (ie cell number), sample sizes have been provided, but phenotypic penetrance has not (Fig.1F dronc-/-; Fig.2K, L rho3 and rescue) and this is required to report variability.

We apologise for these omissions. We have quantified the rho3 mutant and rescue phenotypes. The Dronc mutant phenotype was fully penetrant and we have stated this explicitly in the text.

Fig.2I, J: A quantification is provided within the text for apoptosis caused by xg{degree sign}>EGFRDN, with 5.93{plus minus}0.18 Dcp1 cells per column (N=19). However, this number alone does not mean much unless it is compared to Dcp1 in wild-type. Apoptosis in wild-type is shown but not quantified in Fig.2I. A comparison of Dcp1 counts in control and xg{degree sign}>EGFRDN is required and validated with statistical analysis.

We thank the reviewer for pointing out this mistake. We have now added the graph to the figure (Figure 2D) and have stated this explicitly in the text as follows:

Page 5-6, line 151-156 (Figure 2D):

“We used an antibody against the cleaved form of Death Caspase-1 (Dcp-1), an effector caspase, to detect apoptotic cells (Akagawa et al., 2015) and, indeed, observed a significant increase in the number of Dcp-1 positive cells in the lamina when EGFR signalling was blocked in the xgO (132.8 cells/unit volume ± 19.48 standard error of the mean) compared to controls (49.14 cells/unit volume ± 4.53) (Figure 2A-B, 2D, P<0.0005, Mann-Whitney U Test).”

Fig.S3L, P: authors claim that over-expression of spi in xg{degree sign}>EGFRDN does not rescue nuclear dpMAPK in xg{degree sign}, but it does in L5 neurons. However, the quantification of these data in Fig.S3L shows that nuclear:cytopl dpMAPK levels are not statistically significantly different from xg{degree sign}>EGFRDN. No evidence has been provided of how this single piece of data supports both contradictory claims. The authors must either quantify accurately and separately dpMAPK in xg{degree sign} glia and L5 neurons - it is unclear how this could be done from the data provided - or remove or modify the claim to adjust accurately to the data.

We have now quantified dpMAPK levels in both xgO and L5s in these conditions.

Statistical analysis needs revising. It is unclear why they use non-parametric tests throughout, are data always not normally distributed? The use of bar charts, means, and s.e.m. combined with non-parametric tests does not faithfully represent the data, and box plots or other displays (eg volcano or dot plots, etc) that show the distribution would be more appropriate. And multiple comparison corrections are required. For example, if Fig.S3F is a Kurskal Wallis ANOVA (should be, but it is not stated explicitly), then this requires multiple comparison tests to a fixed control (post hoc Dunn test), and the figure legend should provide the p-value for the ANOVA. Fig.3K, P use Mann Whitney test, whereas these graphs have both more than 2 sample types and therefore should be Kruskal Wallis ANOVA (if distributions are not normal, if they are normal they should be One Way ANOVA), and Dunn post hoc comparison to fixed control, box plots, and no s.e.m as above.

Thank you for flagging that we had not reported our statistical analyses appropriately. We apologise for this and have made sure to explicitly state the statistical test performed for multiple and pairwise comparisons with the Pvalues as detailed by Reviewer 3. These are highlighted throughout the text with track-changes. As well, we have changed all our graphs to box and whisker plots showing the entire distribution of the data as well as the interquartile range, as recommended.

Much of the data in our manuscript are proportions generated from cell counts and, by definition, are limited to numerical values between 0 and 1 (inclusive). As such, as with count data (i.e. discrete numbers such as from cell counts), parametric statistics are generally inappropriate for proportion data because the data violate assumptions about normality (Douma and Weedon, 2019). Therefore, we used non-parametric tests throughout the manuscript except for Figure 1- Figure Supplement 1R where appropriate assumptions were met..

Author Response

Reviewer #2 (Public Review):

This work will be of potential interest to biologists studying aging. While transposable elements have been reported to have higher expression as organisms age, it was previously unclear if their expression can exacerbate aging phenotypes or if they are a byproduct of aging. The authors present evidence in this manuscript that artificially increasing transposable element expression during the whole Drosophila life cycle can worsen aging phenotypes.

Strengths

The authors provide direct evidence that expression of their gypsy construct across the whole life of animals decreases fly lifespan (Figure 4), and that this outcome is dependent on reverse transcriptase (Figure 6).

Monitoring TE mobilization can be difficult in general and is often expensive when using a sequencing approach. The authors accurately monitor gypsy mobilization from their ectopic copy through qPCR and sequencing.

Weaknesses

Experiment design, data interpretation, and story structure:

The current model proposes that TE increases activity in aged animals and potentially contributes to the aging process. However, this paper artificially drives gypsy activation throughout the whole fly life cycle. Under this design, TE may already bring deleterious effects from early developmental stages or young age, thus ultimately shortening their life cycle. To truly test the function of TE during the aging process, the authors need to temporally control gypsy expression and only express their construct in aged animals.

Figure 1: I am not sure I got any convincing messages from this figure. First, flies at 30 days of age should not be considered as old. Second, the authors try to claim that TE expression increased with aged FOXO mutants. However, there is no data to show the comparison between aged wild-type and FOXO mutants (panel e is young wt vs young FOXO null). Meanwhile, Figure 1 has nothing to do with Gypsy. How could this figure fit into the story?

It is clear that we did not do a good job explaining this section. First, we did not mean to imply that the 30-day flies are old. They are simply older than the 5-day flies. The 30-day timepoint was chosen to match previous experiments and data sets in the literature. It was also chosen to minimize any survivor bias that could occur by doing the assay in very old flies. We have clarified this in the text and figures.

Second, it is the number of transposons that show an increase in expression in the dFOXO null animals that we mean to highlight (18 for dFOXO vs only 2 for wDAH). Panel e is meant to illustrate that the transposon landscapes, even in young flies differ by genotype making a direct transposon to transposon comparison impossible. We have added text to clarify these points.

Third, we also do not mean to imply that anything here is specific for gypsy. The work going forward in the paper uses gypsy as a tool because it is one of the better understood retrotransposons, there existed a validated active clone of the transposon and it has already been implicated in aging in the fly. We took gypsy as a model retrotransposon. We have added text to clarify here.

Figure 3: While the data presented in this Figure is sound, it is unclear how this data fits into the overall narrative that transposon activity drives aging.

Figure 3 is a continuation of the characterization of our ectopic gypsy. We wanted to rule out that there is a “hotspot” of insertion that would account for any phenotypes we observe. We find no hotspot in the males we use for analysis suggesting it is the act of transposition, not a specific target gene that is important. We have added to the text to clarify the motivation for these experiments.

Figure 5: It is interesting to see the copies of gypsy are not increased after 5 days. Does gypsy still mobilize after this young age? If yes, the authors should observe increased gypsy gDNA in later time points, unless the cells having gypsy new insertions keep dying. The authors should specifically check tissues with low cell turnover (such as brain) or high cell turnover (such as gut).

Reviewer 2 makes a great observation. In fact, using primer pairs that specifically detect the ectopic gypsy, we consistently see insertion numbers go down in very old animals (figure 5a&b). With our current understanding of retrotransposition, we should not be able to see loss of insertions unless the host cells are being lost from the analysis. We favor the idea that the reviewer suggests; that the cells that have high levels of insertion are dying and disappearing from the analysis. We think this is also reflected in the bias for intergenic or intronic sequences in our insertion mapping of figure 3. In an attempt to address this question we did measure insertions in heads versus bodies. In male flies aged 14 days there was no difference in the average number of insertions (although the variability was greater in heads). This data is reported in Supplemental Figure 6a.

Figure 8: Using Ubiquitin GAL4 to drive both gypsy and FOXO expression could dilute the expression of each individual gene. Thus, it is possible the rescue effect seen by expressing FOXO in addition to gypsy may just be due to lower gypsy expression. Including qPCR data showing gypsy expression levels in Ubi>gypsy, UAS FOXO flies compared to Ubi>gypsy flies would be helpful.

We included this data in Figure 2b and 8c. Unfortunately, we did not clearly direct the reader to compare the values. Comparing Figure 2b with Figure 8c shows the RNA level of the ectopic gypsy is comparable in both cases. Perhaps even slightly higher in the UAS-FOXO case. We have added a sentence to make this clear.

It is unclear if FOXO can rescue TE-specific aging phenotypes. While it appears that FOXO overexpression rescues the decrease in lifespan caused by gypsy expression, the authors did not test if FOXO overexpression could rescue the effects of gypsy in the paraquat resistance assays or rhythmicity experiments.

We include in this revision data showing dFOXO overexpression rescues the paraquat resistance and lowers the levels of overall insertions in the animals.

Author Response

Reviewer #2 (Public Review):

This is a nice study that pulls together a new reference genome and several levels of new popgen and RNAseq data and new analyses to provide interesting new insight on some of the evolutionary forces affecting the evolution of the ~Zal2/Zal2m system which underpins the stripe-colour polymorphism in the white-throated sparrow. The data are well balanced between homozygous Zal2/Zal2 and heterozygous Zal2m/Zal2m birds, and at a technical level, the authors do a good job of accounting for difficulties in disentangling the Zal2 and Zal2m chromosomes in heterozygous birds.

The authors convincingly show that Zal2m has signs of degeneration, similarly to what has been shown in the fire ant Sb supergene and young Y chromosomes. They show this using multiple approaches (increase in repetitive elements, reduced genetic diversity, increased non-synonymous substitutions...). But they also show that part of Zal2m (which is rare in homozygous form) has something interesting going on, with higher local diversity and evidence of balancing selection. Analysis of allelic-biased expression shows signatures of degeneration, but also that allelic bias is associated with expression differences between morphs.

The paper is generally well written and includes much novel insight on a timely topic and system.

Weaknesses in this study might come from:

• Not fully considering differences in the effects of repetitive elements on apparent genotypes (e.g, segmental duplications or jumping of repetitive elements which may have occurred in Zal2m and which lead reads to appear to be somewhere they are not).

• Difficulties in accounting for variation in recombination rates along the genome, where low recombination can lead to patterns that look like selective sweeps.

• Some ambiguities in interpreting allelic biases as adaptive where many of them can simply be collateral effects of the supergene architecture.

Many of the patterns seen and interpretations offered are similar to what is known from young sex chromosomes, such as in Drosophila, but also the anther rust mating type loci and the fire ant Sb social supergene. The haploid systems of anther rust fungus and fire ant males are able to examine such patterns in more depth than what is readily accessible here.

We appreciate an overall balanced perspective on our work. We addressed the specific concerns. Some of the limitations of the current system include the lack of high quality long-range sequence data from the species, thus making it difficult to resolve structural variation and repetitive sequences.

Author Response

Reviewer #1 (Public Review):

The authors of the paper provide new evidence of how prefrontal cortex of mutant mice used as a disease model of schizophrenia differs from wild type littermates. By analyzing local network dynamics at the level of specific cell type, authors shed new light on the circuit mechanisms that underlie changes in network dynamics in these mice.

The claims in the submitted manuscript are supported by the data. I have a few comments and questions that need to be clarified.

We thank the reviewer for highlighting the novelty of our work and its relevance (…shed new light on the circuit mechanisms that underlie changes in network dynamics in these mice…) for the field and the validity of our data (….claims in the submitted manuscript are supported by the data).

1) Average firing rates

Authors claim that they saw a significant reduction in interneuron firing rates in Disc1 mutant mice compared to control mice Fig.1c. However, the difference could be general and not interneuron specific. Due to the high firing rates of interneurons, the statistical test will work better on interneurons than on pyramidal cells as pyramidal cells average firing rates are lower. What I suggest to do is to take interneuron cells that fire at a lower rate (lower 33% for example ) and compare the control and Disc1 groups. Also I would suggest to take pyramidal cells that have higher firing rates (upper 33% for example) and compare firing rates across the same groups. One would like to see if these differences are not due to changes in firing rates per se.

We thank the reviewer for pointing out this important aspect. In our original analysis, we did not take into account that additional differences in the PYR population might be present but ‘masked’ by the overall lower firing rate of that neuronal population. As suggested by the reviewer, we separately considered the firing rate of the ‘top 33%” of the PYR population, which did not significantly differ between genotypes (p=0.958, n=209 control and 245 Disc1 PYRs, Welch’s test). As suggested, we moreover considered the ‘bottom 33%’ of INT firing rates, for which the significantly lower rates of Disc1-mutant INTs remained (control: 4.2 ± 0.6 Hz vs. Disc1: 1.8 ± 0.2, n=26 and 34 neurons, p=0.013, Mann-Whitney U-test). Since only few INTs were recorded per session in some cases (ranges: Disc1: 2-12/session; control: 2-19/session), we performed this analysis on the basis of individual cells (see also our reassessment of the main statistical comparisons in response to #1 by reviewer 2 and #4 by reviewer 3). These data are now reported in the new Fig. 1 – figure supplement 3 and referred to in line 76 ff. (line 72 ff. without tracked changes) of the revised manuscript.

2) Optogenetic tagging

Authors indicate that light triggered and spontaneous spike waveform are similar Fig.1d. This is nice, but would be better to see all the tagged neurons. I would suggest showing all optically tagged neurons spike features. Authors can impose with a different color spike features of tagged neurons in Fig.1a. I suspect that since all PVI are narrow spiking and they must fall into the area of blue colored cells in Fig.1a.

Following the reviewers suggestions, we included the average waveforms with and without light for all opto-tagged PVIs in the revised Fig. 1f. Moreover, we included the kinetic features of opto-tagged PVIs in Fig. 1a (red dots), and separately for control and Disc1-mutant mice in the new Figure 1-figure supplement 2. As predicted by the reviewer, the PVIs indeed cluster with the other putative INTs. We would moreover like to point to our new analysis in response to #2 of reviewer 2 addressing the spike kinetics of optotagged PVIs versus untagged putative INTs, which are similar in their trough-to-peak duration and asymmetry index. These data are shown in the novel Fig. 1 – figure supplement 2.

3) It was not clear why authors assessed only firing rates in last 25ms (line 348-349). If they have a clear justification for this they should provide it. But why not use the latency of the first spike also as an additional metric. A well tagged cell will respond to light pulse with short latency (within 5 ms). My concern is that non PVI cells may increase firing rate after 25ms of stimulation of PVI cells due to disinhibition.

Despite the latency to the first spike being frequently used as a method to detect ChR2-positive neurons, the laser stimulation produced significant photoartefacts in our hands. We were therefore concerned that spikes that happen shortly after the onset of the light pulse might be missed, and hence the latency to the first spike might be misinterpreted. Selecting a later time point in the stimulation interval allowed us to assess the firing rate during light application without the interference by artefacts. Nevertheless, we fully agree with the reviewer’s concern that ChR2-negative non-PVIs might increase their rate due to disinhibition, and that these neurons might thus be falsely classified as PVIs. However, we are confident that that is not the case. First, optotagged PVIs cluster well within the population of electrophysiologically identified INTs (see our response to your first remark on ‘optogenetic tagging’) and were indistinguishable from this population in terms of spike kinetics (see our response to #2 of reviewer 2 and the new Fig. 1 – figure supplement 2), suggesting that no disinhibited PYRs were included in the optotagged sample of cells. Second, we performed an additional analysis to address the time course of firing rate changes in optotagged PVIs. We computed smoothed spike trains (convolved with a 5 ms SD Gaussian kernel), and extracted the average firing rate of each optogenetically identified PVI centered on the onset of the light pulses. This analysis revealed a rapid increase in firing rate upon light delivery, arguing against disinhibitory network effects. These new data are now shown in the new Fig. 1 – figure supplement 5 and reported in line 89 (85 without tracked changes) of the revised manuscript.

4) Spike cross-correlations

The authors show that spike transmission probability from PYR to PVI is reduced in Disc1 mice compared to the controls Fig.2d and Fig.2e, but what happens to PVI to PYR spike transmission probability? Is it different in those groups? Answering this question is important since the authors discuss this topic in line 185-193.

Inhibitory synaptic interactions are indeed detectable by spike-train cross-correlation. However, we find these to be harder to quantitatively interpret than excitatory connections. Those interactions are not visible as spike transmission but rather as a reduction in spike transmission. Reliable estimates of the reduction in spike rate of postsynaptic PYRs require very large spike numbers of postsynaptic neurons that need to be sampled. For instance, Senzai et al., 2019 (Neuron 101: 500-513.e5) identified inhibitory interactions in continuous recordings lasting up to 68 h. Since we did not explicitly design our experiments to investigate inhibitory interactions, our recordings were substantially shorter than the required length. Using the method of Senzai et al., 2019 to identify inhibitory interactions, we detected only 5 INT-INT interactions (in the pooled Disc1-mutant and control data set). This low number does not allow the quantification of potentially reduced spike transmission. Thus, attempts to quantify inhibitory interactions properly would require a substantial amount of additional long-duration recordings. While the point raised by the reviewer is highly relevant and should be investigated in future, we think that given the extensive amount of experimentation needed to address this question, it is beyond the scope of the current manuscript.

5) Authors could try to link oscillations with spike transmission probabilities. On line 180 authors discuss that lower synchrony between PVI might be responsible for observed reduction in gamma power in Disc1 mutant mice. With the available data authors could test this hypothesis. They can look at spike cross correlations in their pool of INT and PVI (if they have pairs of PVI recorded in the same session) population.

We thank the reviewer for this excellent suggestion! We computed the cross-correlations for all simultaneously recorded putative INTs and quantified the baseline-subtracted mean cross-correlation within 10 ms around zero time lag. This analysis revealed weaker cross-correlation in Disc1-mutant mice (p=0.026, Mann-Whitney U test, tested on averages from n=7 control and Disc1 mice with at least 2 INTs recorded simultaneously), suggestive of reduced synchronization of putative INTs at short time lags. These new data are now included in the new Fig. 4 and reported in line 201 ff. (185 ff. without tracked changes) of the revised manuscript.

6) An alternative way to link oscillations with lower spike transmission probabilities in PYR-PVI pairs is to use synchrony triggered LFP analysis. One could take all time points when PVI and PYR cells fired acausal spikes within 2ms window and look at the LFP around this time point. Than take the average of the synchrony-triggered LFP and look at the power spectrum.

The proposal to link spike transmission with LFP power is indeed intriguing. As suggested by the reviewer, we extracted the 60-90 Hz-filtered LFPs triggered by INT spikes that followed a spike in a presynaptic PYR by <2 ms and measured the average gamma amplitude in a window of 20 ms around the INT spike. This analysis revealed comparable gamma amplitudes in Disc1 compared to control pairs. This finding suggests that local PYR-INT loops are still capable to produce gamma oscillations, and that the gamma oscillation defect of Disc1 mice is likely not caused by such a local defect. To investigate the relationship between INT spike timing and gamma oscillations more generally, we further extracted gamma amplitudes of spike-triggered LFPs using all available spikes of the INTs. Moreover, we compared the data to gamma amplitudes measured at randomly selected time points. ANOVA analysis followed by Tukey tests performed on the level of mouse averages indicated that while INT spiking-associated gamma amplitudes were significantly larger than those depicted from random time points in wild type mice (p=0.001). However, the same was not true for Disc1-mutant mice (p=0.591). Furthermore, this analysis revealed significantly reduced spike-triggered high gamma amplitudes in Disc1-mutant compared to control mice (p=0.011). While these results argue against a driving role of local connection alterations in gamma defects, they generally confirm the impaired synchrony of INT spiking relative to gamma oscillation that we observed in our analysis of phase coupling. These data are now shown in the new Fig. 4, which summarizes all new analyses regarding gamma oscillations and phase-coupling, and in figure 4 – figure supplement 2. The new results are described in the main text of the revised manuscript in line 188 ff. (172 ff. without tracked changes).

Considering the reduced short time scale synchronization of INTs (see our new results towards the reviewer’s #5) and reduced gamma amplitude of INT spike-triggered LFPs, it is possible that impaired synchronization among prefrontal INTs might contribute to the observed reduction in gamma power of Disc1-mutant mice (thereby, essentially, reflecting impaired INT gamma (ING)). Additionally, reduced long-range excitatory drive maintaining local gamma oscillations might be a contributing factor. For example, recent work showed that high gamma oscillations in the mPFC occur synchronized with gamma oscillations in the olfactory bulb (Karalis & Sirota, 2022, Nat Commun 13:467). It remains to be investigated whether local INTs are rhythmically driven by input from the olfactory bulb (in a multi-synaptic pathway including olfactory cortex) and to what extent that drive maintaining afferent gamma might be altered in Disc1-mutant mice. While the current data set does not allow a systematic evaluation of these possibilities, they should be further explored in future experiments.

7) Cell assembly analysis

The authors used 10ms for testing synchronization among pairs of PYR neurons in Fig.4a but 25ms for analysis of assembly dynamics. I think the authors justified why they used 25ms bin size, but it was not clear why they used 10ms? Could the authors clarify the reasons behind this decision?

The synchronization analysis was originally applied to PYRs converging on a common postsynaptic INT. English et al. (Neuron 95:505-520, 2017) systematically tested the effect of presynaptic cooperativity on spike transmission in the hippocampus (their Fig. 5). Their analysis revealed a maximum in cooperativity at ~10 ms. To maximize the sensitivity of our approach, we thus focused on 10 ms for this analysis. However, we agree that using the same time window as for assembly extraction is a reasonable proposal, in particular since we find no difference in the synchronization of identified presynaptic PYRs (Fig. 3e of the revised manuscript). Thus, we have recomputed cross-correlations using a 25 ms bin size. To further improve the analysis, we restricted it to neurons with at least 1000 spikes and simplified the quantification of excess spiking by using the ‘coinicident_spikes’ function of the Python package neuronpy.utils.spiketrain. Excess synchrony is now estimated by quantifying the number of coincident spikes between a reference and a comparison spike train detected in a 25 ms time window normalized by the firing rate expected by chance (2*frequency of comparison train * synchrony window * number of the reference train).

By using this improved analysis with a 25 ms time window, we could replicate our original finding of enhanced synchronization of PYR spiking. However, when we averaged the data on the basis of individual mice as suggested in #1 of reviewer 2 and #4 of reviewer 3, we could not observe this effect (irrespective of whether we used the new, coincident spikes-based analysis or the original excess synchrony analysis at either 10 or 25 ms synchrony window). This result is now stated in line 215 ff. (199 ff. without tracked changes) of the revised manuscript.

Reviewer #2 (Public Review):

This is an interesting paper, in which the authors assessed spiking and network deficits in a well-established mouse model of schizophrenia. This mouse model carries a genetic deletion of the Disrupted-in-schizophrenia-1 (Disc1) gene, which is highly penetrant in the human condition. The authors combined behavioral analyses with state-of-the-art electrophysiological recordings in vivo, coupled to optogenetic tagging, to study a subnetwork formed by a major inhibitory neuron subclass (the parvalbumin (PV)-expressing interneuron) and principal excitatory pyramidal neurons in the medial prefrontal cortex. This work indicates reduced firing rates of PV cells in Disc1-KO mice, likely due to reduced coupling with pyramidal neurons, leading to alterations in local network activity. Indeed, the authors found that Disc-KO mice exhibited reduced levels of gamma oscillations and somewhat hypersynchronous networks.

Taking advantage of novel techniques and analytical strategies, the manuscript provides rich, novel insight into the neurobiology of a mouse model of this severe psychiatric condition. The data is of high quality, the findings interesting and the manuscript is well written.

Overall, the results support the authors' conclusions, although some additional analyses are necessary to corroborate their interpretations.

Although the paper does not give information on how PV cell dysfunctions are engaged during cognitive tasks, this study can be considered as an important first step in advancing our knowledge on the basic dysfunctions of cortical networks in this model of schizophrenia

We thank the reviewer for praising the ‘high quality’ of our work, and the ‘rich, novel insights’ on the neurobiology of a mouse model of a psychiatric disorder.

1) The major findings stem from the analysis of the spiking activity of individual neurons recorded using either silicon probes or arrays of tetrodes. Both techniques allow simultaneous recording of many neurons from a single animal; therefore, from a statistical point of view neurons recorded from one animal are pseudo replicas and cannot be considered as independent measurements. Throughout the manuscript, the authors perform two-sample tests on the pooled data from all recorded neurons to compare differences between genotypes; therefore, artifactually increasing the power of statistical tests. Comparisons between genotypes should be performed using each mouse as an independent measurement.

To be able to compare the data on the basis of mouse averages, we performed additional recordings, which resulted in a final data set of 9 Disc1 and 7 control mice. We recomputed the main results of this study based on mouse averages. First, consistent with our original cell-by-cell analysis, we found significantly reduced firing rates of putative INTs but not of PYRs (line 72 (69 without tracked changes)). Moreover, we confirmed our results on decreased spike transmission probability at PYR-INT connections (line 121 (107 without tracked changes)), decreased spike transmission in the resonance window (line 163 (147 without tracked changes)), reduced high gamma power (line 173 ff. (157 ff. without tracked changes)), lower phase-coupling of INT spikes to high gamma oscillations (line 178 (162 without tracked changes)), and reduced strength of assembly activations in Disc1 compared to control mice (line 229 ff. (211 ff. without tracked changes)). Similarly, we performed new analysis on INT-INT synchronization and INT spike-triggered gamma amplitudes (as requested by reviewer 1 #5 & 6), which showed significant effects on the level of mouse averages (line 188 ff. (line 172 without tracked changes)). Second, our original finding on significant differences in the synchronization of individual PYR-PYR pairs could not be reproduced on the level of individual mice. This is reported in line 215 (199 without tracked changes) of the revised manuscript. Finally, the analyses based on optogentically identified PVIs did not allow comparison by mouse averages due to the low number of experiments (n=3 mice each). Given that the vast majority of our conclusions is based on electrophysiologically identified INTs, with optogenetic identification experiments being only confirmatory in nature, and that performing additional experiments for optogentic identification of PVIs would be very laborious, we report the results of these analyses as comparisons between neurons or connected pairs. This is clearly stated at the respective sections throughout the revised manuscript. We hope that the reviewer can agree with our decision.

2) The superficial layers of the mPFC are difficult to reach with a vertical approach of the probes due to the presence of a large blood vessel located medially in the frontal dura. Therefore, the authors are most likely reaching mPFC deep layers where PYR neurons produce fast spikes at high rates. If this is the case, this would make it difficult to sort the spiking of PYR from that of INs based on the spike kinetics and rate. The authors used opto-tagging of PVIs in a set of experiments. It would be reassuring to confirm that the spike waveform and kinetics that they extracted from PVIs are similar to those they assigned as INTs in their experiments with no opto-tagging. Identified PVIs should be statistically different from putative PYRs (not responding to light). Although opto-tagging of PVIs can solve this issue, the amount of cells isolated remains low and the number of animals is not stated. Opto-tagged cells are subsequently used for further analyses but the statistical value of those remain unclear. Since the entire interpretation of the rest of the results depend on this result, this must be clarified.

As correctly pointed out by the reviewer, we indeed targeted deep layers of the mPFC (~0.4 mm lateral of the midline; see also the histological information about the recordings sites that is now included in Figure 1 – figure supplement 1), where higher spike rates are expected compared to superficial layers. To assess whether this might have influenced the identification of putative INTs, we separately plotted the duration and asymmetry index used to classify the neurons in PYRs and putative INTs for Disc1 and control mice. This analysis yielded well separated clusters in both cases. In addition, as suggested by the reviewer, we compared the kinetic properties (spike duration and asymmetry index) and rates of PYRs, putative INTs, and optotagged PVIs. In both genotypes, ANOVA analysis followed by Tukey post-hoc testing revealed significant differences between the PYRs and both groups of INTs, both for rate (smaller in PYRs) and kinetic properties (longer spikes of PYRs) while we found no difference between putative INTs and PVIs. These results thus suggest that the method used to identify INTs works reliably. These new data are now shown in the revised Fig. 1a and the new Figure 1 – figure supplement 2 and mentioned in line 89 ff. (85 without tracked changes) of the revised manuscript.

We agree that the number of experiments using PVI opto-tagging is low (n=3 mice per genotype, this information is now included in the main text in line 93 ff. (88 ff. without tracked changes)). However, our analysis of spike transmission probability using the population of untagged putative fast-spiking INTs revealed similar results as for the sample of optogenetically identified PVIs. We view the PVI optotagging experiment as an additional confirmation that the difference in firing rate and spike transmission did likely not arise from sampling from different INT types in Disc1 and control mice, as pointed out in line 80 (76 without tracked changes) of the revised manuscript. The limitation of the low number of PVIs in our study is critically reflected in the revised discussion in line 249 ff. (229 without tracked changes).

3) Proportion of gamma coupled neurons. The authors mention the use of pairwise phase consistency (PPC). PPC is a good method to measure phase coupling independent of differences in firing rates. However, it is not entirely clear how PPC is used to measure the extent of phase locking. In the methods, the authors mention that they ran the PPC analysis after determining significant phase locking with Rayleigh's test. Moreover, they provide PPC values for high gamma oscillations but not for other frequency ranges. Perhaps, it would be better to test significant coupling of all units by nonrandom spike-phase distributions crossing a confidence interval, estimated by Monte Carlo methods from independent surrogate data set. These can be obtained upon randomly jittering each spike times. Indeed, PPC values estimated by the authors for high gamma are higher for PYR than INT (Fig. 1- Fig. Suppl 4 b). This is at odds with previously published observations in V1 (e.g. Perrenoud et al., PLoS Biol. 2016 PMID: 26890123). Given the existing reports of reduced excitatory transmission in DISC-1 mice, phase locking of PYR to other frequency bands might be affected.

Following the reviewer’s suggestion we have revised our phase-coupling analysis. First, Perrenoud et al (2016) show that gamma oscillations occur in short bursts of high power. To better reflect the coupling of putative INTs to those transient gamma events, we restricted the phase-coupling analysis to epochs within the largest quintile of gamma amplitude (assessed by the envelope of the gamma-filtered signal obtained by Hilbert transformation). Second, instead of the Rayleigh test, we obtained for each unit randomized spike trains by shuffling the inter-spike intervals (500 iterations). Significant phase locking was then obtained by testing whether two consecutive bins of the phase histogram exceeded the 95th percentile of the random distribution. This analysis was performed separately for the low (20-40 Hz) and high gamma bands (60-90 Hz) for both putative INTs and PYRs. Third, the depth of phase coupling was assessed by PPC for all significantly phase-coupled neurons. While this metric is more robust against changes in spike rates than traditional measures, it is still not completely independent of it. Perrenoud et al, for instance, showed using spike sub-sampling that the reliability in estimating PPC depends on spike rate (with >1000 spikes being optimal). However, our data set of PYRs contained fewer than 1000 spikes during high gamma events (mean Disc1: 657 ± 32, mean control: 840 ± 43). To better account for the effect of rate dependence, we restricted the analysis to neurons with >250 spikes. To further limit the potential impact of different spike counts across neurons, we used random subsampling with a fixed spike number of 250 (100 iterations per cell), computed PPC in each iteration, and averaged over the PPC estimates per cell. Finally, in response to the reviewers point 1, the results of all neurons (PYR and INT separately) were then averaged for each mouse.

Consistent with our original analysis, we found a significantly reduced proportion of phase-coupled INTs but unaltered PPC of significantly coupled INTs to the high gamma band. Moreover, we observed no significant effects for low gamma oscillations or for the phase-coupling of PYRs to either low or high gamma bands. These results are now shown in the new Fig. 4 and the new Figure 4 – figure supplement 1, and are described in line 170 ff. (154 without tracked changes) of the revised manuscript. In addition, we provide a detailed explanation of the revised phase coupling analysis, including a formal description how PPC is computed, in the Methods section of the revised manuscript in line 524 ff. (486 without tracked changes).

Using the revised phase-coupling analysis, we observed comparable PPC values of significantly coupled PYRs (0.013) and INTs (0.014) to high gamma in control mice. While the improved analysis thus resolved the paradoxical finding of lower PPC in INTs, we did not observe weaker phase-coupling of PYRs as reported in Perrenoud et al. (2016). A possible explanation for this discrepancy might be genuine differences in gamma coupling of the PYR population between visual cortex (Perrenoud et al., 2016) and the prefrontal cortex (our study), which will require further investigation in future.

Reviewer #3 (Public Review):

In the present study, the authors aim to assess network activity alterations in the prefrontal cortex of mice with a deletion variant in the schizophrenia susceptibility gene DISC1 ("DISC1 mutants"). Using silicon probe in vivo recordings from the prefrontal cortex, they find that mutant mice show reduced firing rates of fast-spiking interneurons, reduced spike transmission efficacy from pyramidal cells to interneurons, and enhanced synchronization and activation of cell assemblies. The authors conclude that "interneuron pathology is linked with the abnormal coordination of pyramidal cells, which might relate to impaired cognition in schizophrenia."

The cellular and circuit basis of psychiatric disorders has received strong interest in the recent past. In particular, alterations of the "excitation-inhibition balance" in cortical circuits has been the focus of extensive scrutiny (reviewed in pmid 22251963). Specifically, in both human samples as well as in mouse models, disruption of interneuron development and function have been implicated in the pathogenesis of schizophrenia. In the DISC1 mouse model, studies have reported disrupted interneuron development (e.g. pmid 23631734, 27244370), reduced numbers of GABAergic neurons (e.g. pmid 18945897), reduced inhibition from GABAergic neurons ex vivo (e.g. pmid 32029441), and reduced firing rates of fast-spiking neurons in vivo in the basal forebrain (pmid 34143365).

The present manuscript makes a potentially important contribution to this question by probing the microcircuitry of the prefrontal cortex in vivo in the DISC1 mouse model of schizophrenia. It goes beyond previous work in assessing circuit dynamics in vivo in more detail, albeit with indirect methods. The experiments and analysis have generally carefully been performed, though the statistical analysis raises some questions. The advances made by the present work compared to previous studies could be delineated more clearly.

We thank the reviewer for praising the analysis of our data ‘…have generally carefully been performed..’ and the ‘important contribution’ of our work to the field.

Author Response

Reviewer #1 (Public Review):

The authors use both in vitro signaling assays, knockdown in chick neural tube patterning assays and some limited use of Plexin mutant mice. The in vitro work convincingly demonstrates that misexpression of several Plexins is sufficient to enhance HH signaling in a way that depends on the Plexin GAP domain.

We thank the reviewer for the positive evaluation of our work.

Not addressed is how the GAP activity promotes HH signaling.

The reviewer raises an interesting point that we hope to address in future mechanistic studies.

The in vivo data are extremely interesting. However, alternative interpretations of the data are not assessed and need to be before the conclusions favored by the authors can be asserted.

We agree with the reviewer.

Reviewer #2 (Public Review):

This is interesting work that expands our knowledge of Hedgehog signaling. The work is well-done, well-written, and the figures are clear. I have comments that would help strengthen some of the experiments and improve the manuscript. In particular, the in vivo loss of function experiments could be measured in additional ways (using additional endpoints) to provide a convincing case of the role that Plexins play in Hh signaling in vivo.

We thank the reviewer for their favorable assessment and appreciate their recommendations to add additional in vivo loss of function experiments, which are addressed in the response to Essential Revisions.

1) The authors show that the effect of SmoM2 or Gli1 overexpression on Hh pathway activity can be potentiated by Plexins. They then conclude that "These data suggest that PLXNs function downstream of HH ligand at the level of GLI regulation...". It is unclear to me how this experiment allows them to conclude this, as the effect of Plexins could be downstream of Gli1, through the regulation of the transcription machinery, for example.

See response to Essential Revisions.

2) Are primary cilia formed normally and present at normal frequency in cells with loss or over-expression of Plexins? This could help understand better how Plexins act to modulate the Hh pathway.

See response to Essential Revisions.

3) Are Gli1 protein levels affected by Plexins?

We have not directly examined GLI1 protein levels. Future studies will investigate the consequence of PLXNs on levels, processing and localization of all GLI proteins based on the findings from this study.

4) In order to provide a convincing case for the role that Plexins play in Hh signaling in vivo, the in vivo Plexin loss of function experiments should be assessed in additional ways to Gli1-lacZ (Figure 6). Also, proliferation should be measured (as previously shown to be Hh-dependent).

See response to Essential Revisions.

5) Data showing whether Plexins bind Shh (or not) should be presented.

The reviewer raises an interesting point. However, the data with the Plxna1∆ECD construct, which lacks the entire extracellular domain suggests that PLXN binding to SHH is not required for HH pathway promotion (see Figure 3). Instead, our experiments suggest that PLXN functions downstream of HH ligand (see Figure 3).

6) The authors show that increased Plexin activity in chick neural tubes increases cell migration into the neural tube lumen. Is this effect of Plexins Gli-dependent?

See response to Essential Revisions.

7) In the chick neural tube experiments, how can the authors conclude that Plexin promotes Gli-dependent cellular responses since their data show that Plexin is not significantly affecting the fate (NKX6.1 and PAX7) of the cells? I was confused by this. The image shows a change, but the quantification does not.

See response to Essential Revisions.

8) Could loss of function experiments in chick neural tube using RNAi against multiple Plexins be performed? This would provide a very convincing case of the requirement of Plexins for Shh signaling.

While we appreciate the reviewer’s suggestion, this experiment would be technically very challenging, given that several PLXNs are expressed in the chicken neural tube (Mauti et al. 2006), and we would likely need to achieve robust knockdown of multiple Plxns to reveal a phenotype. Instead, we have relied on knockdown approaches in cell culture and genetic deletion in mice to assess the consequences of PLXN loss-of-function on HH signaling.

9) Figure 1 panels H-I need a negative control for siRNAs.

As noted in the methods (lines 571-573) and in the results (lines 128-131), negative controls for siRNAs were included in each experiment.

10) Figure 3B needs to control for Plxn1ΔECD expression levels (by western). Can higher activation of the pathway be explained by higher Plexin protein expression?

While higher PLXNDECD protein levels is one possible explanation for the increase in HH pathway activity, the subsequent data with the GAP domain and FYN kinase mutants (in the context of PLXNDECD, would argue that this is not simply a matter of protein expression, but instead is due to the previously demonstrated increase in GAP activity caused by deletion of the PLXN extracellular domain.

Reviewer #3 (Public Review):

The main strengths of this study are the compelling data derived from the use of well-established cell-based assays of Hedgehog signalling and novelty of the finding that Plexins can modulate the response of cells to Hedgehog. The experiments are well designed and carefully controlled.

We thank the reviewer for their favorable assessment.

The main weaknesses are as follows:

1) Plxna2 is expressed at levels lower than a3, b2 and d1, but it is not explained why this gene was knocked out in cell lines in preference to the other three.

We initially generated Plxna1-/-;Plxna2-/- MEFs simply due to the availability of these animals (i.e., we do not have Plxnb2 or Plxnd1 mutant mice in our colony). We then utilized siRNA to achieve a further loss of Plxna3, Plxnb2, and Plxnd1.

2) Most of the analysis and the main conclusions of the study are based on the 3T3 experiments. The data supporting the in vivo significance of these findings are less strong:

First, using electroporation of the chick neural tube, they revealed that constitutive Plexin activity can replicate only a subset of the effects of Gli over-expression. It would be relevant to know if ectopic cell migration can be caused by levels of Gli activity lower than those sufficient to induce Nkx6.1 expression - I am not sure if this is already known.

See response to Essential Revisions above.

Second, the authors investigate the consequences of loss of plexin function in the hippocampus, using mouse Plxna1 and Plxna2 mutants. This is a bit puzzling given that their own cell-based assays show that loss of either or both of these proteins has no impact on the response of 3T3 cells to ligand.

We agree with the reviewer that these were surprising results. However, the profile of PLXN expression in the hippocampus is distinct from that of NIH/3T3 cells, and the relative abundance of PLXNs also differs in these sites. Therefore, it is difficult to assess the relative importance of individual PLXNS in the hippocampus, other than analyzing individual Plxn mutant animals. Future studies investigating the individual and combined contributions of PLXNs to HH-dependent embryogenesis will be of high significance.

Moreover, a previous study cited by the authors (Cheng et al 2001) reported that Plxna3 shows the highest and most widespread expression in the CNS and in the hippocampus in particular. Plxna2, by contrast is expressed at much lower levels whilst Plxna1 was detected principally in mature pyramidal cells. It is not clear why the authors chose to focus on these particular Plexins and to what extent the requirements for Plexin function have been rigorously tested.

We agree that investigating the role of other PLXNs in the CNS will be of great value. However, as noted above, we only had access to Plxna1 and Plxna2 mutants at the time of this study.

Author Response

Reviewer #1 (Public Review):

The authors asked to what extent early visual and visuomotor experience is essential for developing the ability to recalibrate the visuo-motor system flexibly. This kind of recalibration crucially underpins everyday actions, allowing the brain to issue effective feed-forward motor control commands that correctly account for temporary changes in sensory-motor mappings (e.g. when using tools, carrying objects, wearing new glasses). To address the role of experience in developing these recalibration abilities, they used the unusual clinical population of late-operated cataract patients: children and adolescents who initially had many years of sensory experience that is atypical in that it lacked effective pattern vision. They used a standard sensory-motor task in which participants point to targets with and without displacement of the visual image via a prism lens: after the prism displacement, the visuo-motor mapping needs to be recalibrated to enable effective pointing. They compared late-operated cataract patients with controls matched in age, controls matched in both age and visual acuity (via added visual blur), as well as an extensive broader comparison group of typically developing 6- to 17-year-olds. Their key findings were that recalibration was less effective - both in the initial effect and in the subsequent after-effect - in the patient group than in control groups; this was not related to chronological age but was related to time post-operation, such that performance came to match controls after around 2 years of improved visual experience. The authors conclude that flexible sensory recalibration abilities normally rely on extensive sensory-motor experience in childhood, and suggest that the underlying computational problem is establishing the correct correspondences between sensory and motor coordinate frames. This may be achieved through extended exposure to the sensory consequences of self-generated movements.

Strengths of the approach include use of the established (although rare and difficult to access) model population of late-operated cataract patients and a well-established experimental task (pointing after displacement of the visual image by viewing through prism lenses). The task has a known typical time-course of behaviour - supplemented here by an extensive additional study on typical development using the exact same main task, which even alone would be a meaningful contribution to literature on sensory-motor development. The procedure, measures, analysis, and the approach to control groups are careful and rigorous. The findings are rich in showing not only an initial deficit in patient vs control groups but also an approximate time course for further learning and development after which point (by ~2 years) the patients come to match controls. A challenge is the heterogenous group, in terms of age at operation and ages at testing and follow-up. However, this is very usual and almost inevitable in the literature with this kind of population, and is dealt with well in the analyses. The approach is also well supplemented by repeated follow-up of a portion (actually more than half) of the group.

One potential issue is the role of baseline pointing precision differences across the groups. It would be useful to better understand the potential role of the reduced pointing precision that was found in the cataract group (Supplemental Figure 1B). It is not surprising that, following visual deprivation, this group's predictive feedforward visuo-motor control was less precise than that of controls, even in the baseline measures before any prism manipulation, and even when the controls' vision is comparably blurred. It seems likely (although is not shown) that during the adaptation phase and the post-adaptation phase, the variability of individuals around their (gradually shifting) mean pointing location would also be higher than in controls. I wonder how large an explanatory role there could be simply for this noisier initial visuo-motor mapping in the patient group. It might be said that, on each trial, they intend to carry out a feedforward plan with a certain endpoint, but because of noise, they are on average substantially further from that endpoint than comparable controls are. So, during recalibration, while controls are dealing mainly with cancelling out one kind of error - the constant error due to the prism adaptation - the cataract patients are also dealing with more variable errors due to their own noisier visuo-motor system. In theory, could this alone - higher initial noise in the system - explain the difference? This seems like a simpler explanation than that the system has developed differently in substantial ways to do with its abilities to learn and adapt. One starting point for checking in to this would be asking if initial pointing variability predicts recalibration (perhaps controlling for visual acuity), both at first test and in the repeated participants. Another would be looking into ways to perturb controls' baseline pointing performance further (perhaps with something like an unexpected added weight rather than more visual blurring) so that their variable pointing errors were matched to the cataract group.

We thank Reviewer 1 for drawing our attention to this important point. The Reviewer is right in suggesting that precision at baseline (measured as the variance of the pointing errors in the pre-prism phase) might predict recalibration abilities (as measured by the recalibration index irecal ). Indeed, we found that the variance of the errors in pre-prism phase correlates with irecal in cataract-treated participants. Thus, the higher sensorimotor noise in cataract-treated participants (indicating more uncertainty) slows down their rate of recalibration. This finding is in accordance with Burge and colleagues (2008) who found that higher uncertainty (in their case in the form of visual blur leading to more motor variability) slows down the adaptation rate. We have now reported this analysis in the Results section and discussed the contribution of sensorimotor noise to recalibration in the Discussion. However, higher sensorimotor noise cannot explain alone the performance of the cataract-treated individuals. Indeed, the subset of participants tested a second time after surgery (4-to-16 months after the first post-surgery test) presented better recalibration ability (i.e., higher irecal ), although their precision at baseline did not increase accordingly, but stayed basically unchanged. Moreover, in their second test, their precision at baseline did not correlate with the successive irecal.

In the Discussion, we added the greater sensorimotor noise as a factor contributing to recalibration. However, as it does not explain alone the improvement of recalibration performance over time, we still discuss the contribution of their lack of experience with the sensorimotor mapping to their recalibration performance.

Another question is how well the contrast sensitivity function (CSF) as a whole (not just the maximum acuity point) was matched - this is dealt with only briefly. I am not sure to what extent the blurring manipulation would be expected to change the shape of the CSF as a whole to be in line with that of patients, and to what extent other aspects of the CSF besides the maximum acuity point determine the precision and accuracy of ballistic pointing movements under the experimental and lighting conditions used in the study. Depending on the answers to these questions, the concern could be that visual differences relevant to control of pointing remained across the patient and blurred control groups.

We have now provided more information on this point in the Methods section and in the Supplementary Information. In a pilot study, we determined the range of distances between the blurring screen and the visual target that would be needed to reproduce–in controls–the range of visual acuity values of the cataract-treated participants. Nonetheless, to ensure the procedure would lead to the desired contrast sensitivity function (CSF) for each participant, we tested the visual acuity also of the sighted controls. We visually inspected the CSF of each sighted participant (tested with visual blur) and we included in the study only those whose CSF matched the desired CSFs in terms of both cut off frequency and shape. In other words, when the CSF of a sighted control did not match the one of the to-be-matched cataract-treated participant (in the cut off frequency and/or in the shape of the function), that sighted control was not included in the study. This led to excluding 8 sighted controls, before reaching the final sample of 20 controls, individually matched to the cataract-treated participants. We have now reported these further details in the paragraph entitled ‘Procedure to blur vision in sighted controls’ (Materials and Methods). Moreover, we have provided a Figure in the Supplemental Material, showing the mean CSF in the group of cataract-treated participants and in the group of sighted controls tested with visual blur (Figure supplement 1). In that figure, it is possible to appreciate that we ensured matching the two groups not only for the cutoff frequency, but also for the shape of the whole function. However, we have now also mentioned in the Discussion that we cannot exclude that other possible visual differences, besides spatial visual acuity, that we did not consider, between the group of cataract-treated and that of controls tested with visual blur might have influenced the recalibration performance.

Another more minor or technical issue is some lack of detail in how the calibration index, which feeds into most of the key analyses, is calculated. It is likely that many different ways of doing this would lead to similar conclusions, but it should be clear, including for the sake of replicability.

While the index is briefly mentioned in the Results section, we have now explained it in detail in the Material and Methods section. This recalibration index combined the amount of recalibration in the prism phase and at the beginning of the post-prism phases (Adaptation and Initial Aftereffect, respectively). Adaptation was calculated as the error reduction in the prism phase (the induced prism distortion–11.31°–minus the average of the last three pointing errors of the prism phase, cf. Fortis et al. (2010)). Initial Aftereffect was calculated as the magnitude of the aftereffect exhibited right after prism removal (i.e., average of the first three pointing errors of the post-prism phase). The Initial Aftereffect was correlated with the amount of Adaptation in the prism phase (see Material and Methods) and thus provides converging information which in order to increase power can be summarised in the recalibration index. That is, the recalibration index irecal was calculated as the average between Adaptation and the (negative) Initial Aftereffect. Such index is normalized on the induced prism distortion (i.e., the index is divided by 11.31°), so that it ranges between 0 and 1. Further details are provided in the Material and Methods section.

Reviewer #2 (Public Review):

It is very interesting that recalibration effects in the cataract-reversal group increase over time. However, it seems as if the conclusion that it takes about two years to reach recalibration effects comparable to those of typically sighted controls is based on repeated measurements of two participants tested 2 and 3 years after their surgery as well as on singular measurements of two participants tested 10 years after their surgery. Close inspection of Figure 1F suggests that four participants reached comparable levels in their second testing session already about 6 months after surgery. Consistently, the confidence interval of the time constant b is rather large (it also seems to differ between the main text and the figure caption). Given this high degree of uncertainty around the time estimate it would be advisable to not report and discuss a fixed duration of two years but rather focus on the increase of recalibration effects and report an interval during which recalibration effects might reach asymptotic levels.

We thank Reviewer 2 for drawing our attention to this important point. Following this advice, we have now discussed the high inter-subject variability in the recalibration performance over time, and we have discussed the uncertainty inherent in the estimate of the rate of improvement leading to a performance comparable to healthy controls within about 2 years - this estimate for sure is very uncertain (see Results and Discussion).

It is important to note that the exponential fit on all measurements (Figure 1F, dark green curve) is not driven by the 2 participants tested more than 10 years after surgery: when excluding them from the exponential fit, the time constant b (b=1.5, 95% CI=[0.39, 2.67]) is comparable to the one obtained in the whole sample.

We have also reported the linear correlation between time since surgery and recalibration index in the first testing session without the 2 participants tested more than 10 years after surgery, as they would drive the correlation. Note that the effect of time since surgery is evident even when removing them from this analysis (main text, red line in Figure 1 F, and Material and Methods). Importantly, also the linear fit on the first test session alone (excluding the participants tested more than 10 y after surgery) provides converging evidence of the fact that the performance level of controls (tested with visual blur) is reached at roughly 2 years from surgery, as visible in Figure 1F (red regression line crossing dashed line of controls).

Regarding the time costant b previously reported in the figure caption, this was related to the inlaid reported in Figure 1 F in the last submission (i.e., the exponential fit on the difference between each pair of cataract participants and controls). We have now removed this inlaid from the figure and its relative fit (in the figure and figure caption) to avoid confusion.

Having longitudinal data from several participants is great and can provide interesting insights. However, to get an idea about the role of visuo-motor experience it would be helpful to not collapse across the different time points for the second evaluation in the depiction of the data and their analysis. Moreover, it would be helpful to have an idea of the degree of variability across repeated measurements in control participants.

We decided to report these data in two ways: 1) In agreement with Reviewer 2, we showed these longitudinal data in their different time points (Figure 1F), so that the progression of the recalibration ability over time after surgery would be more transparent and easier to appreciate; 2) We still present these data also collapsed in Figure 1 E, because we believe this representation helps clarity and completeness: given that we also included the pre-surgical assessment in that figure, it is easier to visually appreciate the differences between pre- vs. first post-surgical assessment and second post-surgical assessment in the re-tested participants. We also rearranged the text accordingly. However, if the Reviewer still believes that this way of reporting the results is unclear or redundant, we will remove Figure 1E.<br /> Unfortunately, we were unable to collect comparable repeated measures from the control children with the same temporal gap between the first and second test.

Visuo-motor adaptation and aftereffects are related but clearly separate phenomena not least because visual feedback about the position of the finger was only present during the adaptation phase. Combining both effects into one index potentially obscures differential effects of developmental vision on the processes underlying either phenomenon. This concern is supported by the result that the manipulation of visual precision in typically developed controls affected visuo-motor adaptation and aftereffects differentially. Thus, it would be preferable to drop the combined index and analyze adaptation and aftereffects separately throughout. This will have the additional advantage of allowing for direct comparisons of both effects to those reported in the extensive literature on the topic.

We are grateful to Reviewer 2 for bringing this important point to our attention. We have now run all the correlational analyses separately for adaptation (i.e., error reduction in the prism phase) and aftereffect (mean systematic error in the post-prism phase). We have described these analyses in the Results section and in the Material and Methods section. However, as these separate analyses led to comparable results for adaptation and aftereffect, we did not report them in detail in the main text, as they would be very redundant. While it is possible to appreciate each of them in detail in the Supplemental Materials (Figure 1– figure supplement 4), in the main text we avoided this redundancy by combining them into a unified measure, the recalibration index (irecal). Reviewer 2 is right in highlighting the difference between adaptation and aftereffect. Note, however, that the recalibration index does not include the entire aftereffect (which may have a different time constant as it may well be distinct from the adaptation), but only the amplitude of the initial three trials of the aftereffect after removing the prism (i.e., the mean of the first three pointing errors of the post-prism phase). This initial amplitude of the aftereffect (that we have now called “Initial Aftereffect”) is highly correlated with the amount of recalibration in the prism phase. We have now discussed this point in the Results section. In other word, the recalibration index did not include the aftereffect in the entire post-prism phase (i.e., the systematic error across all trials of the post-prism phase). In fact, we agree with the Reviewer that including the development of the after effect across all trials of the post-prism phase would have potentially shown a different phenomenon, namely the effect of proprioception while reinstating the usual sensorimotor mapping. Indeed, at odds with the prism phase, the pointing task in the post-prism phase was performed in the absence of any optical distortion and in the absence of visual feedback. The development of the aftereffect across all trials of the post-prism phase is analysed in the main text and in Figure supplement 3, while the correlations between each factor (age, visual acuity, etc.) and the mean aftereffect across all trials of the post-prism phase is reported in Figure supplement 4. We have now also clarified all these points in the main text and in the Materials and Methods.

The absence of a significant statistical effect does not provide evidence for the absence of the effect. This problem arises in several instances throughout the paper. For example, a non-significant Kruskal-Wallis-Test does not indicate a similar distribution of baseline pointing errors. A figure showing the distribution of pointing errors from this phase provides far more convincing evidence (l. 134). A non-significant t-test does not provide for the absence of a relation between the change in recalibration effects and visual acuity (l. 225). Here, it would be correct to state that there was no statistically significant difference between visual acuity at the two different post-tests.

The problem that the absence of statistical effects does not allow for any conclusions is even more evident for the correlational analyses, which are severely underpowered. The non-significant correlations should be reported in the supplement rather than in a prominent position in the manuscript and all conclusions based on non-significant correlations must be dropped.

We have now modified the text and Figure 1 accordingly, by rephasing the text and removing the non-significant correlations from the figure.

Figures 1C and 1F suggest that the significant correlation between the time since surgery and recalibration effects might be driven by outliers. The analysis should be repeated without outlier data to make sure that the effect is present in the data.

As reported in the first response to Reviewer 2, we have now re-run the analyses also without the participants tested more than 10 years after surgery. The effect of time since surgery is present even when removing the outliers (See main text and Figure 1F).

The abstract makes rather general claims about the influence of developmental vision on recalibration and plasticity which are not supported by the data. All conclusions should be restricted to the visuo-motor domain, which in my view will not impact their importance.

We thank the Reviewer for the comments, and we have adapted the abstract accordingly.

Given that most participants had residual light perception, it would be more accurate to consistently speak of absent pattern vision rather than visual deprivation.

We have rephrased the text accordingly.

Author Response

Reviewer #1 (Public Review):

“Strengths of the paper include the use of the novel promoter (which is stated to have ~50-fold higher abundance in SGCs than astrocytes) and the dataset itself, which is for the most part thorough and convincing.”

We thank the Reviewer for appreciating the novelty of the study, and that in general, our findings are well-supported and convincing.

“Concerning specificity, CNS involvement through effects on other cell types is not totally ruled out in these studies, and effects on the same cell type but in other ganglia (parasympathetic and sensory) might be expected to impact sympathetic function. For example, as Vit (2008) reported that following shRNA knockdown of Kir4.1 in trigeminal ganglia hypersensitivity to mechanical stimulation could affect autonomic activity. The authors tested for the influence of parasympathetic using pupillary constriction, and it is somewhat surprising that there is no deficit if neuronal death and dysfunction are as profound in parasympathetic ganglia as shown here for the superior cervical ganglia.”

We include new results to show that the elevated heart rate in BLBP:iDTA mice is prevented by chemically ablating sympathetic nerves using 6-OHDA (Figures 3E-F, revised manuscript). Since 6-OHDA does not cross the blood-brain barrier in adult mice after i.p injections (Kostrzewa and Jacobowitz, 1974), we conclude that these results point to a peripheral locus for the cardiovascular defect in BLBP:iDTA mice. Since 6-OHDA is selective for sympathetic nerves, we also reason that the potential loss of sensory or parasympathetic satellite glia do not contribute to the increased heart rate in BLBP:iDTA mice. As the Reviewer notes, we also found that BLBP:iDTA mice fully constrict their pupils in response to light, indicative of normal parasympathetic function.

We do not exclude the possibility of defects in sensory or parasympathetic ganglia in BLBP:iDTA mice. A comprehensive analysis of these two systems will warrant significant effort, which we respectfully state is outside the scope of this initial study where we have focused on satellite glia in the sympathetic nervous system. However, our results in the revised manuscript and in the original submission provide evidence that enhanced sympathetic tone is responsible for driving the autonomic defects (elevated heart rate and pupil dilation) observed in BLBP:iDTA mice.

To the Reviewer’s point about CNS involvement in the autonomic dysfunction in BLBP:iDTA mice, we cannot completely exclude the possibility since BLBP is also expressed in astrocytes, albeit to much lower levels (45-fold less) compared to satellite glial cells. However, as discussed in our original submission, astrocyte ablation results in severe motor deficits in mice including limb paralysis, ataxia, as well as smaller body weights (Schreiner et. al, 2015), none of which were observed in BLBP:iDTA mice. These results suggest that astrocytes are minimally perturbed in BLBP:iDTA mice.

“Physiological effects of DTX but not Kir4.1 deletion increased sympathetic activity, whereas increased heart rate was also observed following chemical activation of SGCs using DREADD ligands (Xie et al., 2017). This opposite action is not discussed at length but is attributed to "context-dependence." Inconsistent results with stimuli believed to target the same substrate are worthy of additional consideration by the authors.”

The Reviewer asks about the differences between our findings and a previous study (Xie et. al., 2017) where the authors reported increased heart rate with chemo-genetic manipulation in Gfap-hM3Dq mice. In contrast, we observe increased heart rate with satellite glia ablation in BLBP:iDTA mice. We are unable to reconcile the apparent differences because of the following reasons:

(i) The experimental manipulations in the two studies are very different; acute chemo-genetic manipulation (over a time-scale of minutes) versus genetic ablation of satellite glial cells (over two weeks), making it difficult to directly compare behavioral outcomes (heart rate) at the whole animal level.

(ii) The Reviewer does not distinguish between activation of the Gq-GPCR signaling pathway in satellite glial cells using DREADD ligands in the Xie et. al., study versus “activation” of satellite glia. It remains unknown how activation of this signaling pathway affects satellite glia physiology and functions. Indeed, it remains unclear what “activation” or “silencing” even mean for satellite glial cells. For satellite glial cells, it remains unknown as to how calcium mobilization affects these glial cells, and how this in turn, affects neuronal activity.

We have read the manuscript by Xie et. al., carefully and could not find any direct evidence for exactly how DREADD-based activation of the Gq-GPCR signaling pathway in satellite glial cells could activate sympathetic neurons. The authors speculate that activation of the Gq-GPCR signaling pathway in satellite glia could activate sympathetic neurons via modulating glutamate transporters or inwardly rectifying K+ channels expressed in satellite glia. However, there are no glutamatergic neurons in sympathetic ganglia, and whether glutamate transporters in peripheral satellite glia have a role in glutamate uptake analogous to CNS astrocytes remains to be established. Further, if activation of the Gq-GPCR signaling pathway in satellite glia would lead to increased K+ uptake, as occurs in astrocytes, then this would result in reduced sympathetic neuron activity. However, Xie et. al., observed an increase in sympathetic tone in Gfap-hM3Dq mice.

(iii) The cellular specificity of the Cre driver lines used in the two studies are different. We, and others, have shown that BLBP is a highly specific satellite glial cell marker (this study; Mapps et. al., 2022; Avraham et. al., 2020; 2021; 2022). Notably, using single-cell sequencing, we, and others do not detect GFAP in mouse satellite glial cell under normal or reactive conditions (Mapps et. al., 2022; Mohr et. al., 2021; Jager et. al., 2020), although it is found in rat satellite glial cell (Mohr et. al., 2021), raising the question of the suitability of GFAP as a satellite glia-specific marker in mice.

We have included a modified version of this Discussion (pages 18-19, revised manuscript).

“An alternative conclusion from the finding that the similar cellular level changes in sympathetic neurons induced by DTX and Kir4.1 cKO led to distinct changes in autonomic tone is that the neuronal phenotype does not dictate whole animal physiology”

We have made this same point in our original submission that while BLBP:iDTA and Kir4.1 cKO mice show similar neuronal phenotypes at the cellular level, the loss of a single gene, Kcnj10 (for Kir4.1), from satellite glial cells is not sufficient to drive behavioral changes (pupil size and heart rate) at the whole animal level as seen with satellite glial cell ablation. We reason that there are Kir4.1-independent mechanisms that contribute to neuronal excitability to drive network-level changes.

“Spatial buffering is given as the proposed benefit of Kir4.1 channels to the sympathetic neurons. However, this concept arose from studies in which clearance of local extracellular space was limited, and astrocytes were appreciated to be connected to a vast syncytium allowing siphoning away from the high levels near active neurons. The organization in peripheral ganglia differs in three major respects: Despite narrow extracellular space, there is no true barrier to diffusion of K ions from the neurons (one factor that makes drug targeting peripheral neurons appealing), SGCs are very thin (and thus without spatial consequence to uptake), and the coupling among the SGCs is local to those surrounding individual neurons, with very little coupling under normal conditions to other distal SGC-neuron units.”

Briefly, previous studies indicate that satellite glial cells are capable of influencing neuronal excitability by dissipating extracellular K+ increases, largely by acting via Kir4.1 channels (Tang et. al., 2010). In addition, we include in the revised Discussion (page 16, revised manuscript) other ways by which Kir.4.1 loss in satellite glial cells could indirectly influence neuronal excitability, notably by promoting membrane depolarization of satellite glia or through regulation of diffusible signals such as BDNF.

Reviewer #2 (Public Review):

“Mapps and colleagues' potentially very interesting and important work investigates the biological function of satellite glial cells (SGCs) in the nervous system. SGCs are extremely understudied, even compared to other glia, which are themselves generally understudied compared to neurons. Thus, discoveries concerning what SGCs do would be of very high importance.”

We thank the Reviewer for appreciating the novelty and importance of the study.

“Major Concerns:”

“I have major concerns related to the experimental approach to ablate SGCs, specifically in sympathetic ganglia, the successful accomplishment of which underlies the entire study.”

• Most troublingly, in Figure 1E, Sox2(+) cells do not appear to be gone 14 days post-tamoxifen injection, just dimmer. The cell bodies in the treated panel also appear much dimmer than controls (on a separate note, these cell bodies do not appear to be atrophied, as shown in Figure 2A, which is also confusing). Although Figure 1B shows decreased Blbp levels by IF, there is no quantification. Coupled with the data that tamoxifen administration does not cause any change in phagocytic immune cells, as one might expect if a population of cells was ablated, this raises concerns about whether the experimental paradigm is working as expected. The authors need to convincingly show that SGCs are ablated from sympathetic ganglia for any subsequent critical claims to be supported.”

We include new data to demonstrate the loss of satellite glial cells in BLBP:iDTA mice. Briefly;

(i) There is a significant increase in the number of TUNEL+; Sox10+ satellite glial cells in BLBP:iDTA sympathetic ganglia at 5 days post-tamoxifen injection (Figures 1E, G, revised manuscript)

(ii) Expression of several satellite glia-specific transcripts, including BLBP, is markedly decreased in BLBP:iDTA sympathetic ganglia, revealed by q-PCR analyses (Figure 1-figure supplement 2H, revised manuscript).

(iii) We re-analyzed the images of Sox2-labeling by generating binary images, which removes the dependence on pixel values and simply records the presence/absence of a signal. Quantification revealed a substantial decrease in Sox2-labeled cells (33% decrease) in the BLBP:iDTA ganglia compared to controls at 14 days post-tamoxifen injections (Figure 1-figure supplement 2D-G in the revised manuscript). The 33% decrease in satellite glial cells, when analyzed in this manner, is lower than the 54% loss we had initially reported, suggesting that we may have included some proportion of cells that had down-regulated Sox2 expression but had not been ablated. We have clarified this point in the Results section (page 7, revised manuscript).

Together, our results indicate that a significant proportion of SGCs are being ablated in BLBP:iDTA sympathetic ganglia.

“Given the lack of changes in phagocytes in the experimental approach, it would also be important to show what happens to this large population of dead SGCs to understand the environment of the ganglia more fully and to interpret cellular and behavioral phenotypes better”

Using IBA-1 labeling, we show that macrophage density is unaffected in BLBP:iDTA sympathetic ganglia. However, we do not make any conclusions about the reactivity of the macrophages or their ability to engulf dying satellite glia. It is also possible that persisting satellite glia in BLBP:iDTA ganglia are involved in clearing apoptotic cells, as reported by Wu et. al., 2009. We respectfully state that addressing the precise mechanisms by which dying satellite glial cells are cleared from the mutant ganglia is outside the scope of the current study.

“• If the transgenic approach can be shown to be working to ablate SGCs as expected, it would be important to demonstrate that Blbp is not driving diphtheria toxin in any other cell type. The authors rule out a role for Schwann cells based on prior RNAseq and reporter mouse studies, but they do not verify these findings in their system. RNAseq can lack sufficient depth, and reporter mice do not always faithfully recapitulate endogenous expression. Similarly, the authors rule out astrocytic contributions based on lack of phenocopy but do not directly examine CNS tissue to support this claim.”

We have provided additional evidence in the revised manuscript to support the cellular specificity of BLBP expression in satellite glial cells using single-cell RNA sequencing data from our lab and others (Mapps et. al., 2022; Avraham et. al., 2020; 2021; 2022) as well as the use of genetic reporter mice. Our single-cell RNA sequencing analyses also revealed that Schwann cells are scarce in sympathetic ganglia compared to sensory ganglia (Mapps et. al., 2022).

As discussed in our response to Reviewer #1, DTA expression is restricted to BLBP-positive satellite glial cells and cannot be taken up by other cell types since this would require the DT receptor, which is not endogenously expressed in mice.

In response to Reviewer #1 above and in the revised manuscript, we also discuss that although we cannot exclude the involvement of astrocytes in the behavioral defects observed in BLBP:iDTA mice, BLBP is 45-fold enriched in satellite glia compared to astrocytes. Genetic ablation of astrocytes results in severe motor deficits in adult mice including limb paralysis, ataxia, and smaller body weights (Schreiner et. al, 2015), which are not present in BLBP:iDTA mice. Importantly, we provide new data to show that chemical ablation of sympathetic nerves using 6-OHDA, which does not cross the blood-brain barrier in adult mice, prevents the cardiac dysfunction in BLBP:iDTA mice, indicating a peripheral locus. Together, with the evidence that we have provided for sympathetic neuronal defects at the morphological and cellular levels in BLBP:iDTA mice, we conclude that behavioral defects arise primarily from dysfunction of peripheral sympathetic neurons.

“Additionally, I have some other concerns related to the data/data interpretation that should be clarified:

• In Figure 1C, the authors note that TUNEL-labeled cells have large ovoid nuclei and are likely neuronal. A double-label would demonstrate this claim with more certainty than cell shape.”

We have performed these additional experiments. We show that the majority of apoptotic cells at 5 days post-tamoxifen injections are satellite glial cells (Figure 1E, G, revised manuscript). Although, there was a trend toward enhanced neuronal apoptosis at this early stage, the number of apoptotic neurons in BLBP:iDTA ganglia was not statistically different from that in controls (Figure 1F, H, revised manuscript). We also did not observe a significant loss of neurons at 5 days post-tamoxifen injections (Figure 2-figure supplement 1B, revised manuscript). However, by 14 days post-tamoxifen injections, there is a significant loss (24% decrease) of sympathetic neurons (Figure 2G, revised manuscript). Together, these results suggest that sympathetic neuron loss occurs secondarily to the loss of satellite glial cells in BLBP:iDTA mice.

“Related to this experiment, the quantification in Figure 1D does not appear to match the image shown in Figure 1C. Many TUNEL(+) cells are shown in the Blbp:iDTA image compared to control outside of the ganglionic borders, but this was not mentioned in the manuscript.”

As discussed above in response to Reviewer #1, the quantifications in Figure 1D represents the total number of TUNEL-positive cells in the entire superior cervical ganglia (approximately 24-32 tissue sections of 12 m thickness each), while images in Figure 1C show a single tissue section from the ganglia.

The Reviewer also notes that we observe TUNEL-positive cells outside the ganglia. However, this is evident in both control and mutant ganglia. This may represent a normal turnover of cells in tissues outside sympathetic ganglia (fat deposits and arteries). In the revised manuscript, we provide new images that show TUNEL labeling outside both the control and mutant ganglia (Figures 1C and 4D, revised manuscript), and also clarify this point in the text (page 6, revised manuscript).

“• It is unclear from the Materials and Methods section if the mice are all on a congenic background. For example, how standard is pupil size from mouse to mouse, and is this more variable if mice are not congenic? This may be an issue given that the pupil measurements used as a read-out of sympathetic function have no baseline comparison, just control, and BLBP:iDTA animals.”

We compared pupil size in BLBP:iDTA mice and their litter-mate controls, which are of the same genetic background. Our values of basal pupil sizes in mice after dark adaptation are consistent with previously reported results (Keenan et. al., 2016). Pupil size tends to be similar in darkness across mice of different genetic backgrounds (Keenan et. al., 2016).

Reviewer #3 (Public Review):

“In this manuscript, Mapps et al. report on the very interesting finding that satellite glia deletion significantly impacts sympathetic neuron function and survival. .. This is a very novel finding that reveals an important role for satellite glia in sympathetic physiology. It is comprehensive and well controlled. There are just a few issues that the authors should consider.”

We thank the Reviewer for finding the study to be novel, comprehensive, and well-controlled.

“In Fig. 1C-D, how many dpi was the TUNEL assay performed? It would be helpful to know how quickly the neurons die after glial depletion and if the cell death continues or plateaus. The authors should also co-label using neuronal and glial markers to evaluate whether the apoptotic cells are primarily neurons or glia. They report a loss of neurons, but how much of that is reflected in the TUNEL labeling is not clear.”

Figures 1C-D represent the results of TUNEL labeling done at 5 days post-tamoxifen injections. As discussed above in responses to Reviewers #1 and 2, we include new data in the revised manuscript, using co-labeling with TUNEL and sympathetic neuron/satellite glia markers, to show early apoptosis of satellite glia, but not of neurons, at 5 days post-tamoxifen injections in BLBP;iDTA mice (Figures 1E-H, revised manuscript). We also did not observe a significant decrease in neuronal numbers at 5 days post-tamoxifen injections (Figure 2-figure supplement 1B, revised manuscript). However, by 14 days post-tamoxifen injections, there is a significant loss (24% decrease) of sympathetic neurons (Figure 2G, revised manuscript). These results indicate that satellite glia apoptosis occurs first, followed by the loss of sympathetic neurons in BLBP:iDTA mice. At the moment, we do not know if the neuronal death continues and/or reaches a plateau at later stages. This is a good point, which we will investigate in future analyses.

“In Figs. 1C and 5C TUNEK analysis, there are quite a few TUNEL+ puncta outside of the ganglia, suggesting that there may be apoptosis in other adjacent tissues when the glia removed or Kir4.1 is deleted. The authors should comment on that if it were something consistently observed.”

We observe TUNEL-positive cells immediately adjacent to the ganglia in both control and mutant mice (BLBP:iDTA or Kir4.1 cKO mice). This may represent a normal turnover of cells in tissues outside sympathetic ganglia (fat deposits and arteries). In the revised manuscript, we provide new images that show TUNEL labeling outside both the control and mutant ganglia (Figures 1C and 4D, revised manuscript), and also clarify this point in the text (page 6, revised manuscript).

“The loss of neurons upon glial cell loss or Kir4.1 deletion is interesting. The authors discuss how neuron death could occur, but did they observe TUNEL+ cells in regions where the glia had been deleted? Given that the diphtheria toxin did not ablate all glia, were the neurons left with little or no surrounding glia more likely to die? This may be difficult to tell, but from the images in 1E, it looks like some neurons lack nearby glia. This would be a potential explanation for why only a fraction of the neurons died; those neurons with associated glia may be more protected.”

The Reviewer makes an interesting point that the neurons without attached satellite glial cells are the most vulnerable to apoptosis. We were unable to conclusively make this correlation after looking through multiple images of TUNEL labeling in BLBP:iDTA ganglia. Interestingly, we found a similar (22% loss) of sympathetic neurons in Kir4.1 cKO mice in the absence of obvious disruptions in satellite glia association with sympathetic neurons (see Figure 4C and Figure 4-figure supplement 1C, revised manuscript). Thus, while the loss of neuron-satellite glia contacts may contribute to the neuronal death, there are also other mechanisms that could be involved in neuronal apoptosis.

“It would be helpful to clarify a bit more what the control mice used for comparison were. From the text, it seems as if they were the same mice but not treated with tamoxifen. Were they given diphtheria toxin?”

The Reviewer is correct that we used Fabp7-CreER2;ROSA26eGFP-DTA mice that were injected with either vehicle (corn oil) to serve as controls or injected with tamoxifen for satellite glia ablation. Mice did not have to be injected with diphtheria toxin, since tamoxifen injections would drive CRE-mediated DTA expression in BLBP-positive satellite glia.

“In addition, did the authors check for any effects of tamoxifen alone? Given that estrogen can affect many physiological parameters, including cardiac function, tamoxifen alone could have some effect, e.g., Kuo et al., PMID: 20392827.”

We thank the Reviewer for this point. We measured heart rate by electrocardiogram recordings in adult (P45 day old) wild-type C57Bl/6J mice or control (ROSA26eGFP-DTA) mice that did not express Cre that were either injected with corn oil or tamoxifen using the same paradigm as for BLBP:iDTA mice and litter-mate controls (sub-cutaneous injections, 180 mg/kg body weight for 5 consecutive days). We show that tamoxifen injection alone does not elicit any effects on heart rate in wild-type or control mice in the absence of Cre (Figure 3-figure supplement 1C-D, revised manuscript).

“Interestingly, TH levels in BLBP:iDTA mutant axons appeared to be similar to that in controls, despite the marked reduction in TH mRNA and protein levels in neuronal cell bodies (Figure S2A). The Kaplan lab (PMC7164330) showed that TH mRNA trafficking and local synthesis play an important role in synthesizing catecholamines in the axon and presynaptic terminal. Although a bit beyond the scope of this study, it would be interesting to determine whether TH mRNA transport is altered by deletion of the glia. The authors might check to see if TH transcripts are reduced in axons by something like RNAscope.”

We thank the Reviewer for this interesting point. The Reviewer likely meant that TH levels are up-regulated in axons since BLBP:iDTA mutant axons maintain TH expression despite the reduction of TH in neuronal soma. We tried assessing Th mRNA in axons in vivo using single molecule fluorescence in situ hybridization (smFISH). However, despite several attempts, we were not successful in getting the TH RNAscope probe to work. In the revised manuscript, we discuss enhanced Th mRNA trafficking and local translation as a possible mechanism for maintenance of axonal TH levels in BLBP:iDTA sympathetic neurons (Discussion, pages 19- 20, revised manuscript), and cite the Gervasi et. al., 2016 study.

Author Response

Reviewer #1 (Public Review):

In this paper, Jan Kubanek attempts to derive an 'effective decision strategy' that is optimal (and therefore normative) given certain constraints resulting from computational capacity limitations. The author first points out that neoclassical economics (i.e., expected utility theory, EUT) provides normative predictions for decisions to maximize utility. Next, he (correctly) points out that finding the optimal solutions to decision problems requires computational resources that are unlikely to exist in actually existing decision-makers (animals and humans). He claims that this fact is the most severe problem for concluding that EUT is an accurate description of actual human or animal decision processes. I disagree with him on this point as I will lay out in more detail below. Next, the author attempts to find an 'efficient' (i.e., computationally reasonable) decision strategy that comes close to the original normative framework. He claims that such a strategy is EDM, whereby decisions are made by allocating relative effort in proportion to the relative reward of each option.

Overall, I find this paper hard to judge. The considerations described in this paper are certainly interesting and I have no reason to presume that the mathematical derivations described are wrong (without having made an effort to follow and check it in detail). Still, I find the paper, in the end, sterile and I fear it will have only limited impact. I think the manuscript should be expanded in three different directions to make it more relevant for the neuroscientific understanding of decision making.

First, the author needs to show that EDM can also explain other known violations of EUT related to the axiom of regularity (i.e., preferences between two options should not be affected by the presence of inferior options). This seems relevant because these behavioral effects robustly violate the choice allocation strategy of EDM.

Second, EDM is so abstract that the actual structure and capacity of the nervous system are nearly irrelevant. The author should consider more deeply the computational requirements and capacities of different types of brains; fruit flies, frogs, and primates, and the consequences of these differences for what is (or should be) achievable in terms of optimal behavior.

Third, the paper contains no test for EDM. This is in part because EDM is at no point compared to the predictions of alternative theories.

I thank the Reviewer for these constructive comments, which are addressed below.

My specific concerns are as follows:

(1) The author claims that the most severe problem of EUT is that it is computationally implausible. However, I disagree.

It could be claimed that EUT describes an (unattainable) optimal state that actual brains try to accomplish with limited resources. (In essence, the current paper follows this strategy).

Correct, EDM stems from Expected Utility Theory subjected to specific biological considerations, as shown in Figure 1.

Given this origin, the paper now makes more appropriate statements regarding the biologically-relevant shortcomings of EUT:

i) Abstract: "the apparatus requires a large number of evaluations of the decision options as well as neural representations and computations that are not biologically plausible."—>"the apparatus requires a large number of evaluations of the decision options as well as neural representations and computations that are difficult to implement at the biological level" ii) Introduction: "To address these biologically implausible requirements, …" —> "To address the biological constraints, …").

I think the situation is much direr. During the last 70 years, a small army of psychologists and behavioral economists have described a large number of violations of EUT's normative predictions: the Allais paradox, framing effects, the behavioral tendencies summarized in Prospect theory, and others. These differences between behavior and normative predictions are important because they violate basic assumptions of the normative theory.

Prospect theory can be readily incorporated into EDM.

This has resulted in the following paragraph in the Discussion:

"Notably, the 𝑢𝑖 and 𝑒𝑖 variables can incorporate additional factors such as the probability of an outcome, as in prospect theory (Kahneman and Tversky, 1979). A previous study (Kubanek, 2017) demonstrates that prospect theory’s incorporation of probabilities into utilities does not change the relationship between the differential formulation of Equation 1 and the fractional formulation of Equation 2, which is crucial for EDM. Moreover, the 𝑢𝑖 and 𝑒𝑖 variables can be entirely subjective. So long as the representations are comparable by the brain (e.g., through relative firing rates; Figure 6), the 𝑒𝑖 = 𝑢𝑖 strategy provides an efficient allocation of the decision-maker’s resources."

(2) The most interesting case of such violations is a set of well-known behavioral effects that occur in the context of multi alternative-multi attribute decision making. They are known as the attraction, similarity, and compromise effects (there is a large literature; more recently: Dumbalska T, Li V, Tsetsos K, Summerfield C. A map of decoy influence in human multi alternative choice. Proc Natl Acad Sci U S A. 2020 Oct 6;117(40):25169-25178. doi: 10.1073/pnas.2005058117. Epub 2020 Sep 21.) These biases have received so much attention because they violate a very basic axiom of EUT. Choices between two options should not be affected by the presence of a third option that is inferior to both of them. However, that is exactly what happens in these choice biases. The effects have been shown in many species ranging from humans to amphibians to invertebrates. As far as I can see, EDM cannot explain how choice allocation between two options A and B that have equal value would be changed by the inclusion of a new option D so that is of lower value than A or B in such a way that D is not chosen at all, but A is chosen more often than B if D is similar in attributes to A (the 'attraction' effect). If I am mistaken, the inclusion of an explanation of how this would work would be of major importance.

The new Figure 6 provides a starting point for addressing these effects.

Specifically, this comment has resulted in the following Discussion paragraph:

"In EDM, the relativistic representation of utility at the neural level (black bars in Figure 6) involves divisive normalization. Divisive normalization a common operation performed by neural circuits (Carandini and Heeger, 2012). The specific form of this operation may be crucial for explaining attraction, similarity, and compromise effects observed in multi-alternative, multi-attribute decision environments (Noguchi and Stewart, 2014; Dumbalska et al., 2020). For instance, it has been found that a transformation of utilities by specific monotonic functions prior to divisive normalization can explain these behavioral effects parsimoniously (Dumbalska et al., 2020). On this front, monotonic transformations and divisive normalization are performed by several kinds of feedforward and feedback neural circuits (Lek et al., 1996; Carandini and Heeger, 2012). Nonetheless, how exactly individual attributes of decision options are encoded at the neural level should be investigated using large-scale neuronal recordings."

(3) EDM as described in this manuscript is completely static, that is it ignores actual computational processes that underlie decision making. This is in opposition to an important modern branch of decision research that has stressed the importance of understanding processes (and their limitations) to understand how choices are made. Examples are: (1) Roe RM, Busemeyer JR, Townsend JT. Multialternative decision field theory: a dynamic connectionist model of decision making. Psychol Rev. 2001 Apr;108(2):370-92. doi: 10.1037/0033-295x.108.2.370. PMID: 11381834.; (2) Tsetsos K, Usher M, Chater N. Preference reversal in multiattribute choice. Psychol Rev. 2010 Oct;117(4):1275-93. doi: 10.1037/a0020580. PMID: 21038979. The relationship between EDM and algorithmic implementations should be explored.

This point has been addressed in the following ways:

1) EDM is now implemented at the algorithmic level while positioned within stochastic choice environments.

2) The performance of EDM in the stochastic environments is reported in a new Figure 4.

3) The performance of EDM within the stochastic and deterministic environments is now compared in a new Figure 5. The figure shows that both environments support the same principal conclusions.

4) Figure 4b provides mechanistic examples of the individual effort allocations by EDM and alternative strategies.

5) The Discussion includes a new paragraph that places EDM within a broader context of algorithmic implementations:

"In deterministic environments, EDM comprises a single stage that embodies Equation 7. This rule is analogous to the evolutionarily stable “relative reward sum” in ecology (Harley, 1981; Hamblin and Giraldeau, 2009) and “local fractional income” in neuroscience (Sugrue et al., 2004). In dynamic and stochastic environments, the strategy should additionally incorporate an integration stage that mitigates the effect noise and thus provides meaningful estimates of the worth of each option. Several approaches can be used to keep track of dynamic, stochastic environments and thus estimate their relative worth 𝑢𝑖. The most compact are related to reinforcement learning, in which previous payoffs are discounted exponentially using a “learning rate.” This approach has been applied in ecology (Harley, 1981; Hamblin and Giraldeau, 2009), computer science (Sutton and Barto, 1998), neuroscience (Sugrue et al., 2004; Corrado et al., 2005), and was also applied here when assessing performance in stochastic environments. One benefit of this free parameter is that decision-makers can adapt the learning rate to the speed of change or the level of stochasticity of specific decision situations (Iigaya et al., 2019)."

(4) Most importantly, what is missing is a clear prediction for a finding (behavioral or neuronal) that would only be predicted, but not by any other theory of decision making. Without such a proposed test, the idea has no scientific merit.

The paper includes new analyses and text that provide predictions that are specific to EDM. Specifically, this point has been addressed in three ways:

1) The three predictions that are specific to EDM are now made explicit in a new Figure 5. The figure also provides quantitative support of EDM through performance evaluations across these predictions.

2) The Results include the following text regarding the key defining properties of EDM: "Figure 5 summarizes and expands on the defining properties of EDM. First, the main finding of this article is that EDM is characterized by high performance following a single evaluation of decision options (Figure 5a). Second, Figure 3a suggested that the proportional allocation of effort to relative utilities (𝛽 → 1) may represent an optimum, at least across the space of effort-utility contingencies tested. Figure 5b-top additionally evaluates the impact of this exponent in the stochastic choice situations. This figure replicates the findings of Figure 3a in that 𝛽 = 1 lies near the optimum, with 𝛽 = 1.0 and 𝛽 = 1.2 providing an average gain of 94.0% and 94.1%, respectively. Thus, the proportional allocation of effort to relative utilities is another defining trait of EDM, and this strategy provides near-optimal performance in all decision situations tested. And third, the effort allocation strategy in EDM, 𝑒harvest = 𝑢(𝑒eval), is invoked once regardless of the number of decision options. This is in contrast to optimization, whose convergence time scales with problem dimensionality, i.e., the number of options. The single-evaluation EDM strategy maintains performance across the number of options under the VI schedules (Figure 5c-top; slope 0.67% per option, 𝐹 = 4.46, 𝑝 = 0.073), although it does incur a performance loss (Figure 5c-bottom; slope -0.95% per option, 𝐹 = 34.66, 𝑝 = 0.00061) in the deterministic cases. Notably, to attain the performance of EDM, the theoretical maximizing agents required substantially more evaluations in situations involving a large number of options (Figure 5c gray; top: slope 2.8 evaluations per option, 𝐹 = 21.80, 𝑝 = 0.0023; bottom: slope 3.4 evaluations per option, 𝐹 = 250.2, 𝑝 = 9.7 × 10−7)."

3) The Discussion now includes a dedicated paragraph on the testability of the EDM predictions at the behavioral and neural levels:

"EDM is testable at the behavioral (Figure 5) and neural (Figure 6) levels. At the behavioral level, EDM possesses three distinctive characteristics. First, EDM obtains high reward rapidly (Figure 5a). This characteristic can be tested in choice environments that minimize noise as an additional factor (e.g., Figure 7a), providing performance versus evaluations plots analogous to Figure 2. Second, EDM allocates relative effort to relative utilities proportionally (Figure 5b). This characteristic can be tested in situations in which utilities can be measured precisely, e.g., through the volume of fluid rewards in animal experiments or money in human experiments. And third, EDM allocates effort rapidly regardless of the number of options. This is because the 𝑒harvest = 𝑢 (𝑒eval) strategy is agnostic to the number of options. This characteristic can be tested by varying the number of decision options and quantifying the number of times a decision-maker evaluates the options. At the neural level, EDM only requires the encoding of relative utilities of the recently sampled options. This relative code can be implemented using firing rates of the neuronal pools representing each alternative (Figure 6 top row, middle column). Indeed, this representation has been found in the primate brain. Specifically, the relative value associated with EDM, termed “fractional income,” captures firing rates of neurons in monkey area LIP (Sugrue et al., 2004)."

Reviewer #2 (Public Review):

In this article, Kubanek shows how simple, local decision strategies approximate optimal foraging behavior using analytical methods and model simulations. To ground the argument beyond model simulations, Kubanek generalizes previous theoretical frameworks in economics and foraging to show how evaluating relative utility and effort are sufficient to find optimal behavior. A particular strength of this study is its principled approach to linking general economic theory with foraging theory and deriving the conditions under which local behavioral strategies provide general and efficient means to the optimality problem. Re-casting utility and effort in relative terms offers attractive possibilities to apply these formulations in describing a range of phenomena. I, therefore, believe this short report will be of interest to a multidisciplinary audience from economics, psychology behavior theory, foraging, and neuroscience. The author's main claims are supported by their evidence.

Potential weaknesses of the study include:

1) Predictions from the proposed EDM framework are stated in vague terms and could be formulated more concretely and, if possible, included in the model simulations.

The predictions are now stated explicitly in a new Figure 5 and the associated text, and supported through performance evaluations within deterministic and stochastic choice environments.

Moreover, a new Figure 6 provides a representational and computational account of EDM, and summarizes the main point of the paper that EDM combines high performance with simple, biologically plausible evaluation.

2) The specificity of the EDM model and related model is only briefly touched on. The EDM argument could be strengthened by making the relation to other behavioral models more explicit.

The new Figure 5 now compares the key characteristics of EDM with a set of related and more complex models, and evaluates their performance across these characteristics. The relations to other behavioral models are further specified in two new Discussion paragraphs.

3) Many behavioral situations, including the in this paper often-cited study by Sugrue et al (2004), involve reward contingencies with a high level of uncertainty and non-stationary environments. While the author mentions these situations at the end of the discussion, it remains vague how EDM precisely performs or relates to decision strategies that deal with such environments.

The article now includes also stochastic choice environments, in addition to the original deterministic choice environments. This has resulted in new Figure 4, Figure 5, and the associated text.

The results in the stochastic environment corroborate those obtained in the deterministic environments.

Author Response

Reviewer #1 (Public Review):

Neural stem cells express cascades of transcription factors that are important for generating the diversity of neurons in the brain of flies and mammals. In flies, nothing is known about whether the transcription factor cascades are build from direct gene regulation, e.g. factor A binding to enhancers in gene B to activate its expression. Here, Xin and Ray show that one temporal factor, Slp1/2, is regulated transcriptionally via two molecularly defined enhancers that directly bind two other transcription factors in the cascade as well as integrating Notch signaling. This is a major step forward for the field, and provides a model for subsequent studies on other temporal transcription factor cascades.

Thanks for the positive comments!

Reviewer #2 (Public Review):

The manuscript addresses an important question concerning the mechanisms regulating temporal transitions in Drosophila neural progenitors called neuroblasts. Here, they concentrate on a specific transition between the transcription factors Ey and Slp1/2 that are sequentially expressed within a cascade involving at least 6 temporal transcription factors. Using a combination of new transgenes, bioinformatics and genome-wide profiling of transcription factor biding sites (Dam-ID), they functionally characterize two enhancers of the Slp1/2 genes that are active during this transition. This led to the identification of the Notch pathway as an important facilitator of the transition. They also show that Notch signaling requires cell cycle progression and that Slp1/2 is a direct target of Ey, validating the importance of transcriptional cross-regulatory interactions among the temporal transcription factors to trigger progression.

In my opinion, the study is very interesting, representing the first careful analysis of enhancers involved in temporal transitions in neural progenitors, and leading to new insights into the mechanisms promoting temporal progression.

Thanks for the positive comments!

Reviewer #3 (Public Review):

In this manuscript, the authors present data to suggest that transcriptional activation of the Slp1/2 temporal factors in the medulla neuroblasts of the developing Drosophila optic lobe is dependent on two enhancer elements. The authors concluded that these two enhancers were able to be activated by Ey and Scro, two other factors identified to be involved in the temporal cascade of the medulla NB. The authors show that cell cycle progression is necessary for Notch signaling, and that Notch signaling activates and sustains the temporal transcription factor cascade. The authors use GFP reporter assays to correlate the enhancer activity to Slp1/2 expression and used DamID to show in-vivo binding of Su(H) and Ey to the enhancer fragments.

I agree with the authors that it is important to define the mechanisms by which Notch, cell cycle control and these temporal transcription factors function through their cis-regulatory elements to establish this self-propagating cascade to generate diverse cell types during neurogenesis. However, the findings in this study offer limited new insights toward reaching this goal for a myriad of reasons. First, studies in invertebrate and vertebrate neurogenesis have agreed on the conceptual framework that transcriptional control plays a key role in regulating the generation of diverse cell types. The data showing the patterns of slp1/2 transcript simply reaffirm the proposed model as well as recently published single-cell transcriptomic analyses of fly optic lobe neuroblasts. Second, it remains unclear how physiologically relevant the enhancer analyses presented in this study are to the regulation of Slp1/2 expression, as the data can only suggest that they act redundantly to each other. It is also troubling to see that mutating binding sites of a single transcription factor appears to completely abolish enhancer activity while Slp1/2 protein expression is delayed in mutant clonal analyses. Third, the authors do not offer any explanation for how Notch signaling contributing to the timing of Slp1/2 expression, considering that Notch signaling should be active during the entire life of the neuroblast based on canonical Notch target gene expression. What action do Ey and Scro play in this timely enhancer activation as both appear to be necessary to activate the enhancers along with Notch. Fourth, many studies including the Okamoto et al., 2016 study cited in this study have contributed to our appreciation of the role of proper cell cycle control in promoting generation of diverse neurons in vertebrate neurogenesis. It is unclear to me if findings from the current study contribute to significant advancement on this regulatory link.

Thanks for raising these concerns. Here are our responses:

First, we agree that there have been great advances in this field including classical studies in the ventral nerve cord, recent studies on type II lineages and medulla including our own scRNA-seq study of medulla neuroblasts. These studies have revealed the sequential expression of transcription factors in neuroblasts of different ages, and proposed that these transcription factors form a transcriptional cascade based on the cross-regulations among them. However, these cross-regulations were based on mutant phenotypes, and in most cases, the cis-regulatory elements of these TTFs have not been characterized, and it hasn’t been studied whether these cross-regulations are direct or not. Little is known about exactly how the timing of the transition is regulated and coordinated with cell-cycle control. We have addressed these questions and identified two enhancer elements for slp1/2, and demonstrated that the previous TTF Ey, another TTF Scro, and Notch signaling directly regulate slp expression. Further we demonstrated that Notch signaling is dependent on cell cycle progression in neuroblasts, and supplying Notch signaling rescues the delay in Slp expression in cell cycle mutants. We believe this study has provided important insights in this field and is another step forward.

Second, now we provide evidence that deletion of both enhancers specifically abolished Slp1 and Slp2 expression in medulla neuroblasts.

Regarding the concerns about binding site mutation:

1) Ey: With loss of Ey, Slp is completely lost. The Ey binding site mutation phenotype is consistent with loss of Ey phenotype.

2) Su(H): For the u8772 250bp enhancer, mutating all four predicted Su(H) binding sites did abolish the reporter expression. During the revision, we generated another construct, in which we mutated the two predicted Su(H) binding sites which are perfect matches to the consensus, and found that this dramatically reduced the reporter expression. For the d5778 850bp enhancer, mutation of Su(H) binding sites caused strong glial expression which prevented us to precisely assess the neuroblast expression. Thanks to the excellent advice from review #3, we used repo-Gal4 and GFP-RNAi to remove the glial expression. This approach turned out very informative. We found that mutation of four or six out of six predicted Su(H) binding sites actually did not decrease the reporter expression in neuroblasts, suggesting that Notch signaling does not active the d5778 850bp enhancer through these binding sites. However, we think this is the explanation why this enhancer drives a delayed expression comparing to the 220bp enhancer and the endogenous Slp. In addition, this also explains why with loss of Notch signaling, endogenous Slp expression is only delayed but not completely lost. This is because although the 220bp enhancer driven expression is completely lost, the d5778 850 bp enhancer still directs a delayed expression of Slp and this expression is not dependent on Notch signaling.

3) Scro: Mutation of Scro binding sites caused a decreased expression level of the reporter, consistent with the scro RNAi phenotype on Slp, which is a decreased expression level.

Third, regarding how Notch signaling which is active in the entire neuroblast life, can act to activate Slp expression in a specific time We tested genetic interactions between Ey, Scro, and Notch in the regulation of Slp expression. We found that with loss of Ey, supplying constitutive active Notch or Scro is not sufficient to rescue Slp expression. Thus Ey as the previous TTF, may be required to prime the slp locus, so that Notch signaling and Scro can act to further activate Slp expression. Therefore, Notch signaling requires Ey to specifically further activate Slp at the correct time. We have added these experimental results and discussion.

Fourth, the Okamoto et al., 2016 study actually concluded that cell cycle progression is not required for the temporal progression. In their experimental setup, they supply Notch to maintain the un-differentiated status of cortical neural progenitors when they block cell cycle progression. The observed that temporal transition still happened, and they concluded that cell cycle progression is not required for temporal transitions. However, they didn’t consider the possibility that Notch signaling, which is itself dependent on cell cycle progression, actually rescued the possible phenotype caused by arrest of cell cycle progression. Our result demonstrated that in Drosophila medulla, supplying Notch signaling can rescue the delay in the transition to the Slp stage in cell-cycle arrested neuroblasts, and further showed that the mechanism is by direct transcriptional regulation. We believe that publication of our results will be informative to the vertebrate study, promoting vertebrate researchers to re-consider the role of cell cycle progression and Notch signaling in temporal progression.

Author Response

Reviewer #1 (Public Review):

Edmondson et al. develop an efficient coding approach to study resource allocation in resource constrained sensory systems, with a particular focus on somatosensory representations. Their approach is based on a simple, yet novel insight. Namely - to achieve output decorrelation when encoding stimuli from regions with different input statistics, neurons in the sensory bottleneck should be allocated to these regions according to jointly sorted eigenvalues of the input covariance matrix. The authors demonstrate that, even in a simple scenario, this allocation scheme leads to a complex, non-monotonic relationship between the number of neurons representing each region, receptor density and input statistics. To demonstrate the utility of their approach, the authors generate predictions about cortical representations in the star-nosed mole, and observe a close match between theory and data.

Strengths:

These results are certainly interesting and address an issue which to my knowledge has not been studied in-depth before. Touch is a sensory modality rarely mentioned in theoretical studies of sensory coding, and this work contributes to this direction of research.

A clear strength of the paper is that it demonstrates the existence of non-trivial dependence between resource allocation, bottleneck size and input statistics. Discussion of this relationship highlights the importance of nuance and subtlety in theoretical predictions in neuroscience.

The proposed theory can be applied to interpret experimental observations - as demonstrated with the example of the star-nosed mole. The prediction of cortical resource allocation is a close match to experimental data.

We thank the reviewer for the feedback. Indeed, demonstrating an ‘interesting’ effect in even such a simple model was one of the main aims.

Weaknesses:

The central weakness of this work are the strong assumptions which are not clearly stated. In result, the consequences of these assumptions are not discussed in sufficient depth which may limit the generality of the proposed approach. In particular:

1) The paper focuses on a setting with vanishing input noise, where the efficient coding strategy is toreduce the redundancy of the output (for example through decorrelation). This is fine, however, it is not a general efficient coding solution as indicated in the introduction - it is a specific scenario with concrete assumptions, which should be clearly discussed from the beginning.

2) The model assumes that the goal of the system is to generate outputs, whose covariance structure isan identity matrix (Eq. 1). This corresponds to three assumptions: a) variances of output neurons are equalized, b) the total amount of output variance is equal to M (i.e. the number of of output neurons), c) the activity of output neurons is decorrelated. The paper focuses only on the assumption c), and does not discuss consequences or biological plausibility of assumptions a) and b).

We have clarified the assumptions in the revised version. The original version did not distinguish clearly between assumptions that were necessary to allow study of the main effect, and assumptions that were included to present a full model but that could have been chosen otherwise without affecting the results.

This has now been made much clearer. Regarding the noise issue (point 1), we have clarified the main strategy pursued by the model namely decorrelation, we acknowledge other possible strategies, and we make clear whether and how noise could be incorporated into the model. Regarding the biological plausibility of our assumptions (point 2),

Reviewer #2 (Public Review):

The authors propose a new way of looking at the amount of cortical resources (neurons, synapses, and surface area) allocated to process information coming from multiple sensory areas. This is the first theoretical treatment of attempting to answer this question with the framework of efficient coding that states that information should be preserved as much as possible throughout the early sensory stages. This is especially important when there is an explicit bottleneck such that some information has to be discarded. In this current paper, the bottleneck is quantified as the number of dimensions in a continuous space. Using only the second-order statistics of the stimulus, and assuming only the second-order statistics carrying information, the authors use variance instead of Shannon's information. The result is a non-trivial analysis of ordering in the eigenvalues of the corresponding representations. Using clever mathematical approximations, the authors arrive at an analytical expression -- advantageous since numerical evaluation of this problem is tricky due to the long thin tails of the eigenvalues of the chosen covariance function (common in decaying translation-invariant covariances). By changing the relative stimulus power (activity ratio), receptor density (effectively the width of the covariance function), and the truncation of dimensions (bottleneck width), they show that the cortical allocation ratio, surprisingly, is a non-trivial function of such variables. There are a number of weaknesses in this approach, however, it produced valuable insights that have a potential to start a new field of studying such resource allocation problems all across different sensory systems in different animals.

Strengths

• A new application of the efficient coding framework to a neural resource allocation problem given acommon bottleneck for multiple independent input regions. It's an innovation (initial results presented at NeurIPS 2019) that brings normative theory with qualitative predictions that may shed new light to seemingly disproportionate cortical allocations. This problem did not have a normative treatment prior to this paper.

• New insights into allocation of encoding resources as a function of bottleneck, stimulus distribution, andreceptor density. The cortical allocation ratios have nontrivial relations that were not shown before.

• An analytical method for approximating ordered eigenvalues for a specific stimulus distribution.

Weaknesses

The analysis is limited to noiseless systems. This may be a good approximation in the high signal-to-noise ratio regime. However, since the analysis of allocation ratio is very sensitive to the tail of eigenvalue distribution (and their relative rank order), not all conclusions from the current analysis may be robust. Supplemental figure S5 perhaps paints a better picture since it defines the bottleneck as a function of total variance explained instead of number of dimensions. The non-monotonic nonlinear effects are indeed mostly in the last 10% or so of the total variance.

We agree that the model is most likely to apply in the low-noise regime, as stated in the Discussion. The robustness of the results is indeed a worry, and indeed we have encountered some difficulties when calculating model results numerically due to the issue pointed out by the reviewer, and this led us to focus on an analytical approach in the first case. However, to test model robustness we have now included numerical results for several other covariance functions to demonstrate that, at least qualitatively, the results presented in the paper are not simply a consequence of the particular correlation structure we investigated.

In case where the stimulus distribution is Guassian, the proposed covariance implies that the stimulus distribution is limited to spatial Gaussian processes with Ornstein-Uhlenbeck prior with two parameters: (inverse) length-scale and variance. While this special case allowed the authors to approach the problem analytically, it is not a widely used natural stimuli distribution as far as I know. This assumed covariance in the stimulus space is quite rough, i.e., each realization of the stimulus is spatially continuous isn't differentiable. In terms of texture, this corresponds to rough surfaces. Of course, if the stimulus distribution is not Gaussian, this may not be the case. However, the authors only described the distribution in terms of the covariance function, and lacks additional detail to fill in this gap.

We would argue that somewhat ‘rough’ covariance structure might be relatively common, for example in vision objects have clear borders leading to a power law relation and similarly in touch objects are either in contact with the skin or they are not. In either case, we have now extended the analysis to test several other covariance functions numerically. We found that, qualitatively, the main effects described in the paper were still present, though they could differ quantitatively. Interestingly, the convergence limit appeared to depend on the roughness/smoothness of the covariance function, indicating that this might be an important factor.

The neural response model is unrealistic: Neuronal responses are assumed to be continuous with arbitrary variance. Since the signal is carried by the variance in this manuscript, the resource allocation counts the linear dimensions that this arbitrary variance can be encoded in. Suppose there are 100 neurons that encode a single external variable, for example, a uniform pressure plate stimulus that matches the full range of each sensory receptor. For this stimulus statistics, the variance of all neurons can be combined to a single cortical neuron with 100 times the variance of a single receptor neuron. In this contrived example, the problem is that the cortical neuron can't physiologically have 100 times the variance of the sensory neuron. This study is lacking power constraint that most efficient coding frameworks have (e.g. Atick & Redlich 1990).

We agree that the response model, as presented, is very simplistic. However, the model can easily be extended to include a variety of constraints, including power constraints, without affecting the results at all. Unfortunately, we did not make this clear enough in the original version. The underlying reason is that decorrelation does not uniquely specify a linear transform and the remaining degrees of freedom can be used to enforce other constraints. As the allocation depends only on the decorrelation process (via PCA), we do not explicitly calculate receptive fields in the paper and any additional constraints (power, sparsity) would affect the receptive fields only and so were left out in the original specification. We have now added clearer pointers for how these could be included and why their inclusion would not affect the present results.

The star-nosed mole shows that the usage statistics (translated to activity ratio) better explains the cortical allocation than the receptor density. However, the evidence presented for the full model being better than either factor is weak.

We agree that the results do not present definitive evidence that the model directly accounts for cortical allocations and as we state in the paper, much stronger tests would be needed. Our idea here was to test whether, in principle, the model predictions are compatible with empirical evidence and therefore whether such models could become plausible candidates for explaining neural resource allocation problems. This seems to be the case, even though the evidence in favour of the ‘full model’ versus the ‘activity only’ model is indeed not overwhelming (though this might be expected as the regional differences in activity levels are much greater than those in density). We have now added additional tests to show that the results are not trivial. We would also like to note that it is not obvious that the ‘full’ model would perform better than the ‘activity only’ model: for either we choose the best-fitting bottleneck width (as the true bottleneck width is unknown), and therefore the degrees of freedom are equal (with both activity levels and densities fixed by empirical data).

Reviewer #3 (Public Review):

This work follows on a large body of work on efficient coding in sensory processing, but adds a novel angle: How do non-uniform receptor densities and non-uniform stimulus statistics affect the optimal sensory representation?

The authors start with the motivating example of fingers and tactile receptors, which is well chosen, as it is not overstudied in the efficient coding literature. However, the connection between their model and the example seems to break down after a few lines when the authors state that they treat individual regions as independent, and set the covariance terms to zero. For finger, e.g. that would seem highly implausible, because we typically grasp objects with more than one finger, so that they will be frequently coactivated.

Our aim was to take a first stab at a model that could theoretically account for neural resource allocation under changes in receptor density and activity levels, and by necessity this initial model is rather simple. Choosing a monotonically decreasing covariance function along with some other simplifications allowed us to quantify the most basic effects, and do so analytically. Any future work should take more complex scenarios into account. Regarding the sense of touch, we agree that the correlational structure of the receptor inputs will be more complex than assumed here, however, whether and how this would affect the results is less clear: Across all tactile experiences (not just grasps, but also single finger activities like typing), cross-finger correlations might not be large compared to intra-finger ones. Unfortunately, there is currently relatively little empirical data on this. That said, we agree with the broader point that complex correlational structure can be found in sensory systems and would need to be taken into account when efficiently representing this information.

The bottleneck model posited by the authors requires global connectivity as they implement the bottleneck simply by limiting the number of eigenvectors that are used. Thus, in their model, every receptor potentially needs to be connected with every bottleneck neuron. One could also imagine more localized connectivity schemes that would seem more physiologically plausible given the observed connectivity patterns between receptors and relay neurons (e.g. in LGN in the visual system). It would be very interesting to know how this affects the predictions of the theory.

We agree that the model in its current form is not biologically plausible. While individual receptive fields can be extremely localised, the initial allocation of neurons to regions we describe in the paper relies on a global PCA, and it is not clear how this might be arrived at in practice under biological constraints. However, our aim here was to specify a normative model that generates the optimal allocation and thereby answer what the brain should be doing under ideal circumstances. Future work should definitely ask whether and how these allocations might be worked out in practice and how biological constraints would affect the solutions.

The representation of the results in the figures is very dense and due to the complex interplay between various factors not easy to digest. This paper would benefit tremendously from an interactive component, where parameters of the model can be changed, and the resulting surfaces and curves are updated.

We have aimed to make the figures as clear as possible, but do appreciate that the results are relatively complex as they depend on multiple parameters. The code for re-creating the figures is available on Github (https://github.com/lauraredmondson/expansion_contraction_sensory_bottlenecks), making it easy to explore scenarios not described in the paper.

For parts of the manuscript, not all conclusions made by the authors seem to follow directly from the figures: For example, the authors interpret Fig. 3 as showing that activation ratio determines more strongly whether a sensory representation expands or contracts than density ratio. This is true for small bottlenecks, but for relatively generous ones it seems the other way around. The interpretation by the authors, however, fits better the next paragraph, where they argue that the sensory resources should be relatively constant across the lifespan of an animal, and only stimulus statistics adapt. However, there are notable exceptions - for example, in a drastic example zebrafish change their sensory layout of the retina completely between larvae and adult.

We have amended the text for this section in the paper to more closely reflect the conclusions that can be drawn from the figure. These are summarised below.

The purpose of Fig. 3B is to show that knowledge of the activation ratio provides more information about the possible regime of the bottleneck allocations. We cannot tell the magnitude of the expansion or contraction from this information alone, or where in the bottleneck the expansion or contraction would occur. Typically, when we know the activation ratio only, we can tell whether regions will be expanded or contracted or whether both occur over all bottleneck sizes. For a given activation ratio (for example, a = 1:2, as shown in the 3B), we know that the lower activation region can be either contracted only or both expanded and contracted over the course of the bottleneck. In this case, regardless of the density ratio, the lower activation region cannot be contracted only. Conversely, for any density ratio (see dashed horizontal line in Fig. 3B), allocations can be in any regime.

In the final part of the manuscript, the authors apply their framework to the star nosed mole model system, which has some interesting properties; in particular, relevant parameters seem to be known. Fitting to their interpretation of the modeling outcomes, they conclude that a model that only captures stimulus statistics suffices to model the observed cortical allocations. However, additional work is necessary to make this point convincingly.

We have now included a further supplementary figure panel providing more details on the fitting procedure and results for each model. Given that we fit over a wide range of bottleneck sizes, where allocations for each ray can vary widely (see Figure 6, supplement 1A), we tested an additional model to confirm that the model requires accurate empirical density and/or activation values for each ray to provide a good fit to cortical data. Here we randomise the values for the density and activation of each ray within the possible range of values for each. We find that with this randomisation of the values the model performs poorly on fitting even with a range of bottleneck sizes. This suggests that the model can only be fitted to the empirical cortical data when using the empirically measured values.

Author Response

Reviewer #1 (Public Review):

This manuscript reports a new analytical method (rhapsodi) to impute genotypes on human gamete data. The authors characterize the specificity and sensitivity of the approach and benchmark it against the current tool to analyze gamete data. rhapsodi is more efficient and versatile than the current approach, and thus represents an important technical feat. The last analysis of the manuscript is a reanalysis of the SpermSeq dataset, a massive sequencing effort to characterize recombination in human sperm haplotype data. rhapsodi fails to find any deviations from random segregation and challenges the notion that there are distorters in the human genome. In general, the manuscript represents an important technical piece but the results could be better contextualized to provide a perspective of what are the implications of the findings for our understanding of human recombination and segregation distortion.

Thank you for appreciating the technical importance of our work for improving the analysis of transmission distortion (TD) based on low-coverage single-cell sequencing data from gametes. We agree that the results (in regard to the method performance, statistical power, and implications for human TD) should be better contextualized, which we address in a point-by-point manner below.

Reviewer #2 (Public Review):

This paper describes a new and powerful method of inferring gametic haplotypes using low-coverage sperm sequencing data, rhapsodi. It is a highly useful tool, and the authors demonstrate its robustness using simulations and comparisons to the current gold standard, Hapi. The authors also use the results of rhapsodi on a sample of low-coverage human sperm sequencing data to assess the evidence for moderate transmission distortion (TD), a pattern that previous studies using pedigrees have sought to identify without replicable success. The work's main strength lies in the method the authors have developed and their clear and thorough description and validation of its use. The rhapsodi method clearly performs substantially better than Hapi in several relevant use cases, and in some instances it is usable when Hapi would fail to run or require unreasonable resources. This study, then, provides a highly useful tool to researchers wishing to phase donor haplotypes, infer gamete genotypes, and estimate rough locations of recombination breakpoints using Sperm-seq data.

Thank you for engaging with our method and for noting its use cases and performance.

A major limitation is the lack of consideration of strong TD. Under this scenario, there may be "allelic dropout" in the low-coverage Sperm-seq data; without information on the parental genotype from somatic cells, over-transmission of one allele would appear to be absence of the alternate allele (i.e., the donor would be erroneously inferred to be homozygous). Some known examples of TD in other species are extremely strong; e.g., the SD locus in Drosophila can cause distortion as strong as k=0.99. Such cases seem highly likely to be missed using Sperm-seq + rhapsodi, and a lack of power to detect them would influence both ability to observe individual cases of TD as well as the authors' test for a global signal of biased transmission. Since the provided simulations only include scenarios up to 70% transmission of one allele, the paper does not address this potential limitation.

The authors claim that their work conclusively excludes the presence of ongoing TD in their sample of human males, which, if they are from the same populations as former studies, may provide additional evidence against ongoing TD in these human populations. However, whereas earlier studies were only highly powered for extremely strong TD, the current method appears to be highest powered for intermediate levels of TD, strong enough to generate differences from binomial expectations, but not so strong that one allele might be missing in the low coverage pool of sperm serving as input to rhapsodi. This claim, then, may be better framed as a lack of evidence for TD of intermediate strength in current samples, rather than the strict adherence to Mendelian transmission indicated in the title.

This is an interesting and important point, and we agree that extreme TD would produce apparent tracts of homozygosity across the sample of sperm genomes. Without external knowledge of heterozygous sites in the donor genome, such SNPs would be unobserved within the sperm sequencing data. To address this possibility, we performed additional simulations of very strong TD (transmission rate, k = 0.99; Figure 4-figure supplement 3; lines 416-434; lines 1062-1083). These simulations demonstrate that despite the homozygosity of the causal SNP, recombination in flanking regions recovers heterozygosity but still manifests extreme and detectable TD. Specifically, across 2,200 simulations (100 independent simulations x 22 chromosomes; k = 0.99) with parameters matching a typical Sperm-seq donor, we identified the TD signature in all 2,200 cases (Power = 1) despite homozygosity (and thus filtering) of the causal SNP in 89% of cases (1958 / 2200). This high power also holds for donor samples with higher (Power = 1) and lower (Power = 1) coverages, respectively.

In summary, even though it is the case that the causal SNP and nearby flanking SNPs “drop out” of the data, recombination occurs as one extends out from these regions in both directions, and very strong signals (well beyond genome-wide significance thresholds) are detectable within these heterozygous regions. While we cannot attribute the signal to the true causal SNP, this limitation is not unique to our study, but is a general limitation of any study design (including pedigree and pooled sequencing studies) that must contend with linkage disequilibrium.

Nevertheless, as highlighted by Reviewer 3, the use of the term “strict” in the title may be too subjective. TD of 5% or less could be considered strong from a population genetic perspective, but undetectable based on binomial variance and our stringent multiple testing corrections. We have therefore removed the word “strict” from the title and moderated the adjectives we use when describing the strength of detectable TD throughout the paper. We also enumerate various forms of TD that would be undetectable based on our study design in the Discussion (lines 581-586; lines 603-638).

Reviewer #3 (Public Review):

The authors reanalyze an existing dataset of single-cell Sperm-seq data to search for signals of transmission distortion. They develop an improved genotype imputation method and use this approach to phase donors and characterize the landscape of ancestry across each sperm genome. Using these data, the authors determined that there are no regions in any of the male donors' genomes that display a significant excess of TD. The main biological claim of the paper is that there is a strict adherence to Mendelian transmission ratios in human males.

The computational approaches for accurately phasing and reconstructing haplotypes in individually lightly sequenced gametes is a potentially useful advance that I expect may be valuable for geneticists analyzing similar datasets. The quality of software documentation and usability is high. I have concerns about the appropriateness of the comparisons selected for this approach and the algorithm does not appear particularly novel.

I have no doubt about the authors' basic conclusion that there are no strong male TD loci in the male donors examined. However, I find their statements about "strict adherence to Mendelian ratios" and many references to strong statistical power to be oversold. The power of this study is still quite limited relative to the strength of TD that we would expect to find in human populations.

Thank you for your comments and for engaging with our manuscript so closely. We agree that additional discussion of statistical power, the strength of TD that can be detected, and the uses of our software are necessary, and these changes have substantially strengthened our revised manuscript.

Major Concerns:

There are really two distinct papers here. One is about improved imputation and crossover analysis from sperm-seq data and one is about TD. The bulk of the methodological development is a rework of the approach for genotype imputation and haplotype phasing in Sperm-seq. Yet, the major conclusions are focused on a scan for TD. I am left wondering if analyzing these data using the original method in the Bell et al paper would have produced different conclusions about either? If not, is there a systematic bias such that one would find an excess of false detections of TD? Phasing slightly more markers is not a particularly compelling link between these sections because even fairly sparsely distributed markers that are correctly phased would certainly be fine in a scan for TD within a single individual due to linkage. If this cannot be shown I wonder if this work would be better split into two manuscripts with one more technical paper describing the differences in recombination maps associated with rhapsodi and the other as a brief report stating that strong TD is probably uncommon in human males.

While we agree that there are two important aspects of our study, we feel that the combination of a generalizable method as well as an application to test an important biological hypothesis is a strength of our work.

For additional context, Dr. Bell is a co-author on our study and collaborated with us in part based on the motivation to build a reproducible software toolkit for similar analyses. Bell et al. (2020) did not implement their method as generalizable software, but rather as a set of analysis scripts tested only with their data and computing environment. Unlike our method (rhapsodi) and the comparison approach (Hapi), those scripts were not written as user-friendly software and are therefore less likely to be used by the research community.

It is not surprising that rhapsodi outperforms Hapi since Hapi was designed for a very different quantity of samples and sequencing depths. I appreciate the authors' point that Hapi performed better than other methods in comparisons run by the Hapi authors. However, they were looking at very few gametes (10 or so, I believe). For that reason, this comparison is not appropriate to address the application to the datasets used in this paper. The authors should include an analysis comparing rhapsodi against hapcut2, PHMM and other methods that are appropriate for the full scale and sequencing depth of the data. Additionally, the original Bell paper used a phasing + HMM approach of some kind for exactly this data. Why wasn't that approach considered as a point of comparison?

While your point is well taken, we do not believe that a direct comparison between rhapsodi and PHMM would provide additional insight. In the publication describing PHMM (Hou et al. 2013), their algorithm was designed for datasets containing lower numbers of cells (11-41) sequenced to higher coverage per cell (0.4-0.9) relative to the data analyzed by rhapsodi. PHMM is therefore, like Hapi, optimized for a more narrow range of parameters than rhapsodi. Across this range of parameters, Hapi uniformly performs better than PHMM. Other tools such as hapcut2 may be designed to work with lower coverages and higher cell numbers than PHMM and Hapi, but are designed for use exclusively with diploid genomes. rhapsodi is therefore the first haploid phasing tool that can work with large numbers of low-coverage cells and there is no existing software that operates in the same niche. While the parameter spaces of Hapi and rhapsodi only partially overlap, Hapi therefore remains the most appropriate point of comparison.

In addition to the point about analysis scripts versus a generalizable software package, we note two major differences between the steps employed in Bell et al. 2020 and rhapsodi’s method:

1) For phasing, Bell et al. (2020) used Hapcut2 in an “off-label” way that required artificial assignment of alleles from the same sperm cell to the same “read” for input. This approach ignores the positional information that was already encoded in the alignment and may not take full advantage of the co-inheritance patterns of the SNP alleles. The phasing method implemented in rhapsodi is a principled approach tailored to the structure of the input data and knowledge of the biological process of meiosis.

2) For crossover discovery, Bell et al. (2020) handled genotype error by encoding an “error” state in the HMM. In our method, we assign gamete-level genotypes via HMM-based imputation prior to detecting recombination breakpoints. We believe dealing with the error prior to crossover discovery is a simpler approach that better leverages the strengths of HMMs.

With respect to the method for imputation, no comparison is made to known recombination maps nor do the authors make any comparison across the maps derived from each donor. Reporting an improved method without it motivating novel biological conclusions is not compelling in itself. I suggest the authors expand that analysis to consider these are related questions. E.g., are there males whose recombination maps differ in specific regions? Are those associated with known major chromosomal abnormalities? Is this map consistent with estimates from LD, pedigrees, Bell et al?

We agree that evaluating the inferred crossover landscape in relation to published maps would be useful as a technical evaluation of our method, though we respectfully disagree with the suggestion to expand the scope of the manuscript to the analysis of inter-individual variability in the crossover landscape—topics that were the main focus of Bell et al. (2020). The distinction between our work and that study was addressed in our responses to previous comments.

To address the suggestion to compare to existing maps, we counted the number of inferred recombination events for each 1 Mbp genomic bin, pooling across the donors. We compared this result with a published male-specific recombination map inferred from trio sequencing data (Halldorsson et al. 2019) and observed a strong correlation with our map (R = 0.9; Figure 5-figure supplement 5). We have incorporated this in “Results: Application to data from human sperm” (lines 372-377; lines 385-391) and note the potential biological and technical reasons for the observed discrepancies (lines 391-399). One such technical reason for the observed modest discrepancy appears to be related to the sample sequencing depth of coverage. Rather than pooling the number of inferred recombination events for each bin across all donors, we repeated the correlation analysis in a donor specific manner. Then, we fit a linear regression model with the sample-specific sequencing depths of coverage as the predictor and the sample-specific correlations as the response variable. We found that the sample-specific correlation with the deCODE map was positively associated with depth of coverage (lines 391-399).

Most of the validations presented are based on simulated data. This is fine and has some advantages, but real data imposes challenges that these analyses do not address. My understanding is that the Bell et al. (2020) paper includes a donor with a phased diploid genome. A comparison of rhapsodi's phasing accuracy against that genome should be included.

Bell et al. 2020 included only sperm donors with previously unknown genomes, and phased their genomes via the sperm sequencing data. They validated their phasing approach in two ways: 1) via simulated data and 2) via comparing to the phase generated by Eagle (Loh et al 2016, Nat Gen) for one donor genome, specifically comparing the phase of neighboring sites phased with both approaches. Importantly, such population-based approaches achieve only local phasing of common variation, as opposed to the chromosome-scale phasing achieved via gamete sequencing. Nevertheless, we acknowledge that real data exhibits features that are not captured by simulated data. We tried to capture the most significant potential contributors from real data (e.g., genotyping errors) in our simulations. Our newly added comparisons to the Halldorsson et al. (2019) map help address this concern (Figure 5-figure supplement 5).

The main biological conclusion about a "strict adherence to Mendelian expectations across sperm genomes" is an overstatement. Statistical power of this study is still limited relative to the strength of TD that would be expected within human populations. One reason is the multiple testing correction. Another is that 1000-3000 draws from a binomial distribution with expected p = 0.5 is just not sufficient to overcome binomial sampling variance. In light of this concern and the central conclusion of this paper, the authors' discussion of power is inadequate. The main text really should contain explicit discussion of the required genotype ratio skew for TD in each donor to be detected with good power. Given previous pedigree studies, it is not surprising that no significant TD was discovered that exceeded the necessary ~10% effect sizes to be detectable. Recent, much more powerful analyses in mice, Drosophila and plants, indicate that strong TD is probably uncommon and even weak effects can be detected but are uncommon.

Thank you for these detailed suggestions regarding statistical power. Our manuscript is greatly improved by these updates to the power analysis and our comparison to alternative methods for investigating TD.

Specifically, we added additional simulations of TD at different rates (including very strong TD, as also noted in response to Reviewer 1) to demonstrate the range in which our study would be able to detect TD in this sample, considering the burden of multiple testing (Figure 4-figure supplement 3).

We added to the section titled “Results: Statistical power to detect moderate and strong TD” a statement about the strength of TD that would be detectable within the Sperm-seq dataset (lines 400-415). Briefly, the 25 donors have an average of 1711 gametes each (range 969-3377). Based on this sample size, we have Power = 0.681 to detect deviations of 0.07 (i.e., 57% transmission of one allele in a single donor) and Power = 0.912 to detect deviations of 0.08, accounting for multiple hypothesis testing across the genome and across donors (p-value threshold = 1.78 x 10-7). For an individual with 950 gametes, we have Power = 0.637 to detect deviations of 0.09 and Power = 0.84 to detect deviations of 0.1.

Based on these calculations, we agree that the term “strict” is subjective and may be considered an over-statement depending on the point of comparison, and we have modified the title accordingly.

This manuscript would benefit from a much clearer examination of statistical power and a detailed comparison of the power of this approach vs pedigree-based analyses as well as bulk gamete sequencing approaches. Although the authors are correct that all scans for TD in human genomes have been pedigree or single-cell based, more powerful alternatives are known. These are based on sequencing pools of individuals or gametes (e.g., Wei et al. 2017, Corbett-Detig et al. 2019). Each of those studies has been able to identify signatures of segregation distortion below the thresholds required for significance in this study. These and related works should be acknowledged in both the introduction and discussion. Although I appreciate that the ability to phase the genome in a single experiment may be appealing, phasing diploid genomes via hi-c omni-c is straightforward and the advantages in statistical power suggest that approaches using pools of gametes are preferable for well-powered scans for TD.

Thank you for your suggestions regarding contextualizing the statistical power of single-gamete sequencing-based approaches. Our steps to address these comments have strengthened our manuscript and made the paper more applicable to future research.

The single-cell nature of the low-coverage (~0.01x) Sperm-seq data allowed us to augment our sample size 100-fold at each SNP in a way that is not possible with a pooled sequencing approach. Pooled sequencing methods may augment statistical power for detecting TD by 1) combining information from nearby SNPs and 2) assuming different sperm are sampled at each site. This approach has relied on external knowledge of haplotypes (e.g., obtained through sequencing of inbred strains of Drosophila). This permits aggregation of alleles supporting one haplotype or the other across adjacent SNPs, which can increase statistical power. The same statistical test for TD cannot be applied to bulk sequencing data from human sperm (e.g., Bruess et al. 2019, Yang et al. 2021) without external knowledge of the parental haplotypes. One potential approach for circumventing this issue would be local phasing using patterns of LD from a reference panel, but this would limit the analysis to common SNPs within relatively small windows that can be adequately phased with such methods.

It is not immediately obvious that pooled sequencing studies have greater power for discovering TD than single-cell studies. None of the pooled sequencing studies mentioned by the reviewer performed similarly exhaustive power analyses, and the power analyses that were performed in pooled sequencing studies were done in systems with different levels of heterozygosity, different genome sizes, different sample sizes of donor individuals, etc. All of these factors affect the multiple testing burden, making it impossible to compare directly to a study in humans. Given the above considerations, we believe that an in-depth analysis of the statistical power of pooled sequencing approaches for discovering TD in humans lies outside the scope of our study.

We have nevertheless updated our manuscript to discuss the strengths of pooled sequencing methods as an approach for investigating TD, citing relevant studies in both the Introduction (lines 37-46) and Discussion (lines 508-529; lines 557-580). We acknowledge that these methods have been successfully applied in other species (e.g., Wei et al. 2017, Corbett-Detig et al. 2019) and their potential to improve statistical power. We note the steps that would be necessary for making these methods applicable for TD scans in humans as new datasets are produced.

We added a general power analysis of pedigree studies (Figure 4-figure supplement 4A) to illustrate the large sample sizes necessary to detect weak TD. To demonstrate the large sample size required for a pedigree study to achieve strong statistical power, we plot the number of informative transmissions of each SNP in the two pedigrees from Meyer et al. 2012 for which data was publicly accessible (Figure 4-figure supplement 4B).

Importantly, in a single-gamete sequencing study, the number of informative transmissions is equal to the number of genotyped gametes for all heterozygous SNPs. In a pedigree-based study, the number of informative transmissions varies across SNPs, as not all parent-offspring trios will include one or more parent heterozygous for a given SNP. For example, the Hardy-Weinberg expected proportion of heterozygous parents for a common SNP with an allele frequency of 0.5 is 2pq = 0.5. Meanwhile, variants at lower frequencies will possess smaller proportions of heterozygotes, thus capturing fewer informative transmissions and limiting statistical power. One implication of this distinction is that pedigree-based studies rely on distorter alleles that act across multiple families, effectively restricting such scans to variants that are common in the population. This contrasts with single-gamete sequencing studies, which provide equal power for detecting TD involving common and rare alleles, provided that they are heterozygous in the sampled donor individual. We note this in the Discussion (lines 508-529).

As noted by the reviewer, single-cell sequencing allows both phasing and examination of TD in a single study, allowing the investigation of meiotic recombination and its potential relationship with TD and fertility profiles. We have added text in the Conclusion (lines 659-693) to address this important point. Because of this study design, we are uniquely positioned to detect TD caused by any rare alleles we do capture; this contrasts with pedigree-based studies, where a distorter would need to be acting across multiple families to be detectable (thus restricting these scans to common variants). We have noted this in the Discussion (lines 521-529).

Author Response

Reviewer #1 (Public Review):

McLachlan and colleagues find surprisingly widespread transcriptional changes occurring in C. elegans neurons when worms are prevented from smelling food for 3 hours. Focusing most of the paper on the transcription of a single olfactory receptor, the authors demonstrate many molecular pathways across a variety of neurons that can cause many-fold changes in this receptor. There is some evidence that the levels of this single receptor can adjust behavior. I believe that the wealth of mostly very convincing data in this paper will be of interest to researchers who think about sensory habituation, but I think the authors' framing of the paper in terms of hunger is misleading.

There is a lot to like about this paper, but I just cannot get over how off the framing is. Unless I am severely misunderstanding, the paper is about sensory habituation, but the word habituation is not used in the paper. Instead, we hear very often about hunger (6x), state (92x), and sensorimotor things (23x). This makes little sense to me. The worms are "fasted" (111x) for 3 hours, but most of the expression changes are reversed if the worms can smell, but not eat, the food. And I've heard about the fasted state, noting that worms don't eat more food after this type of "fasting". So what is with all of this hunger/state discussion?

We think that the most straightforward interpretation of our data is that both sensory experience and internal nutritional state modulate str-44 expression. However, we agree that in the previous manuscript draft there was a disproportionate emphasis on state (as compared to sensory experience). The revised manuscript corrects this. However, several results in the manuscript do suggest that state is important, so we have not removed this from the manuscript. The lines of evidence that suggest this are:

(1) Animals exposed to inedible aztreonam-treated food show an increase in str-44 expression compared to animals exposed to untreated, ingestable food. Thus, food ingestion acts to suppress str-44 expression (Figure 1E).

(2) Animals exposed to food odor in the absence of food show an intermediate level of str-44 expression between “on bacteria” and “off bacteria” controls (Figure 1E). This incomplete suppression suggests that food odors alone can not explain the suppression of str-44 expression in well-fed animals.

(3) Animals that lack intestinal rict-1, a component of the TOR2 nutrient-sensing complex, show an increase in str-44 expression, which suggests that nutrient sensing in the intestine impacts str-44 expression (Figure 5).

(4) When animals are off food, osmotic stress inhibits the upregulation of str-44 (Figure 1G), reduces the enhanced behavioral sensitivity to butyl acetate (Figure 2G), and reduces the enhanced AWA activity in response to food (Figure 3). This physiological stressor provides a competing state that also impacts str44 expression.

We apologize for not adequately describing how three hours of fasting impacts C. elegans behavior in the initial submission. This is obviously a key piece of information and we have corrected this in the revised manuscript. [lines 68-70; 123-126] Regarding pharyngeal pumping rates, C. elegans typically exhibits pharyngeal pumping at a near-maximal rate on the OP50 laboratory diet even when well-fed.

Consequently, even much longer starvation times will fail to induce more feeding under these conditions. However, many other feeding-related behaviors do change with three hours of fasting, such as velocity on and off food, turning rates, roaming/dwelling behavior on OP50 food, and sensitivity to odorants. Thus, three hours of fasting is sufficient to impact several food search behaviors.

To more directly address whether sensory habituation in AWA alters str-44 expression, we performed an additional experiment. We exposed wild-type animals to the str-44 odorants butyl acetate or propyl acetate and measured str-44 expression. If habituation explains this effect (e.g. repeated exposure of an odorant reduces transcription/translation of the receptor), we would expect that exposure to these odorants would reduce str-44 expression in “off bacteria” animals. However, we observed no differences between odor-exposed animals and controls. [Figure 4-figure supplement 2B; lines 414-421]

And the discussion of internal states is often naïve. In the second paragraph of the introduction, we are told that "Recent work has identified specific cell populations that can induce internal states", beginning with AgRP neurons, which have been known to control the hunger state in mammals for nearly 40 years |||(Clark J. T., Kalra P. S., Crowley W. R., Kalra S. P. (1984). Neuropeptide Y and human pancreatic polypeptide stimulate feeding behavior in rats. Endocrinology 115 427-429. Hahn T. M., Breininger J. F., Baskin D. G., Schwartz M. W. (1998). Coexpression of Agrp and NPY in fasting-activated hypothalamic neurons. Nat. Neurosci. 1 271-272). Instead, the authors cite three papers from 2015, whose major contribution was to show that AgRP activity surprisingly decreases when animals encounter food. These papers absolutely did not identify AgRP neurons as inducing internal states or driving behavioral changes typical of hunger (Aponte, Y., Atasoy, D., and Sternson, S. M. (2011). AGRP neurons are sufficient to orchestrate feeding behavior rapidly and without training. Nat. Neurosci. 14, 351-355. doi: 10.1038/nn.2739; Krashes, M. J., Koda, S., Ye, C., Rogan, S. C., Adams, A. C., Cusher, D. S., et al. (2011). Rapid, reversible activation of AgRP neurons drives feeding behavior in mice. J. Clin. Invest. 121, 1424-1428. Doi: 10.1172/jci46229). Nor did Will Allen's work in Karl Deisseroth's lab discover neurons that drive thirst behaviors.

We agree that this introductory paragraph did not do justice to the literature and improperly cited only relatively recent work. We have addressed this oversight. [lines 48-53]

Later in the same paragraph, we hear that: "However, animals can exhibit more than one state at a time, like hunger, stress, or aggression. Therefore, the sensorimotor pathways that implement specific motivated behaviors, such as approach or avoidance of a sensory cue, must integrate information about multiple states to adaptively control behavior." This is undoubtedly true, but it's not clear what it has to do with any of the data in this paper - I don't even think this is really about hunger, much less the interaction between hunger and other drives.

To summarize: I think the authors could give the writing of the paper a serious rethink. I want to stay far away from telling people how to write their papers, so if the authors insist on framing this obviously sensory paper as being about hunger and sensorimotor circuitry I think they should at least explain to their readers why they are doing that in light of the evidence against it (and I think they should state clearly that worms don't actually eat more in this fasted state).

Please see the comments above that address these concerns.

I was also surprised by how unsurprised the authors seemed by the incredibly widespread changes they observed after 3 hours away from food. Over 1400 genes change at least 4-fold? That seems like a lot to me. But the authors, maybe for narrative reasons, only comment on how many of them are GPCRs (16.5%, which isn't that much of an overrepresentation compared to 8.5% in the whole genome). For me, these widespread and strong changes are much of the takeaway from this paper. But it does make you wonder how important the activity of one particular GPCR (selected more or less randomly) could be to the changes the worm undergoes when it can't smell food.

We agree with the reviewer that given the widespread gene expression changes in fasted animals, the changes in AWA are only a small part of the picture. We have added a discussion of this to the revised manuscript. In addition, we provide some discussion of how our gene expression profiling results relate to others in the field. For example, animals that lack the fasting-responsive transcription factor DAF-16 have been shown to have >3,000 genes differentially expressed relative to controls (Kaletsky, Lakhina et al., 2016). Given the large number of genes changing in those data and in our data, it is possible that transcriptional changes are extremely widespread during fasting. [lines 588-593]

str-44 is very convincingly upregulated when worms can't smell food, but it's clear from the data that this upregulation has very little to do with the actual lack of eating, and more with the lack of being able to sense bacteria for 3 hours. In Figure 1E, when worms are fasted, but in the presence of bacteria, receptor levels are largely unchanged (there are 5 outliers, out of ~50 samples). Since receptor expression doesn't change in this case even though the worms are in the fasted state, it cannot be "state-dependent" - unless the state is not having smelled food for the last 3 hours. And, in my opinion, that would divorce the word "state" from its ordinary meaning.

We have more closely examined that dataset, but we don’t feel that it would be accurate to say that the aztreonam (inedible) condition matches the fed. The highest points in the aztreonam-treated condition are most visible on the plot, but the effect is driven by the bulk of the data. Even if we remove the top 5 datapoints from the aztreonam condition, the effect is still statistically significant. Moreover, we performed this experiment over multiple days and the effect was present on each day. However, the reviewer’s point is well taken that sensory experience is equally (if not more) important for str-44 regulation and the text of the initial manuscript did not properly reflect this. As described above, we have modified the revised manuscript so that it is more balanced.

The authors argue that str-44 expression modulates food-seeking behavior in fasted worms by causing them to preferentially seek out butyl and propyl acetate. However, the behavioral data to back this up has me a little worried. For example, take Figures 2F and 2G. They are the exact same experiment: comparing how many worms choose 1:10,000 butyl acetate compared to ethanol when the worms are either fasted or fed. In the first experiment (2F), ~70% chose butyl acetate for fasted worms and ~60% for fed worms. But in the replicate, ~60% choose butyl acetate for fasted worms and ~50% for fed worms. A 10% variability in baseline behavior is fine (but not what I would call a huge state change), but when the difference between conditions is the same size as baseline variability I start to disbelieve. Can the authors explain this variability? Or am I misunderstanding?

We and others often observe large variance in C. elegans chemotaxis behavior over time because of small changes in environmental variables such as temperature, humidity, and pressure, so it is standard to always run wild-type controls together with all experimental groups and compare within day. The experiment in Figure 2F was conducted before the others in Figure 2G and Figure 4F. However, we remain highly confident in this result – we observed a difference in fed vs starved every time that we ran this experiment, which (in sum total for wild-type) was on 6 different days, with at least 3 plates per day (40-200 worms per plate).

And I'll say it just one last time, I think the authors are overselling their results...or at least the str-44 and AWA results (they are dramatically underselling the results that show the widespread changes in the expression level of 10% of the genome in response to not smelling food for 3 hours):

"Our results reveal how diverse external and internal cues... converge at a single node in the C. elegans nervous system to allow for an adaptive sensorimotor response that reflects a complete integration of the animal's states."

This implies that str-44 expression AWA is the determinant of whether a worm will act fasted or fed. I have already expressed why I don't believe this is the case (inedible bacteria experiment, Figure 1E), but just because things like osmotic stress suppress the upregulation of str-44, that doesn't mean that it is the site of convergence. It could be any of the other 1400 genes that changed 4+ fold with bacterial deprivation. And even in terms of the actual AWA neuron, it was chosen because it showed modest upregulation of chemoreceptors (1.8 fold compared to ~1.5 fold in ASE and ASG), even though chemoreceptors were highly upregulated in other neurons as well.

We agree that AWA chemoreceptors alone are unlikely to explain all of the behavioral changes observed in an animal that has been removed from food, and we certainly did not intend to imply that str-44 expression in AWA is the central determinant of whether the animal acts as though it is fasted or fed. Rather, we have shown that str-44 expression can explain some of these behavioral changes. We have added language throughout the manuscript to indicate that we expect other fasting-regulated genes to be of importance. See also: response to Essential Revision #1.

Overall, and despite my critiques (and possibly tone), I really like this paper and think there really is a lot of interesting data in there.

Author Response:

Reviewer #1 (Public Review):

Here, the authors used multiple F1 crosses and the resulting embryonic fibroblasts to perform molecular profiling with ATAC-seq and a combination of ChIP-seq, Hi-ChIP, and CUT&RUN on multiple modified histones and transcription factors proteins. The resulting data are a good resource for quantifying allelic bias in protein-DNA binding and chromatin accessibility.

The authors claim there's "enrichment of SNPs/indels within a 150 bp window" in enhancers (Fig. 2H), but this enrichment looks quite middling. Can they quantify the level of enrichment and is it significant?

We have added a quantification of the enrichment of SNPs in the allele-specific enhancers compared to shared enhancers (Lines 1382-1385). The average number of SNPs within central 150 bp of enhancers is:

4.468 for enhancers with allele-specific H3K27ac levels. 3.203 for enhancers with shared H3K27ac levels. For these shared enhancers, we subsampled the shared sites to generate a set with an identical distribution of H3K27ac levels to that observed on the active allele of the allele-specific set. This helps to control for potential differences in mappability of each allele given that the allele-specific set has more SNPs, on average, and SNPs are necessary to identify allele-specific reads. (discussed in Lines 1261-1264).

This enrichment is also clearly significant (p-value < 2.2 x 10-16, Pearson’s Chi-squared test). We have added this information to the corresponding figure legend in the revised manuscript (Lines 1381-1382).

Author Response

Reviewer #3 (Public Review):

This work addressed some of the limitations in the production of the CVS-N2c strain of the rabies virus. CVS-N2c exhibits lower cytotoxicity and more efficient transsynaptic spread than the more widely used SAD-B19 strain, but its use as a circuit tracing tool has been held back by its slow packaging process and low resultant titers. By demonstrating that rabies packaging cell lines do not affect retrograde labelling efficiency and by creating a pseudotyping cell line that can amplify pseudotyped virus from a small amount of starting material, Sumser et. al have achieved an improvement in the speed, titer, and native coat contamination of CVS-N2c preparations whilst generating a new set of viral vectors that will help to implement a range of circuit mapping tools.

While many of the results from N2c evaluation experiments shown here (including bicistronic rabies usage, time courses of functional characterisation with GCaMP/channelrhodopsin, Cre-OFF labelling) have been previously demonstrated in other N2c and SAD-B19 rabies studies, the suite of vectors described in the manuscript will serve as a useful resource for the community. However, some key aspects of these vectors, specifically the propensity for the starter AAV for off-target labelling, are not characterized.

We thank the reviewer for his / her positive comments (“improvement”, “useful resource”).

1) The six DIO AAV vectors described here, and the Flp-dependent AAV-FRT-EF1a-TVA-2A-N2cG do not contain recombinase leak prevention mechanisms such as the "ATG-out" approach, where the initiating codon and Kozak sequence are moved outside of the recombinase recognition sites to reduce inverted ORF expression. Even with these measures in place, DIO constructs are prone to recombinase-independent reversion, proposed to occur during AAV production from spontaneous recombination (Fischer et al., 2019). This presents an issue for the sensitive TVA/EnvA system, where only a small amount of TVA expression can mediate off-target rabies infection in non-Cre expressing cells. The dilution of AAV vectors can have a strong effect on the amount of non-specific labelling (Lavin et al., 2020). As the bicistronic TVA-N2cG vectors used here do not allow for individual dilutions of TVA with respect to N2cG, which is required at higher expression levels for efficient transsynaptic spread, it is especially important to test these vectors for leak expression. A sensitive test for starter leak would be to inject the AAV and rabies virus in WT mice.

We are aware of these potential issues with the AAV targeting system. We can confirm that in our hands, all vectors have been thoroughly vetted, and no leak has been found for any. For each new viral batch produced (37 in total) we have conducted experiments in which pseudotyped particles at work concentrations (1–5 × 108 TU/ml) were injected into naïve brains and have found only minimal non-specific labeling (less than 1–2 cells per 5–10 100-µm-thick sections examined).. We have added a sentence to the Materials and Methods section (p. 5 of the revised manuscript).

Furthermore, we have tested the effects of extremely high viral titers are (100–500-fold higher than the titers used throughout the manuscript). We found that even with these extremely high virus concentrations, contamination was minimal. Furthermore, we found that the negligible contamination in these experiments likely arises from direct penetration of pseudotyped particles into damaged cells and cell processes along the needle tract. We have added a new Figure 1 – figure supplement 2 and added a sentence on p. 5 of the revised manuscript.

We agree that the system might benefit from additional safety measures. However, these potential safety measures could also introduce new problems. In finding the right balance, one should take into account that such leak events are rare, and their random occurrence should make it possible to distinguish them from the main effects by replication.

2) The manuscript reports the use of a bicistronic N-P system to express the optogenetic actuator ChIEF together with a fluorescence protein. While the results of the bicistronic experiments show that both proteins are successfully expressed, control experiments using other expression strategies would strengthen the claim that the bicistronic N-P system is superior.

In our work, we compare the activation effectiveness of the optogenetic actuator to previously published results from two separate manuscripts (Reardon et al., 2016; Osakada et al., 2011), using comparable light intensity. Our results demonstrate that our vectors achieve higher AP success rates with substantially shorter light pulses. While we have not conducted a direct comparison, we think that the improvement presented in the bicistronic vectors is sufficiently substantiated, and the logic behind this improvement sufficiently sound. Since this is a lateral point in our manuscript but a relevant information for the community, we believe that this point is worth mentioning even without a direct comparison.

Author Response

Reviewer #1 (Public Review):

The authors used single cell RNA-seq to assess the heterogeneity of megakaryocytes, thereby identifying a distinct CXCR4 high subpopulation that was also enriched in inflammatory genes and other chemokines or cytokines. They sort CXCR4 high cells and are able to investigate specific functional properties of this megakaryocyte population. This work complements prior studies which have suggested immune modulatory roles for certain megakaryocyte subsets such as the work of Pariser and colleagues (JCI 2021) on the antigen presentation capacity of lung megakaryocytes or the work by Liu et al (Advanced Science 2021) on immune surveillance gene expression in megakaryocytes (MKs).

The strengths of the paper are:

1) Analysis of scRNA-seq to identify MK subsets with validation

2) The use of sorted CXCR4 cells to interrogate the specific in vitro functions of this immune modulatory subset (using CXCR4 low MKs as a comparison) such as phagocytosis assays

3) Elegant use of the PF4-Cre DTR model to ablate MKs while replenishing CXCR4 high cells as a means to assess functional effects of this subset in vivo which is a reasonable approach in the absence of a Cre that would specifically delete this subset.

We appreciate the positive feedback from this reviewer.

Potential weaknesses are:

1) The unclear distinction between previously identified immune modulatory MK subsets such as the lung MKs which have antigen-processing capacity (Pariser et al) and the currently identified MK5 subset. The authors indicate that the MK5 subset has transcriptomic similarities to the previously described antigen-processing MK subset but this does not explain whether MK5 and/or CXCR4 high subset is indeed the primary. This is an important question because it would help address whether the immune modulatory roles are all concentrated in one MK subset or whether different MK subsets may play distinct roles in innate and adaptive immunity. For example, in Fig 3, there is a broad claim that MKs can modulate innate and adaptive immunity but it is not clear whether this claim is valid only for the specific MK5/CXCR4 subset.

We totally agree with this argument. Our revised data showed that CXCR4high MKs, but not CXCR4low MKs, were able to phagocytose bacteria (Revised Fig 3F), process and present ovalbumin (OVA) antigens on their cell surface (Revised Fig 3G) to activate CD8+ OT-I T cells (Revised Fig 3H) and B3Z T cells (Revised Fig 3-S2), a T cell hybridoma which expresses TCR that specifically recognizes OVA. These revised data showed that CXCR4high MKs are an antigen processing and presentation subset in MKs.

2) It would be helpful to understand whether the CXCR4 status of MKs can change over time. Are the CXCR4 high cells generated in infection (Fig 5) generated by the conversion of CXCR4 low cells (or non MK5 cells)? Or do CXCR4 high / MK5 cells differentiate from MK progenitors directly?

Thanks for the suggested experiment. Our revised data showed that inflammatory treatment, including interferon γ, LPS, and L. monocytogenes could not increase CXCR4 expression in CXCR4low MKs (Revised Fig 4H and Fig 4-S4D). This experiment suggested that CXCR4high MKs might not be reprogramed from CXCR4low MKs. Furthermore, our HSPC tracing experiment showed that CXCR4high MKs were generated from HSPCs as efficiently as CXCR4low MKs during the acute inflammation-induced emergency megakaryopoiesis (Revised Fig 5E-G).

Reviewer #2 (Public Review):

Wang J. et al. examines bone marrow megakaryocyte (MK) heterogeneity, and the role that a specific subpopulation plays in the mouse immune response to Listeria monocytogenes infection. Using single cell RNA-sequencing (scRNAseq) the authors identified a bone marrow MK subpopulation, characterized by high CXCR4 expression. This subset referred to as MK-derived immune-stimulating cell (MDIC) population has immune-stimulatory properties and supports the migration and activation of innate immune cells potentially via TNFα and IL-6 secretion.

In agreement with recent studies mapping in situ myelopoiesis which occurs near bone marrow sinusoidal vessels upon acute inflammatory stress with L. monocytogenes (Zhang J. et al Nature 2021), the authors observed a significant association of myeloid cells with perivascular CXCR4high MK but not with the more abundant CXCR4low MK subset. This study also revealed that MK in vivo deletion leads to a significant increase in the bacterial load in extramedullary hematopoietic organs accompanied by a reduction in the number of myeloid cells, although it is unclear if a similar MDIC population exists outside the bone marrow. Accordingly, it is unclear the effect of MK depletion in the context of L. monocytogenes infection in bone marrow myelopoiesis.

Notably, in a rescue experiment, MDIC infusion was able to partially rescue the bacterial clearance defect in MK depleted and infected mice, further confirming the important role of MDICs in regulating bacterial immune responses.

Using Pf4-cre reporter mice the authors further evaluated the capacity of bone marrow MDIC to enter circulation and migrate into organs upon bacterial infection potentially in response to an increase in CXCL12 expression in extramedullary organs. Finally, in agreement with recent studies (Haas S. et al Cell Stem Cell 2015), Wang et al. discovered that upon inflammatory stress, emergency hematopoietic stem cell-derived megakaryopoiesis is activated to restore platelets lost upon inflammation-induced thrombocytopenia but also to regulate immune response to bacterial infection.

Overall, this study builds on recently published work regarding MK heterogeneity which technically is very challenging to investigate. Although it's suggested that MDIC greatly overlap with the recently described CD53+LSP1+ MK immune population (Sun S. et al Blood 2021), it is still unclear the extent to which these subsets overlap, accordingly, it's still unclear the relationship between bone marrow MDIC and previously described lung MK subsets, though to be enriched in immune function. Nevertheless, the authors performed a detailed characterization of bone marrow MDIC in homeostasis and in acute inflammatory stress, providing new evidence and mechanistic clues on the mechanisms by which MK subsets regulate immune function to bacterial infection.

While this manuscript has many strengths, some of the author's conclusions and claims require further technical support and discussion. In particular:

1) The potential mechanism via TNFα and IL-6 secretion is very interesting, however further data is necessary to support the author's claim. First, it's unclear if steady-state MDIC MK express TNFα and IL-6. If so, does this expression change upon infection?

MDIC MKs (now referred to as CXCR4high MKs) expressed TNFα and IL-6 during the steady state, and maintained their expression levels upon L. monocytogenes infection (Revised Fig 2J).

Second, mechanistically it would be important to evaluate or at least discuss how MDIC sense bacterial infection and respond by secreting TNFα and IL-6.

Thanks for the suggestion. In this revision, we have included a brief discussion about previous studies that reported that MKs express multiple inflammation signals, which enable MKs to sense inflammation signals and express cytokines, as “MKs were reported to express multiple inflammation receptors, such as Fcγ receptors (Markovic et al., Br J Haematol 1995), Toll-like receptors (Beaulieu et al., Blood 2011; Ward et al., Thromb Haemost 2005), interleukin receptors (Navarro et al., J Thromb Haemost 1991; Yang et al., Br J Haematol 2000), and IFN receptors (Negrotto et al., J Thromb Haemost 2011), which might enable MKs to receive inflammation signals and express cytokines.” (Line 15-19, Page 13).

Third, in Fig 2L and 2M it's missing a control for the effect of anti-TNFα and anti-IL-6 on phagocytes activity in the absence of MKs.

Thanks for the suggested control. In this revision, we have confirmed the phagocytosis activity of immune cells by flow cytometry assays as suggested by this reviewer, in which we included the anti-TNFα and anti-IL-6 controls in the absence of MKs (Revised Fig 2M, N). Our revised data consistently showed that CXCR4high MKs enhanced the phagocytosis activity of neutrophils and macrophages through a TNFα and IL-6 dependent manner.

Fourth, in Fig 2J and 2K it's unusual to evaluate TNFα and IL-6 levels by imaging.

We agree with the argument. In this revision, we have further evaluated the expression of TNFα and IL-6 by flow cytometry, which consistently showed that CXCR4high MKs had higher expression levels of TNFα and IL-6 than CXCR4low MKs (Revised Fig 2J).

2) The authors further explored the potential role of MKs in regulating adaptive immune function against bacterial infection, however these studies were very superficial and further studies are needed to substantiate this claim.

We totally agree with this argument. In this revision, we have deleted the claim that MKs regulate adaptive immune function. Furthermore, Our revised data showed that CXCR4high MKs were able to phagocytose bacteria (Revised Fig 3F), and process and present ovalbumin (OVA) antigens on their cell surface (Revised Fig 3G) to activate CD8+ OT-I T cells (Revised Fig 3H) and B3Z T cells (Revised Fig 3-S2), a T cell hybridoma which expresses TCR that specifically recognizes OVA. These revised data suggested that CXCR4high MKs had antigen processing and antigen presentation capacity, which suggested that CXCR4high MKs might contribute to the regulation of adaptive immune function. We have included a brief discussion (Line 2-5, Page 14).

3) Overall, the study relies heavily on subjective imaging quantification. The identification of CXCR4high and low MK subsets does not seem entirely objective and it is prone to inaccuracies due to the technical difficulty of bone imaging. The usage of other surface marker(s) for the MDIC subset would significantly improve the study. Accordingly, many of the experiments should be accompanied and/or replaced by flow cytometry analyses such as the phagocytosis experiments in Fig 2; quantification of MKs in Fig 4 H, I and N.

We totally agree with this argument, and we have discussed that additional markers are warranted to further enrich CXCR4high MKs (Line 5-9 Page 14). Furthermore, we have further confirmed our imaging quantifications by flow cytometry, such as the bacterial phagocytosis ability of immune cells and CXCR4high MKs (Revised Fig 2M, N, Fig 2-S2A, B and Fig 3F) and the number of Tomato+ CXCR4high MKs in the liver, spleen, and lung (Revised Fig 4I, O and Fig 4-S4I).

4) Regarding MK-deletion experiments, studies from the Passegue lab have shown that this will cause persistent bone marrow myeloid granulocyte/macrophage progenitor (GMP) formation during 5FU stress, most likely due to the reduction in the levels of PF4 and TGFb1 and the effect on hematopoietic stem cells. What happens to bone marrow myelopoiesis upon MK-deletion and bacterial infection? The authors describe a significant reduction in the liver and spleen but it's unclear the effect on the bone marrow. It would be helpful to discuss this point.

Our revised results showed MK ablation increased the number of hematopoietic stem and progenitor cells and myelopoiesis in the bone marrow upon infection (Revised Fig 3-S1A-D). However, myeloid cells were reduced in the liver and spleen after MK ablation and bacterial infection (Revised Fig 3D-E). This further suggested the important role of CXCR4high MKs in promoting the migration and function of myeloid cells. We have included a brief discussion on this point (Line 10-14, Page 14).

Reviewer #3 (Public Review):

Overall this is an interesting study that adds significant knowledge to our understanding and characterization of Mks as immune cells. The identification of CXCR4hi Mks as immune regulatory cells is potentially important, particularly in the bacteria model used in this study.

We appreciate the positive feedback of this reviewer.

At this stage, the authors have however made a number of conclusions not yet supported by the data. In particularly differentiating the role of Mks versus the platelets they produce is not clear, so many conclusions about MDIC in immune responses need to be better supported and differentiated from platelet functions.

We agree with this argument. We cannot exclude the role of platelets in immune responses. Our revised data showed that CXCR4high MKs produced fewer platelets (Revised Fig 1-S6D) but had more robust abilities in phagocytosis and antigen processing and presentation (Revised Fig 3F-H and Fig 3-S2), and stimulating innate immune cells by secreting cytokines (Revised Fig 2E-N and Fig 2-S2) than CXCR4low MKs. Furthermore, infusion with CXCR4high MKs, but not CXCR4low MKs, partially rescued the host-defense responses in MK ablated mice, which further supported the role of CXCR4high MKs in immune responses. However, the infusion rescue experiment with CXCR4high MKs did not fully rescue the host-defense responses in MK ablated mice (Revised Fig 3K-L). This is partially due to the reduced platelets in MK ablated mice as platelets are known for immune responses. We have discussed this possibility in the current version (Line 16-17, Page 9).

Author Response

Reviewer #1 (Public Review):

This manuscript addresses the role of the p75NTR neurotrophin receptor in the development of cerebellar granule precursor cells (CGPs). This cell type is notable for having high levels of p75NTR expression in a discrete developmental window yet the specific role of the receptor in this setting has remained obscure.

The authors show that although p75NTR expression correlates with the CGP proliferative state, expression of p75NTR is not required to maintain the proliferative state. Rather, migration CGPs in culture and within cerebellar slices is optimal only when p75NTR levels are reduced and the authors conclude that the expression of p75NTR normally reduces CGP migration. They examine signalling mechanisms that lie downstream of p75NTR to elicit this effect and show that RhoA, previously shown to be activated by p75NTR, is required to block CGP migration, that RhoA activity is lower in p75NTR-/- CGPs than in wild-type counterparts, and that RhoA inhibitors enable CGP migration, even in cells overexpressing p75NTR.

This is an important study that uses a combination of descriptive methods and chemical and genetic gain- and loss- function approaches to demonstrate that a p75NTR-RhoA signaling pathway normally functions to limit CGP migration during development. The paper is logical and well written and the data presentation is excellent.

Some points to consider:

Figure 2A introduces the CGP cultures and shows that p75NTR levels are high in cells exposed to SHH. However, these results are difficult to interpret in the absence of controls showing p75NTR levels at the time of plating - does the SHH exposure increase p75NTR expression? Or prevent its decrease?

We agree with the question raised by the reviewer, and we have done this experiment. In these results, we observed an increase in p75NTR expression after 24h or 48 h of Shh exposure compared with the levels of the receptor at the time of plating. However, there are a few caveats to the interpretation of these results, that make it difficult to establish whether Shh increases or prevents the decrease of the receptor:

1. When quantifying the levels of p75NTR in vivo, we obtained a granule cell population that includes proliferating and differentiated granule cells, this mixed population of cells is present at the time of plating. When establishing primary culture, a large percentage of the cells do not survive, and the majority of dying cells would be differentiated cells, therefore introducing a bias toward proliferating cells for the 24 and 48 h in vitro from the time of plating. The proportion of proliferating/differentiated cells would be different between the in vivo and the in vitro after 24 or 48h.

2. The concentration of the mitogen most likely would be very different between the cells in vivo (the time of plating) and the exposure to Shh in vitro, introducing a second bias. It might be that the increase in p75NTR is a consequence of more cells proliferating since they respond to higher concentration of the mitogen.

3. We know Shh induces proliferation in CGN, and this is accompanied by an increase in p75NTR. Therefore, the increase of p75NTR might be due to more proliferating cells, but not necessarily an induction of the expression of the receptor.

I recognize the convenience of using the p75NTR-GFP construct to track migration but was surprised that the potential confounds of this approach were not examined or even mentioned. Does p75NTR-GFP activate RhoA more or less than the wild-type receptor? What experiments have been performed to ensure that this construct is an effective mimic of the wild-type receptor? Would it be possible to co-transfect p75NTR and GFP as an alternative approach?

The p75NTR/GFP construct has been used in the field for an extensive period and the biology of the construct has been well characterized (i.e. cellular localization and translocation, activation and signaling). Co-transfecting the slices with p75NTR and GFP with separate construct doesn’t necessarily mean that each cell receives both constructs, which is not the case using a fusion protein. Although we cannot completely rule out the possibility of subtle intracellular differences between the endogenous p75NTR and the construct, we are confident that this result is supported by the other experiments in the manuscript (the conditional deletion of p75, results with the p75NTR -/-, and the use of inhibitors) Paper showing that the p75-GFP construct is correctly sorted https://www.ncbi.nlm.nih.gov/pmc/articles/PMC2139957/

The authors discuss previous findings that indicate that p75NTR can play a pro-migratory role but oddly do not place their results in other contexts where p75NTR has been shown to block migration. CGPs have been quite widely used to dissect the role of p75NTR in the Rho-dependent migration blockade induced by MAG and other myelin components and interesting insights on receptor components (e.g. LINGO1) and signalling mechanisms (e.g. RhoA) that mediate these effects. The results reported here should be discussed in the context of these previous findings.

We agree with the reviewer and we will discuss our findings in this context.

Author Response

Reviewer #1: (Public Review):

“My main quibble is with the framing. There are many places throughout the manuscript where the authors claim that there is a great deal of controversy about the extent of the branching of these neurons.”

We agree with our reviewer that some of our statements were misleading. Thus, we have rephrased the Introduction (Pages 3-5; Lines 54-99), Results (Page 20; Lines 356-363) and Discussion (Pages 26-32; lines 472-478, 492-498, 525, 530532, 551-578, 586, 596-602) sections to focus on the controversial issues of the simultaneous projection to NAc and VTA by the same prefrontal cortical population.

Reviewer #2 (Public Review):

“The scope of this work is somewhat smaller than the recent reconstruction and molecular subtyping of ~6300 neurons performed by others: a comprehensive paper on this very topic ("Single-neuron projectome of mouse prefrontal cortex", Nat Neurosci 25:515”

The Gao et al. (2022) study published during our reviewing process, indeed, confirms some of our findings. A common finding of ours and Gao et al (2022) is that mPFCNAc and mPFCVTA neurons form distinct classes within the mPFC projecting neuronal population. In addition, there is a small PT-like mPFC population, located rather in the L5b (showing RBP4 expression in our study), which sends branching axons to both NAc and VTA.

Still, we think that the novelty of our work has remained significant.

1) We have provided easy-to-use, widely available molecular approaches to investigate mPFC territories and laminar organization. Using the detailed expression pattern of neurochemical markers revealed via multiple immunohistochemical technique and confocal microscopy, we were able to delineate borders between mPFC regions and layers with considerably high precision. For this purpose, mostly brain atlases are used. However, in a cortical region, like the mPFC, territory borders and shapes, as well as laminar thickness and depth are greatly changing at antero-posterior as well as dorso-ventral axes. Therefore, experiment-to-experiment, ‘stable’ markers are necessary to identify the exact location of neurons, recording sites, optic fibre positions, etc; that we, in our opinion, provided in the present study.

2) Using the presented direct molecular composition, we have identified genetic markers for selective examination of layer (and at some extent, region) -specific mPFCNAc and mPFCVTA populations.

3) We have also provided evidence for the utility of this characterization using Cre mouse lines. The use of Calb1-, Rbp4-, Ntsr1- and FoxP2-Cre, which strains are widely used in cortical studies, in an intersectional approach, allow scientist to selectively investigate each of these mPFC populations, even in a target-selective manner via an intersectional approach.

Major points:

”…But what I think is lacking here is a characterization in a region-by-region manner of the laminar organization of the cell types you either identify by retrograde label (CAV-Cre anatomy, for example) or by molecular approaches (how the lamination of Ntsr1+ neurons vary between the areas you lump together here as PFC).”

”…I think this subdivision might help by defining these areas in stereotaxic coordinates and giving some idea of how defined cell types (defined by Cre driver or retrograde label or other marker) might vary in their laminar distribution across these areas. Maybe I am wrong, but my perception of Fig 1 and 2 is mainly that the laminar pattern of cortical labeling from VTA and NAc varies somewhat depending on where you assess it in cortex...”

We have plotted the location of the retrogradely labeled mPFCNAc and mPFCVTA cells which clearly shows their characteristic laminar and regional distributions. These panels are added to Figure 1-2.

The lamination of NTSR1 neurons is remarkable, indeed. As it can also be seen on the GENSAT website (http://www.gensat.org/imagenavigator.jsp?imageID=48699), the L6 of PrL, IL and the more ventral regions lack NTSR1-expressing cells, while L6 of the cingulate and motor cortices contain a moderate density of this cell type.<br /> In our experiment, in which we aimed to target Prl-IL-MO (as majority of the retrogradely labeled mPFCNAc and mPFCVTA cells were located there), we could not detect any viral labeling in any of the layers ventral to PrL cortex (Figure 3). The labeling in the cingulate cortex is missing, probably, due to the lack of AVV diffusion into its deep layer, L6. However, as it can be seen in Figure 3–figure supplement 2H, the NTSR1-expressing the L6 neurons in M1 are also present in our trials. Altogether, it means that NTSR1 is only present in L5a of PrL cortex among the cortical regions which contain mesolimbic-projecting neurons. The shift in the distribution of Ntsr1expressing cells is present between PrL and Cg cortices.

Author Response

Reviewer #1 (Public Review):

Marchetti and colleagues present an ex vivo culture method that enables live imaging studies of Drosophila adult midguts for periods up to 3 days. Important technical innovations include defining an optimized tissue culture media, placing midguts at an air-liquid interface for better oxygenation of the tissue, performing inducible gene expression while imaging, and performing multiplexed imaging of up to 12 midguts in a single culture. Using this ex vivo method, the authors show that midgut progenitor cells proliferate and differentiate in response to epithelial damage ex vivo. The authors exogenously activate the cell cycle, which enables them to trace and analyze the division behaviors of multiple generations of stem cell progeny, including the distances between sibling cell nuclei over time. Finally, proof-of-principle imaging of adult renal tubules and egg chambers is provided.

Altogether, this ex vivo method offers important new advantages that will attract broad interest in the Drosophila community. My main concerns are (1) midgut viability when imaging is performed with a confocal microscope and (2) uncertainty about the authors' classification of asymmetric and symmetric fate outcomes.

Major comments:

1) The ability to perform continuous imaging over periods as long as 72 hours is a significant achievement. As the authors point out, this time scale is several fold longer than the 16 hour viability window of in vivo imaging (Martin 2018). The multiday timescale is important because it could, in principle, enable live imaging of many fundamental, but slow, cellular behaviors such as enterocyte differentiation.

If I understand correctly, the multi-day experiments in the study were captured using imaging conditions that were particularly gentle: (1) widefield epifluorescence, (2) an interval of 1 hour between time points, and (3) at most two fluorescent channels. By comparison, the 16 hour viability window defined in Martin 2018 was based on confocal imaging at 7-15 minute intervals in 3-4 channels. Can the authors provide information on midgut viability when their culture method is combined with confocal microscopy at minutes-long time intervals? This information is important to help users assess the types of questions that ex vivo culture can address given the widespread use of confocal imaging and the necessity of subcellular spatial or better temporal resolution for certain types of questions.

Viability during prolonged imaging is greatly dependent on the conditions used. If acquisition parameters are carefully set, intestines can be imaged using a confocal microscope with 15 minute intervals for a 48h interval. A movie has been added to demonstrate this (Video 23), and it has been discussed on lines 951-953. We also tested our live-imaging protocol on a Zeiss Lattice Lightsheet 7 microscope and observed no visible signs of phototoxicity after a 48 hours session with two channels (nlsGFP and His2Av.mRFP) 60µm z-stacks captured at 15 minute intervals. In regards to phototoxicity, it is hard to compare the different microscopes we tested quantitatively. As phototoxicity depends on the amount of light shone on a sample, we would need to carefully quantify the amounts of light delivered to the samples to determine the optimal frame rates and durations of different imaging methods, and have haven’t done this. Of course, since widefield, confocal, and lightsheet microscopes image samples in very different ways, comparing imaging quality is also a challenge. Therefore, all we can say with confindence is that, in our experience, if imaging parameters are set to minimize light exposure, all three different microscope types are viable for long term live-imaging. We have added some comments about microscopes to the Results section, lines 139-145, which we think will be helpful to users.

2) The real-time tracing of multiple stem cell lineages through up to three generations is an impressive first for the midgut. The lineage trees are fascinating to examine. However I am unsure that division fate outcomes can be classified as symmetric or asymmetric using the data that are shown.

2a) Some divisions (9 of 25) were classified as asymmetric because exactly one sibling cell divided at a time point >6 hours before the end of the movie (lines 271-277). In my view, these fate outcomes are ambiguous because it cannot be excluded that the other sibling is a stem cell that would have divided after the movie ended. Although 6/7 sibling pairs that the authors observed exhibited temporally correlated divisions, failure to observe temporally correlated divisions is not a basis for concluding that sibling fates are asymmetric.

2b) Other divisions (8 of 25) were classified as asymmetric based on both the criteria in 2a and the observation that the non-dividing sibling showed increased nuclear size and decreased GFP intensity (lines 277-279). I agree with these criteria, but to my eye, the images in Fig 6 and Video 16 do not clearly show these changes. The nuclear size of the non-dividing sibling in panel G is not significantly different from the (presumably 4N) nuclei of the symmetrically dividing siblings in panel E. The GFP signal of the non-dividing sibling diminishes at the end of the movie, but without the His2Av::mRFP channel, I cannot tell whether the cell has lost GFP or, alternatively, has disappeared from view.

2c) The midguts lack markers to distinguish enteroblasts, enteroendocrine precursor cells, and stem cells. Without these, several types of fate outcomes are indiscernible: Asymmetric divisions that produce a stem cell and an enteroendocrine precursor (which remains diploid and can divide again), symmetric divisions (of enteroendocrine precursors) that produce two enteroendocrine cells (c.f. Chen 2018), and symmetric divisions (of stem cells) that produce two enteroblasts (c.f. de Navascues 2010, Guisoni 2017). Additionally, Kolhmaier 2015 has shown that stg/cycE manipulation results in divisions of SuH+ enteroblasts; these enteroblast divisions cannot be distinguished from stem cell divisions in the movies.

Can the authors either provide additional data that resolves the ambiguity of these fate classifications, or, alternatively, revise the text to describe these data in terms of division timing, displacement, and the other cell behaviors that are observed? In the latter case, speculation about fate outcomes could be added to the discussion.

As we were unable to collect additional data that could distinguish cell fates in our live lineage analyses, we have revised the text to describe division events based on the daughter cells’ actual behavior rather than their presumed cell identities and fates. We now refer to sister cells in lineages as either “co-dividing” and “non-co-dividing”, and define these terms (lines 277-283 and 301-307).

Reviewer #2 (Public Review):

This work provides a new protocol for extended culture of Drosophila midguts ex vivo and live-imaging for up to three days. This paper reveals a significant improvement of explanted intestines survival compared to previous protocols by optimizing the dissection procedure; by modifying the culture medium so that it approximates the adult hemolymph and by fine-tuning the live-imaging setup. In addition, this new protocol allows temperature-sensitive gene expression or knock-down ex vivo. By successfully performing intestinal stem cell lineage tracing experiments and cell tracking over time, authors demonstrate the potential and the robustness of this system in understanding key intestinal processes such as stem cell proliferation and cell differentiation over time. Interestingly, preliminary results demonstrate the possible use of this protocol for extended culture of other organs and its implication in other areas of research.

The relevance of the new protocol proposed by the authors in the improvement of the extended culture and live-imaging of intestines is well supported by the data. However, additional key control experiments would be needed to increase the confidence in using this protocol for the study and understanding of key intestinal processes.

1) Authors tested the viability of explanted intestines over time by assessing different aspects such as the cell death or by testing the ability of cells to proliferate and differentiate. Adding control experiments to assess the state of the trachea and the visceral muscles, two major components of intestinal processes, would be needed.

We have now added considerations about trachea (lines 96 and 112) and visceral muscle (lines 984-996) to the main text.

2) Authors tested GFP expression at permissive temperature in explanted intestines using intestinal stem cells or enterocytes GAL4 driver and detected no differences compared to in vivo condition.

Did the authors quantify the number of intestinal stem cells at different time points in explanted intestines? Did they see a difference compared to in vivo conditions?

Same questions for other cell types?

This analysis could be a good control to further validate the use of this system for the study and understanding of key intestinal processes.

Since in undamaged intestines we did not observe cell death, the number of cells of any type remains constant in our cultured intestines. Therefore, cell composition is the same before (i.e. in vivo) and after (i.e. ex vivo) dissection. When using the esgTS>UAS-GFP line, we did not observe any difference in GFP+ cell numbers between intestines shifted to the permissive temperature in vivo or ex vivo.

3) Authors tested the ability of explanted intestines to regenerate following intestinal damage induced by SDS feeding. SDS feeding results in stem cell proliferation and progenitors differentiation in explanted intestines. Adding control experiments comparing stem cell proliferation and cell differentiation upon control feeding or upon SDS treatment in explanted intestines versus in in vivo conditions would reinforce the use of this system.

A new figure (Figure 3 – figure supplement 1) has been added to provide a SDS treatment in vivo comparison to our observation ex vivo. Results are discussed in the main text at lines 210-220.

Author Response

Reviewer #2 (Public Review):

Ivica et al., conducted a series of electrophysiological and cryo-electron microscopy studies to investigate what differentiates partial agonist versus full agonist effects at the glycine receptor, a member of the cys-loop receptor superfamily. To this end, they used aminomethanesulfonic acid (AMS), a novel partial agonist that possesses efficacy intermediate between the high efficacy agonist glycine and the partial agonists beta-alanine and taurine. AMS was shown to possess a maximal channel open probability of 0.85, compared to 0.96 for glycine and only 0.12 for taurine. Cryo-EM structures of glycine receptors that had bound glycine, AMS, or taurine differed, with only glycine and AMS yielding a compact conformation that differed from that seen after taurine binding. This is thought to be partially responsible for the different efficacies of these ligands. This study was performed meticulously, with compelling evidence provided supporting the authors' primary hypothesis.

The authors should consider defining what they mean by glycine being a "full agonist". In previous publications, they have argued that, since efficacy is a ratio of rates of transitions among different states of receptors, what anyone currently defines as a full agonist is in reality just the highest efficacy ligand discovered to date. There isn't any problem with the use of the term "full agonist" per se, since it is a concise way of comparing the high efficacy of glycine versus other ligands at the GlyR, but the reader would be served by having this clarified.

This is correct. We have changed “full agonist” into “highly efficacious” wherever possible (all tracked) and added in the introduction that we shall refer to glycine as a full agonist (Line 54). In the interest of conciseness, we have tried to keep this as light-handed as possible. A complete explanation of what a full agonist is would have to include various caveats such as the fact that it depends on the receptor isoform and that glycine itself becomes partial in loss-of-function hyperekplexia mutants.

Is there a qualitative rather than just a quantitative difference between high and low efficacy agonists at glycine receptors, in that only low efficacy compounds can interact with the loop B serine 174 residue and only high efficacy ligands yield compact binding pockets? In other words, should ligand efficacy be considered a continuum at the GlyR, or should it be considered more quantal in nature, with different agents occupying discrete categories? Explicitly addressing this issue would likely be of interest to the reader.

The reviewer raises a good point. In this receptor, differences in the size of the binding pockets with agonists of different efficacy was relatively small (see our reply to point 1 of reviewer #1). The numbers have been added to the text on lines 239 and following.

We did ask ourselves whether the interactions of the partial agonists with loop B could also make parts of the receptor more rigid, and thus reduce efficacy in a quantal fashion, but this is highly speculative at the moment. Answering this question will require the availability of more structures showing the receptor bound to other agonists, and possibly MD.

Author Response

Reviewer #1 (Public Review):

a) A "hidden gem" in the work is an exploration of whether lamotrigine directly enhances HCN function and finding it did not. While an important negative result, this was not demonstrated in native tissue, leaving the question open regarding direct effects on the native channel in neurons.

The point is well taken, and we have added this caveat in the relevant section (page 17).

b) One weakness of the study is the data from the set of experiments exploring impact of overexpression of the variants in neurons. This technique can be highly variable and the data interpretation in this case would benefit from more rigor.

It is indeed very difficult to rigorously compare expression patterns obtained using different viruses. To address the reviewer’s concerns, we carried out the following additional experiments and analyses:

i. We repeated the viral injection experiments using two different AAV serotypes for each series (HA-WT, HA-GD, and HA-MI in AAV2/8; HA-WT, HA-GD, and HA-MI in AAV2/9) to ensure that our results are reproducible and independent of virus preparation.

ii. We evaluated multiple independent injection sites in each series, ensuring that an adequate number of repetitions was executed under the same conditions (equal virus titer, injection volume, time before animal perfusion, tissue processing, and imaging).

iii. We presented our results in a series of new figures (Figure 7 and Figure 7 – figure supplements 1 and 2) with added panels showing equivalent vs. boosted laser intensities and gain conditions, where necessary, and parvalbumin protein counter-labeling for reference.

c) There are minor questions about statistical methods for comparing and concluding about the significance of differences between some experimental groups.

We have now added statistical analysis supporting all our comparisons and conclusions regarding differences between groups (please see the detailed response to Reviewer #1, Recommendations for the Authors, points g,j,l, and q).

d) An important conceptual gap remains unanswered by the study. Given the phenotypic similarities between patients with sequence variation in Na+ channel and HCN genes, as well as evidence of reduction of other channels or pumps in this case and the strong co-localization of Na+ channels and HCN channels in the PV+ neurons thought critical in the epilepsy of the HCN sequence variants, is it possible that Na+ channels are impacted as a secondary effect of HCN channel dysfunction here?

This is certainly a possibility, and indeed one that we very much favor. We have added a new analysis of AP morphology (Figure 5 – figure supplement 1) and performed a microarray-based experiment to screen for changes in Na+ channel expression (Source Data 1). While these experiments yielded negative results, they do not definitively rule out potential cell-type specific alterations in the function of Na+ channels or other conductances. A more thorough experimental examination of this important question will have to await future studies. We have added text to underscore how changes in other conductances may indeed impact neurons’ intrinsic properties in our mice (pages 10-11).

Reviewer #2 (Public Review):

a) It is not clear whether the mouse equivalent of the severe developmental disability seen in humans was present in mice.

We have added new behavioral experiments, which show impairment in some cognitive abilities in Hcn1GD/+ mice but not in Hcn1MI/+ mice, consistent with the more severe development disability observed in patients carrying the p.G391D variant compared to patients carrying the p.M153I variant (new Figure 3 and text on page 6 and 7).

b) (…) there is no demonstration of hyperexcitability at a cellular or network level, so we do not know how HCN1 mutation predisposes to seizures. In fact, hippocampal pyramidal neurons were shown to be hypoexcitable, at least to one method of action potential generation. There is a suggestion that parvalbumin-positive interneurons may be affected, but there is no evaluation of their excitability. It is possible that HCN1 mutation is directly causing neuronal hyperexcitability, but this would only be uncovered by studying HCN1 channel effects on pyramidal neuron dendrite excitability (where they are mostly localized); synaptic function; or on interneuron excitability. There is also no direct demonstration of the effects of channel mutation on HCN1-mediated current (Ih) in native neurons, so we cannot assess how channel biophysics is altered.

We agree with the Reviewer that there are indeed limitations to the interpretation of our study. Each of these important questions will need additional experimentation before they can be answered definitively. We have added text to underscore such limitations in the Results (pages 10 and 17) and Discussion (pages 20-21) sections. In future studies, we plan to evaluate both the excitability of interneurons through genetic labeling of PV+ cells and patch-clamp recordings, as well as evaluate their synaptic function. Voltage-clamp recordings in pyramidal neurons and possibly dendritic recordings may also be attempted. However, each of these lines of experimentation will require considerable time to complete, particularly because of the difficulty in obtaining patch-clamp recordings from hippocampal slices from the mouse mutants. So we ask that we be allowed to leave them to a future study.

Reviewer #3 (Public Review):

a) The authors characterize cerebellum-dependent functional deficits in the mutant mice, basing their studies on the high expression levels of HCN1 in cerebellum, citing Notomi & Shigemoto, They do not present phenotypic deficits in function ascribed to hippocampus or cortex. (…) Therefore, it should be excellent if the authors presented functional tests of hippocampus or cortex dependent behaviors, regardless of the outcome in Fig.2. At a minimum, they should modify the text and downplay the cerebellar emphasis.

Following the Reviewer’s helpful recommendations, we have added new behavioral experiments testing short-term and long-term memory (see new Figure 3) and modified the panels in Fig 2. The manuscript text has been revised accordingly (pages 6 and 7).

b) The authors base their proposed mechanism for the pro-epileptic effects of the mutation on the notion that HCN1 Channels are localized to axons only of PV interneurons. Whereas this fact may be true for the adult, during development, axonal targeting is not unique to basket-type interneurons. It is observed in the developing hippocampal circuit, in medial entorhinal cortex neurons innervating dentate gyrus granule cells, i.e., the perforant path. Have the authors looked at axonal targeting in this region in the mutant mice during appropriate developmental stages? Its absence might modulate the firing of GCs, specifically during development (Bender et al., J Neurosci 2007). At a minimum this point merits discussion, particularly in view of the developmental nature of the epilepsies described.

The Reviewer correctly points out that HCN1 channels are present not only in the axons of PV+ interneurons but also in the axons of certain subclasses of excitatory neurons (see Huang et al., 2011, 2012, and 2019). Regarding axons from medial entorhinal cortex neurons innervating dentate gyrus granule cells, i.e., the perforant path, there is an interesting difference between mice and rats. While HCN1 channel subunits at this site are downregulated in adult rats, they persist in adult mice. This can be seen in the immunostainings shown in Figure 5A (formerly 4A) of the manuscript. Similar to hippocampal PV+ axons in CA3 (Figure 7A, formerly 6A), it can be noted that HCN1 expression in the perforant path is considerably decreased in Hcn1GD/+ mice compared to wildtype and Hcn1MI/+ mice.

c) In this context, there are distinct developmental profiles for the 4 HCN subunits, including HCN1, and these profiles might contribute to age-specific defects leading to seizures. This point merits discussion.

We thank the reviewer for raising this important point and have added text underscoring the potential contribution of altered HCN1 channel function to brain development (page 19) to address this issue, and in accord with the comments raised by Reviewer #1 above (see point p).

d) Whereas the focus of this paper is on the role of genetic mutations in HCN1 in epilepsy, the paper may be enriched by being placed in the context of the overall contributions of HCN1 channels to human epilepsy, including "acquired epilepsy"" via potential epigenetic changes in the expression of normal HCN channels (Bender et al., 2003 and others).

We agree with the Reviewer and now refer to these datasets in the Introduction, citing the excellent review by Brennan et al., 2016 (page 4).

Author Response

Reviewer #1 (Public Review):

1) In the future it will be interesting to determine how these changes in the bone marrow relate to the different subsets or recruited macrophages present in obese tissues. For example, whether monocytes in the bone marrow preferentially generate CD9+Trem2+ Lipid associated macrophages recently described in obese adipose tissue (Jaitin et al, Cell, 2019) or if they are equally capable of generating monocyte-derived tissue resident macrophages in obese tissues.

We appreciate and concur with the Reviewer’s suggestion, as stated for future analysis, of how bone marrow monocytes compare with macrophages in adipose tissue. That is a long-term plan and will make the subject for a full new study of interest to the immunometabolism community. As preamble to that future study -and considering that Jaitin et al identified CD9 and Trem2 in lipid-laden macrophages- we have tentatively explored if bone marrow-derived macrophages (BMDM) from mice fed HFD and LFD differ in their expression of these markers. In these exploratory experiments, however, HFD did not statistically change the expression of either marker in the BMDM.

2) The main strength of this paper is in the identification of the changes in the monocyte subsets abundance early after feeding a HFD and in uncovering the metabolic changes in and between these two monocyte subsets in obese mice. One concern regarding the data as a whole is that, while the authors have nicely indicated the number of samples/mice in each figure, there is no mention of how many times each experiment was performed.

We have more explicitly and amply stated the number of times every experiment was performed and this information is also added to the figure legends.

Additionally, the inclusion of the different gating strategies used particularly for the first figures would be advantageous to fully appreciate the findings being presented. This is particularly relevant for the identification of the Ly6Chi and Ly6Clo BM monocytes.

We now present the gating strategy at the beginning of the Results as Figure 2 – figure supplement 1. In Figure 2 – figure supplement 1B, control flow experiments without anti-Ly6C or anti-Cd11b are shown gated for the Gr1(-) vs CD115(+) subset, confirming the proper positioning for the Ly6clo and Ly6chi gates. In Figure S1C, we illustrate the gating strategy shows that CX3CR1 segregates with the Ly6Clo sorted monocytes, and CCR2 segregates with the Ly6Chi, as expected. We hope that this complements the information on the identification of the Ly6Chi and Ly6Clo monocytes. In the future, a more complete analysis of the FACS-sorted Ly6Clo and Ly6Chi cells could be performed using RNAseq, which was however outside the realm of possibilities for this study.

3) The alternative explanation (to Ly6Clo conversion to Ly6Chi monocytes) could be that there are some progenitors remaining in these cultures that give rise to Ly6Chi monocytes following exposure to the conditions media. .. It is important to confirm that the sorted cells are a pure population of Ly6Clo monocytes with no contamination from progenitors that are also Ly6Clo

We appreciate the suggestion; to address this interesting possibility, in new experiments we used markers of myeloid progenitor cells (CD117+;Sca1-, followed by gating for CD16/32 vs. CD34 to identify GMP, CMP and MEP populations). The new findings show that GMP represent the majority of progenitors that are present in the FACS-identified Ly6Clo and Ly6Chi monocyte populations derived from complete bone marrow cells. In this analysis, we find the GMP are present at low abundance (ranging 140 GMP per 1000 Ly6Clo, in results from 3 separate mice). (NEW Figure 7E). This finding complements our original observation that there are relatively few progenitor cells in the in vitro-generated monocyte samples, detected by FACS analysis (Figure S5). Despite their relatively low abundance, we cannot discount that some could become Ly6Chi cells. However, the 18-hour duration of exposure of FACS-sorted Ly6Clo cells to WATA-CM would have allowed for only about one doubling event of precursor cells. If so, the progenitors could not fully account for the entirety of the change in proportion of Ly6Clo in favour of Ly6Chi.

Supporting this argument, when treating in vitro-generated monocytes with WATA-CM, the slight increase in CMP progenitors did not manifest as an increase in the downstream GMP progenitor numbers (now in Figure 7 – figure supplement 1), which are upstream of the Ly6C monocyte lineage.

To more directly explore the growth potential of progenitor cells, we have now used the Colony Forming Assay to determine the ability of progenitors to give rise to more differentiated monocyte precursor colonies upon incubation with the various conditioned media. In vitro-generated bone marrow-derived monocytes were exposed to control-, WATA- and BATA- CM, The new results, shown in the new Figure 7C,D, indicate that whereas white adipocyte media (WATA-CM) did not expand colonies from CMP (GEMM), GMP (CFU-G and CFU-M) or MEP (BFU-E) progenitors, brown adipocyte media (BATA-CM) slightly expanded colonies derived from CMP/GEMM and skewed GMP cell differentiation toward CFU-M (which lead to monocytes) from CFU-G (which lead to granulocytes and ‘neutrophil’ like monocytes, Yáñez et al, 2017). The new text on pages 15-16, lines 341-365 reads as follows:

“To buttress the above results, we also assessed the colony forming potential of in vitro-generated monocytes that received pre-treatment of WATA-CM or BATA-CM, to assess the potential for expansion of progenitor cells present in the samples. Colonies were identified as BFU-E (giving rise to erythroid cells); CFU-GEMM (giving rise to large mixed cultures of granulocyte, erythroid, macrophage, megakaryocyte; also, known as CMP); CFU-G (giving rise to granulocytes) or CFU-M (giving rise to macrophages). BATA-CM promoted growth of CMP/CFU-GEMM cultures over control Media ( p<0.01 Two-way ANOVA, Tukey’s multiple comparisons, Figure 7C) and biased granulocyte/macrophage progenitors (widely known as GMP) towards macrophage over granulocyte differentiation, relative to control Media ( p<0.01) or WATA-CM (p<0.05 or **p<0.001, Figure 7C). The total numbers of colonies that grew after 7-10 days of culturing of each pre-treated cohort of monocytes were not different across the three treatments, although trended upwards with BATA-CM (Figure 7D). These results indicated that while BATA-CM promoted expansion of selected populations (CMP/CFU-GEMM and CFU-M), consistent with the increase in BrdU incorporation shown above, WATA-CM was without effect relative to control Media. The above findings suggest that while the proportional increase in Ly6Clow monocytes induced by BATA-CM involves cell proliferation, the proportional increase in Ly6Chigh monocytes induced by WATA-CM does not. As a complementary approach, BM cells were analyzed by flow analysis for the presence of monocyte progenitors within the Ly6Clow or Ly6Chigh monocyte subsets. GMP progenitor cells were essentially the only progenitors detected by this approach in the Ly6Clow monocyte subset, and they represented 140 GMP per 1000 Ly6Clow cells (Figure 7E). During the incubation time of 18 h with conditioned medium, we anticipate the progenitors could theoretically undergo only one doubling and therefore unlikely to account for the full changes in Ly6Clow cell numbers produced by WATA-CM. Collectively, the results in Figures 7C-E indicate that WATA-CM treatment did not result in an appreciable expansion of progenitor cells or colony formation. Therefore, alternative mechanisms were explored that might contribute to the WATA-CM induced shift towards Ly6Chigh monocyte preponderance, particularly the possible conversion of one subset into the other.”

Altogether, we feel that these previous and new results do not endorse the possibility that the brunt of the Ly6Chi cells increase is due to progenitor differentiation in response to WATA-CM. We therefore lean towards the interpretation that Ly6Clo cells convert to Ly6Chi but agree that this potential mechanism will require further additional analysis in the future.

Author Response

Reviewer #2 (Public Review):

Taguchi et al. carried out a functional and structural analysis of microtubule dynamics inhibition by the C. elegans kinesin-4 KLP-12. The authors found that both the motor domain and the tail of KLP-12 are necessary to precisely control axon length in C. elegans. The authors showed that a minimal dimer of KLP-12 is motile along the microtubule lattice and reduces microtubule growth rate in vitro; further biochemistry assay demonstrated that the KLP-12 motor domain can similarly bind the microtubule lattice and free tubulin. The authors then solved the crystal structure of KLP-12 motor domain in complex with tubulin and compared their structure data with that of Kif5B (a motile kinesin that does not depolymerize microtubules) and Kif2C (not actively motile but depolymerizes microtubules). They found that the structure of KLP-12 is more similar to that of Kif5B than that of Kif2C, whereas the curvature of tubulin in complex with KLP-12 is between the curvatures of tubulin in complex with Kif5B and Kif2C. The high-resolution structural data from this study suggest how kinesin-4 can be motile along the microtubule lattice and at the same time stop the microtubule dynamics at its plus end; the mild effect of KLP-12 on protofilament bending may be crucial in enabling the inhibition of both the polymerization and depolymerization of the microtubules.

Overall, this is a very nice study, although some aspects of data analysis or interpretation need to be extended or clarified.

We sincerely appreciate the kind and fair evaluation of this reviewer.

1) Microtubule dynamics may be inhibited by reducing growth rate, inducing pausing, or altering catastrophe. To make their results more solid, the authors should examine whether KLP-12 impacts microtubule pausing and/or catastrophe. Such additional metrics may help strengthen the results and further the insight into the role of tubulin curvature in microtubule dynamics.

We thank this reviewer for the constructive suggestion. We evaluated each factor and found growth rate is the most affected but depolymerization rate was not significantly affected. The frequency of MT catastrophe events was slightly reduced (Figure 2G). This is similar to the result of KIF21A- or KIF5-bound microtubules suggesting the property is conserved in a broad range of kinesins. Frequency of rescue events was reduced as well (Fig 2I). One possibility is that KLP-12 suppresses microtubule polymerization. Another possibility is the indirect effect induced by reduced MT catastrophe events. We have included these in the result section (pages 8-9, line 187-204; Figure 2).

2) Structural comparison may be sensitive to the resolution of protein structures that are compared. The authors solved the crystal structure of KLP-12 at a resolution of 2.9 A, which is different from that of Kif4, Kif5B, or Kif2C from previous structure studies (1.7, 3.2, and 3.2 A). The values of root-mean-square distance between protein structures tend to increase if the two proteins that are being compared have been resolved at different resolutions. To strengthen their structural comparison results, the authors should account for the effect of different crystallographic resolutions on their root-mean-square distance evaluations.

We agree that the resolution of protein structures is important for the rmsd comparison. Thus, we have re-calculated the rmsd values for a fair comparison using the main chain residues (page 13, lines 310-312; Figure 4A).

3) Structural comparison may also be sensitive to what the proteins are in complex with. The authors solved the structure of KLP-12 that is in complex with GTP-tubulin, which may be different from the structure of KLP-12 that is free of tubulin, or in complex with GDP-tubulin. Previous studies had solved the structure of Kif4 which is free of tubulin (Chang et al 2013), and the structures of Kif5B (Gigant et al 2013) and Kif2C in the presence of GDP (Wang et al 2017). To strengthen their results, the authors should clarify how these differences between the previous and the current structural studies impact their structural comparison results.

As this reviewer suggested, the kinesin conformations are affected by the nucleotide state of the motor, by forming a complex with tubulin or microtubule, and the nucleotide state of tubulin or microtubule. Thus, we have compared the KLP-12–GTP-tubulin complex with available kinesin-4 structures, kinesin-1 structures, and kinesin-13 structure. These comparisons are shown in the revised Figure 4 and Figure4–supplement 1, demonstrating what is specific for KLP-12 or what is common among kinesin-4.

Author Response*

Reviewer 2 (Public Review):

1) The periodic components of the simulated power did not overlap as is often seen in empirical data, they were confined to 1-40 Hz (e.g. no gamma activity was simulated), and the simulations did not include a knee in the aperiodic component. This means that it Is unclear whether SPRiNT would work as well in more complex or excessively noisy datasets. The non-sinusoidal waveform shape of the periodic component in the rodent data reiterates this concern.

We are grateful that the Reviewer raised these important considerations about the practical value of SPRiNT in more complex data scenarios.

We wish to clarify that in the simulations reported, although two simultaneous periodic components would not share the same centre frequency, a substantial number of realizations of the simulations made these components overlap with centre frequencies separated by less than 5 Hz (6% of all simultaneously simulated peaks; n = 8166). We now provide an example of two overlapping spectral peaks in the revised version of Figure 3 – figure supplement 1C.

In preparing the revised manuscript, we also studied how the spectral overlap of periodic components would determine the peak detection rate: we found that the peak detection rate increases with the separation between two consecutive peaks along the frequency spectrum, but that it is independent of the presence of other peaks if they are at least 8 Hz apart from each other (Figure 3 – figure supplement 1D).

As correctly mentioned by the Reviewer, the original synthesized data did not comprise components beyond a maximum frequency of 40 Hz, nor did they include a knee in their aperiodic component. In the revised manuscript, we now report new results obtained from the analysis of 1000 synthesized time series that comprise two periodic components (including one periodic component between 30-80 Hz) and a knee in their aperiodic component (Figure 3 – figure supplement 2). The relevant additions to the Methods section are pasted below:

"We also simulated 1000 time series with aperiodic activity featuring a static knee (Figure 3 – figure supplement 2). Aperiodic exponents were initialized between 0.8-2.2 Hz-1. Aperiodic offsets were initialized between -8.1 and -1.5 a.u., and knee frequencies were set between 0 and 30 Hz. Within the 12-36 s time segment into the simulated time series (onset randomized), the aperiodic exponent and offset underwent a linear shift and a random magnitude in the range of -0.5 to 0.5 Hz-1 and -1 to 1 a.u., respectively. The duration of the linear shift was randomly selected for each simulated time series between 1 and 20 s; the knee frequency was constant for each simulated time series. We added two oscillatory (rhythmic) components (amplitude: 0.6-1.6 a.u.; standard deviation: 1-2 Hz) of respective peak centre frequencies between 3-30 Hz and between 30-80 Hz, with the constrain of minimum peak separation of at least 2.5 peak standard deviations. The onset of each periodic component was randomly assigned between 5-25 s, with an offset between 35-55 s. (Lines 773 to 784)"

We analyzed these data with SPRiNT within the 1-100 Hz frequency range. These new results indicate that SPRiNT performs in a satisfactory manner on data with components distributed over a broader frequency range, with a knee in their aperiodic component.

Below are the related edits to the revised Results section:

"SPRiNT did not converge to fit aperiodic exponents in the range [-5, 5] Hz-1 only on rare occasions (<2% of all time points). We removed these data points from further analysis. The simulated aperiodic exponents and offsets were recovered with MAEs of 0.22 and 0.42, respectively; static knee frequencies were recovered with a MAE of 3.55x104 (inflated by large outliers in absolute error; median absolute error = 11.72). Overall, SPRiNT detected the peaks of the simulated periodic components with 56% sensitivity and 99% specificity. The spectral parameters of periodic components were recovered with equivalent performances in the lower (3-30 Hz) and respectively, higher (30-80 Hz) frequency ranges: MAEs for centre frequency (0.32, resp. 0.32), amplitude (0,27, resp. 0.22), and standard deviation (0,35, resp. 0.29). (Lines 244 to 252)"

We also now discuss possible limitations in the Discussion:

"Finally, SPRiNT’s performances were slightly degraded when spectrograms comprised an aperiodic knee (Figure 3 – figure supplement 2). This is due to the specific challenge of estimating knee parameters. Nevertheless, the spectral knee frequency is related to intrinsic neuronal timescales and cortical microarchitecture (Gao et al., 2021), which are expected to be stable properties within each individual and across a given recording. Thus, we recommend estimating (and reporting) aperiodic knee frequencies from the power spectrum of the data with specparam, and specifying the estimated value as a SPRiNT parameter. (Lines 480 to 486)"

The Reviewer’s point on non-sinusoidal waveform shapes is also well taken, but we would like to emphasize that they challenge all current methods, including but not specific to SPRiNT or specparam (Donoghue et al., 2021). Indeed, SPRiNT and specparam perform a parametric decomposition of the spectrally transformed data, regardless of whether periodic components of a true sinusoidal nature are present. Non-sinusoidal periodic time series, such as the sawtooth waveforms observed in the rodent data analyzed in the manuscript, comprise spectral peaks as harmonic components (here of a theta-band fundamental rhythm). For this reason, we opted to focus our analyses and discussion of these data to the temporal dynamics of their aperiodic components.

2) Furthermore, the SPRiNT and specparam parameters were fixed and arbitrary, and it is unclear how robust the current results are with respect to changes in these parameters.

Here too, we appreciate the Reviewer’s insight and concern.

We explored a subset of the simulations with SPRiNT using alternative settings for STFT (Figure 2 – figure supplement 3) and observed overall satisfactory performances. We now report the relevant results in an addition to the Supplemental Materials, as pasted below:

"SPRiNT settings for higher temporal resolution (time range: 1-59 s, in 0.25 s steps; frequency range: 1-40 Hz, in 1 Hz steps) provided slightly larger estimation errors of exponent (MAE = 0.15) and offset (MAE = 0.20) relative to original settings (exponent, offset MAE = 0.11, 0.14, respectively). Alpha peaks were recovered with slightly lower sensitivity (98% at time bins with maximum peak amplitude; original 99%) and specificity (9% spurious detections; original 4%), and with greater errors in centre frequency (MAE = 0.43), amplitude (MAE = 0.24), and bandwidth (MAE = 0.53) compared to original settings (centre frequency, amplitude, bandwidth MAE = 0.33, 0.20, 0.42, respectively). Down-chirping beta oscillations were detected with lower sensitivity (93% sensitivity at time bins with maximum peak amplitude, original 98%; 86% specificity, original 98%), and with greater errors in centre frequency (MAE = 0.57), amplitude (MAE = 0.22), and bandwidth (MAE = 0.57) compared to original settings (centre frequency, amplitude, bandwidth MAE = 0.43, 0.17, 0.48, respectively). SPRiNT settings for higher frequency resolution (time range: 2-58 s, in 0.5 s steps; frequency range: 1-40 Hz, in 0.5 Hz steps) provided comparable estimation errors of exponent (MAE = 0.13) and offset (MAE = 0.16) relative to original settings (exponent, offset MAE = 0.11, 0.20, respectively). Alpha peaks were recovered with similar sensitivity (99% at time bins with maximum peak amplitude; original 99%) but lower specificity (21% spurious detections; original 4%), and with comparable errors in centre frequency (MAE = 0.35), amplitude (MAE = 0.23), and bandwidth (MAE = 0.41) to original settings (centre frequency, amplitude, bandwidth MAE = 0.33, 0.20, 0.42, respectively). Down-chirping beta oscillations were detected with comparable sensitivity (99% sensitivity at time bins with maximum peak amplitude, original 98%) but lower specificity (78%, original 98%), and with greater errors in centre frequency (MAE = 0.50), amplitude (MAE = 0.21), and bandwidth (MAE = 0.59) relative to original settings (centre frequency, amplitude, bandwidth MAE = 0.43, 0.17, 0.48, respectively). (Lines 1190 to 1213)"

We now provide in the Discussion practical recommendations for setting the methods parameters, which will depend on the specific objectives of a given study. We saw the rationale for the settings used in the manuscript as guidelines to future users. We believe the specific recommendations added will be of greater practical value of the manuscript.

Reviewer 3 (public Review):

1) Based on the simulated data, SPRiNT seems to be very efficient and robust, and it is also superior to the wavelet-specparam approach. However, while the simulations are very extensive, I find that they are constructed in a manner that may induce biases as the comparison is conducted between SPRiNT and a single, fixed wavelet-based approach. Like any spectral analysis technique, wavelets possess their own trade-off between temporal and frequency resolutions. As the wavelet analyses are conducted using a fixed set of parameters, it may be that some of the differences between the methods stem from how well they are suited for detecting the simulated activity that is constructed using a certain standard deviation of their oscillatory frequencies. It would be valuable to evaluate whether changing the wavelet-analysis parameters or the width of the simulated oscillations would change how the alternative methods compare. It is of course clear that the STFT based approach would remain computationally superior, but it would be interesting to see whether the other differences would remain as robust after the above more detailed evaluation of the methods. Related to the method comparison, it also appears that the outlier removal within SPRiNT markedly improves the quantification of the periodic components. This matter could be discussed more within the manuscript.

We appreciate the concerns expressed by this Reviewer regarding our choice of wavelet parameters.

To respond to the concerns expressed, we have performed new analyses with the wavelet-specparam approach with a diversity of alternative time-frequency resolutions: FWHM of 2s at 1 Hz, and FWHM of 4s at 1 Hz (Figure 2 – Figure supplement 2).

The changes observed remain qualitatively moderate, and the performances below those obtained with SPRiNT. The new results are displayed in Figure 2 – figure supplement 2 and described in the following revisions to Supplemental Materials:

"Wavelet settings of finer resolution in time and coarser in frequency (time range: 3-57 s, in 0.005 s steps; central frequency = 1 Hz, FWHM = 2 s; frequency range: 1-40 Hz, in 1 Hz steps) yielded lower estimation errors of exponent (MAE = 0.12) and offset (MAE = 0.35) compared to original settings (exponent, offset MAE = 0.19, 0.78). Alpha peaks were recovered with higher sensitivity (97% at time bins with maximum peak amplitude, original 95%) and specificity (32% spurious detections, original 47%), although with greater errors in centre frequency (MAE = 0.61), amplitude (MAE = 0.25), and bandwidth (MAE = 0.94) compared to original settings (centre frequency, amplitude, bandwidth MAE = 0.41, 0.24, 0.64, respectively). Down-chirping beta oscillations were detected with lower sensitivity (29% sensitivity at time bins with maximum peak amplitude, original 62%) but higher specificity (97%, original 90%), and with greater errors in centre frequency (MAE = 0.63), amplitude (MAE = 0.17), and bandwidth (MAE = 1.59) relative to original settings (centre frequency, amplitude, bandwidth MAE = 0.58, 0.16, 1.05, respectively). When wavelet settings prioritized resolution in frequency over time (time range: 4-56 s, in 0.005 s steps; central frequency = 1 Hz, FWHM = 4 s; frequency range: 1-40 Hz, in 1 Hz steps) relative to original settings, the errors in estimates of exponent (MAE = 0.16) and offset (MAE = 0.47) parameters were reduced (original exponent, offset MAE = 0.19, 0.78, respectively). Alpha peaks were recovered with higher sensitivity (99% at time bins with maximum peak amplitude, original 95%) and similar specificity (46% spurious detections, original 47%), although with larger errors in centre frequency (MAE = 0.33), amplitude (MAE = 0.20), and bandwidth (MAE = 0.43) compared to original settings (centre frequency, amplitude, bandwidth MAE = 0.41, 0.24, 0.64, respectively). In contrast, down-chirping beta oscillations were detected with slightly higher sensitivity (79% at time bins with maximum peak amplitude, original 62%) and specificity (91%, original 90%), and with lower errors on centre frequency (MAE = 0.37), amplitude (MAE = 0.14), and bandwidth (MAE = 0.71) compared to original settings (centre frequency, amplitude, bandwidth MAE = 0.58, 0.16, 1.05, respectively). (Lines 1155 to 1179)"

We now discuss the outlier peak removal process and its benefits/drawbacks more extensively in the revised Discussion. The relevant section is pasted below:

"SPRiNT’s optional outlier peak removal procedure increases the specificity of detected spectral peaks by emphasizing the detection of periodic components that develop over time. This feature is controlled by threshold parameters that can be adjusted along the time and frequency dimensions. So far, we found that applying a semi-conservative threshold for outlier removal (i.e., if less than 3 more peaks are detected within 2.5 Hz and 3 s around a given peak of the spectrogram) reduced the false detection rate by 50%, without affecting the true detection rate substantially (a <5% reduction; Figure 3 and Figure 3 – figure supplement 3). Setting these threshold parameters too conservatively would reduce the sensitivity of peak detection. (Lines 487 to 494)"

2) As for the investigation of real data, there are a few aspects that in my opinion could be investigated more thoroughly. Based on the findings it appears that the fine-grained time-resolved parametrization yields added value, especially in eyes-open rest where the fluctuation of alpha center frequency dissociates the different age groups, whereas the other time-resolved findings are not as unambiguously supportive of the need for fine-grained time-resolved analysis. Regarding the first point (fluctuation of alpha center frequency), the finding that the amount of fluctuation within the alpha frequency is distinct across age groups is very interesting. On the methodological, an open question is whether SPRiNT is required for making this observation. That is, is this effect observed only when applying the specparam-based parametrization (and outlier removal) after STFT or would the same observation have been made simply by estimating the fluctuations directly from the STFT based spectral estimates? As for using SPRiNT to determine the properties of aperiodic activity, presently it is not clear whether the approach yields added value compared to the more direct use of specparam. That is, the present findings show that the mean aperiodic slope dissociates both different age groups and resting-state conditions (eyes-open vs. -closed). It would be appropriate to test whether the same observation would be made by using specparam in the more standard way by first obtaining one spectral estimate across the whole one-minute time windows and then parametrizing this estimate. This type of testing would yield insights into whether there is a difference between SPRiNT that builds on dynamic but noisier spectral estimates and that allows the outlier removal and the standard approach benefiting from more stable spectral estimates for the present data and possibly for other questions. As for the rodent movement data, the evidence is clear that the aperiodic exponent differs between resting and movement state. However, the fundamental meaning of the change of the exponent at transition points is not explored. Does this change simply reflect the speed of the animal/amount of movement that changes across the time period prior and post rest and movement onsets? That is, does the transition curve align with the movement curve or does it represent something more complex? This aspect could be evaluated and discussed more extensively. Together, the above additional evaluations would be beneficial for determining whether there is value in looking at aperiodic activity in a time-resolved manner and whether a fine-grained analysis is needed or would a more static analysis takes into account the fact tasks/states fare equally or even in a superior manner.

We appreciate all concerns raised here by the Reviewer. We intended to report that age-related changes of spectral features in healthy aging (Cellier et al., 2021; Donoghue et al., 2020; Hill et al., 2022; Ostlund et al., 2022; Schaworonkow & Voytek, 2021) can be replicated using summary statistics of SPRiNT outcomes. Our intention was not to showcase these effects as novel. To clarify our purpose and the novelty in the proposed approach, we have revised Figure 4 accordingly and now emphasize the genuine novel aspects of our findings from the time-resolved parameterization of the spectrogram.

We further investigated the benefits of using SPRiNT to detect age-related changes in the temporal variability of alpha-peak frequency. Using STFT, we replicated the same effect trends whereby older individuals exhibit greater temporal variability of alpha-peak frequency. One asset from the SPRiNT approach is the interpretability of the effect because it detects genuine peak components in the spectrogram and correct their parameters from possible confounds from concurrent aperiodic components. Individual alpha peak frequency derived from STFT is based on instantaneous fluctuations of signal power in the alpha band, regardless of the actual presence of a periodic component.

As for apparent discrepancies between the SPRiNT and specparam outcomes, we found that only the specparam-derived alpha amplitude, not SPRiNT’s, was predictive of age group. Please see our response to Reviewer 1’s first comment for a detailed interpretation of this outcome.

Concerning the rodent data, we followed this Reviewer’s suggestion of determining whether aperiodic exponent was related to movement speed at the transitions between movement and rest (and vice versa). Indeed, we found that variability in aperiodic exponent proximal to transitions between movement and rest was partially explained by instantaneous movement speed (see Figure 5 – figure supplement 3). Below, we have revised the Results and Discussion sections accordingly:

"We tested whether changes in aperiodic exponent proximal to transitions of movement and rest were related to movement speed and found a negative linear association in both subjects for both transition types (EC012 transitions to rest: β = -9.6x10-3, SE = 4.7x10-4, 95% CI [-1.1x10-2 -8.6x10-3], p < 0.001, R2 = 0.29; EC012 transitions to movement: β = -7.3x10-3, SE = 4.3x10-4, 95% CI [-8.1x10-3 -6.4x10-3], p < 0.001, R2 = 0.18; EC013 transitions to rest: β = -1.1x10-2, SE = 2.3x10-4, 95% CI [-1.2x10-2 -1.1x10-2], p < 0.001, R2 = 0.32; EC013 transitions to movement: β = -1.2x10-2, SE = 3.2x10-4, 95% CI [-1.3x10-2 -1.2x10-2], p < 0.001, R2 = 0.26; Figure 5 – figure supplement 3). (Lines 403-410)"

Changes in aperiodic exponent were partially explained by movement speed (Figure 5 – figure supplement 3), which could reflect increased processing demands from additional spatial information entering entorhinal cortex (Keene et al., 2017) or increased activity in cells encoding speed directly (Iwase et al., 2020). (Lines 556-560)

Author Response

Reviewer #1 (Public Review):

Although a bunch of studies have been carried out to see whether calcium supplementation is a prerequisite for the promotion of bone health or prevention of bone diseases, this is the first trial to see its effect on the population whose age is reaching peak bone mass. Outcomes are clear and justified by sound methodology. Also, the message from this systematic review could directly influence the clinical decision on who might gain benefit from calcium supplementation.

We are very grateful for your considerate comments and your recognition of our work in this study. Your suggestions really helped us to improve the clarity of this manuscript.

Strengths of this study are:

1) This is the first systematic review by meta-analysis to focus on people at the age before achieving peak bone mass (PBM) and at the age around the PBM. 2) Detailed subgroup and sensitivity analyses drew consistent and clear results.

Thank you very much for your comments. We are very grateful for your recognition of our work in this study.

Limitations of this study are:

1) Substantial intertrial heterogeneity should be considered in terms of dose effect of calcium supplementation and differences between both sexes etc.

Thank you very much for your kind comments. We performed subgroup analyses to explore whether different doses of calcium supplementation had different effects, and the results are showed in Table 4a and 4b at the end of this Author Response. The results showed that the intertrial heterogeneity in the subgroup with doses of calcium supplementation greater than or equal to 1000 mg/day was significantly smaller than that in the subgroup with doses less than 1000 mg/day, suggesting that different doses of calcium supplementation across trials may be a potential source of the substantial intertrial heterogeneity.

Similarly, we also performed subgroup analyses by sexes. Of all included trials, 23 trials focused on women only, and 20 trials involved both men and women participants, however these 20 trials did not report the results for men or women separately. We therefore divided the included trials into two subgroups: trials with women only and trials with both men and women. The corresponding results of subgroup analyses are showed in Table 5a and 5b at the end of this Author Response. The results showed that the subgroup with both men and women seemed to have less heterogeneous than the subgroup with women only, suggesting that sex may be a possible source of the observed heterogeneity.

In addition, we were also aware of the large heterogeneity between trials and explored the possible sources through several additional approaches. Firstly, instead of using fixed-effects models, we have chosen random-effects models to summarize the effect estimates. Secondly, we performed meta-regression analyses by age, population regions, calcium doses, baseline intake and sample sizes to explain the intertrial heterogeneity. The results of meta-regression are provided in Table 6 at the end of this Author Response. The results suggested that this heterogeneity could be explained partially by differences in regions of participants.

We have updated the results and discussions about potential sources of heterogeneity in the revised manuscript, as follows:

In general, the heterogeneity between trials was obvious in the analysis for BMD (P<.001, I2=86.28%) and slightly smaller for BMC (P<.001, I2=79.28%). The intertrial heterogeneity was significantly distinct across the sites measured. Subgroup analyses and meta-regression analyses suggested that this heterogeneity could be explained partially by differences in age, duration, calcium dosages, types of calcium supplement, supplementation with or without vitamin D, baseline calcium intake levels, sex and region of participants. (See Lines 293-298 on Page 20 in the Main Text)

Several limitations need to be considered. First, there was substantial intertrial heterogeneity in the present analysis, which might be attributed to the differences in baseline calcium intake levels, regions, age, duration, calcium doses, types of calcium supplement, supplementation with or without vitamin D and sexes according to subgroup and meta-regression analyses. To take heterogeneity into account, we used random effect models to summarize the effect estimates, which could reduce the impact of heterogeneity on the results to some extent. (See Lines 394-399 on Page 24 in the Main Text)

2) Rarity of RCTs focused on the 20-35-year age group.

Thank you very much for raising this point. We have comprehensively searched databases for eligible studies and found only three RCTs (Islam et al; Barger-Lux et al; Winters-Stone et al) focused on the 20-35-year age group. We did notice this fact as well. Because of this, we intend to perform a randomised controlled trial to evaluate the effects of calcium supplementation in this age group. In fact, this trial has already been started and is currently ongoing (Registration number: ChiCTR2200057644, http://www.chictr.org.cn/showproj.aspx?proj=155587).

In this open-label, randomized controlled trial, we will randomly assign (1:1) 116 subjects (age 18-22 years) to receive either or not calcium supplementation with milk (500 mL/day, contains about 500 mg/d calcium) for 6 months. The primary outcomes are bone mineral density and bone mineral content at the lumbar spine, femoral neck and total hip. The secondary outcomes are clinical indicators related to bone health, such as serum osteocalcin, bone-specific alkaline phosphatase, urinary deoxypyridinoline, etc. We will conduct the current trial with great care and diligence and look forward to the results of this trial.

Reviewer #2 (Public Review):

This systematic review and meta-analysis titled 'The effect of calcium supplementation in people under 35 years old: A systematic review and meta-analysis of randomized controlled trials' provide good evidence for the importance of calcium supplementation at the age around the plateau of PBM. The statistical analyses were good overall and the manuscript was generally well written.

We are very grateful for your considerate comments and for your recognition to our work in this study. Your suggestions really helped us to improve the clarity of this manuscript.

One concern in this study is that RCTs included were substantially heterogenous in subjects, calcium types, duration, vitamin D supplements, etc. According to the inclusion criteria, RCTs with calcium or calcium plus vitamin D supplements with a placebo or no treatment were included in this study. However, no information about vitamin D supplementation was provided. Therefore, it seems unclear whether the effect of improving BMD or BMC is due to calcium alone or calcium plus vitamin D.

We are extremely grateful for your great patience and for your kind suggestions. According to your suggestions, we have added the corresponding analyses regarding calcium supplementation with or without vitamin D supplementation. Among the included RCTs, 32 trials used calcium-only supplementation (without vitamin D supplementation) and 11 trials used calcium plus vitamin D supplementation. The detailed information are provided in the Table 1 and 2 at the end of this Author Response. We have added subgroup analyses by vitamin D supplementation as you suggested, and the corresponding results are provided in Table 3a and 3b at the end of this Author Response.

When we pooled the data from the two subgroups separately, we found that calcium supplementation with vitamin D had greater beneficial effects on both the femoral neck BMD (MD: 0.758, 95% CI: 0.350 to 1.166, P < 0.001 VS. MD: 0.477, 95% CI: 0.045 to 0.910, P = 0.031) and the femoral neck BMC (MD: 0.393, 95% CI: 0.067 to 0.719, P = 0.018 VS. MD: 0.269, 95% CI: -0.025 to 0.563, P = 0.073) than calcium supplementation without vitamin D. However, for both BMD and BMC at the other sites (including lumbar spine, total hip, and total body), the observed effects in the subgroup without vitamin D supplementation appeared to be slightly better than in the subgroup with vitamin D supplementation. Therefore, these results suggested that calcium supplementation alone could improve BMD or BMC, although additional vitamin D supplementation may be beneficial in improving BMD or BMC at the femoral neck.

We have added relevant parts in the main text of the revised manuscript. (See Lines 258-263 on Pages 12-13 and Lines 367-374 on Page 23 in the Main Text)

As you mentioned, there exists large intertrial heterogeneity in this study, for which we compulsorily chose the random effect model, which was appropriate to get more conservative results. In addition, we did meta-subgroup analyses by calcium dose, sex, age, duration, regions, baseline calcium intake, types of calcium supplements, in order to explore possible sources of heterogeneity.

The results of subgroup analyses by dose of calcium supplementation are showed in Table 4a and 4b at the end of this Author Response. For both BMD and BMC at the lumbar spine and whole body, the intertrial heterogeneity was significantly smaller in the subgroup with a calcium supplementation dose greater than or equal to 1000 mg/day than that in the subgroup with a calcium supplementation dose less than 1000 mg/day, suggesting that different doses of calcium supplementation may be a potential source of the heterogeneity.

The results of subgroup analyses by sex are showed in Table 5a and 5b at the end of this Author Response. The intertrial heterogeneity was significantly smaller in the subgroup with both men and women than that in the subgroup with women only, also suggesting that sex could be a possible source of the heterogeneity.

The results of subgroup analyses by age (pre-peak VS. peri-peak ) are showed in Table 7a and 7b at the end of this Author Response. The intertrial heterogeneity was significantly smaller in the peri-peak subgroup than that in the pre-peak subgroup, also suggesting that age may be a potential source of the heterogeneity.

The results of subgroup analyses by intervention duration (pre-peak VS. peri-peak ) are showed in Table 8a and 8b at the end of this Author Response. For both BMD and BMC at the lumbar spine and total hip, the intertrial heterogeneity was smaller in the subgroup with a intervention period less than 18 months than that in the subgroup with a intervention period greater than or equal to 18 months, suggesting that intervention duration might be a potential source of the heterogeneity.

Table 9a and 9b at the end of this Author Response showed the results of subgroup analyses by population region. The intertrial heterogeneity was significantly smaller in the Asian subgroup than that in the Western subgroup, also suggesting that population region may be a source of the heterogeneity.

Table 10a and 10b at the end of this Author Response showed the results of subgroup analyses by dietary calcium intake levels at baseline. The intertrial heterogeneity was smaller in the subgroup with the dietary calcium intake level greater than or equal to 714 mg/day than that in the subgroup with the dietary calcium intake level lower than 714 mg/day, also suggesting that dietary calcium intake levels at baseline could be a potential source of the heterogeneity.

Table 11a and 11b at the end of this Author Response showed the results of subgroup analyses by types of calcium supplements. For both BMD and BMC at the lumbar spine, the intertrial heterogeneity was smaller in the subgroup with calcium supplementation than that in the subgroup with dietary calcium, also suggesting that types of calcium supplements might be a source of the heterogeneity.

In conclusion, the observed heterogeneity might be due to the differences in sex, age, regions of subjects, doses, intervention duration, and types of calcium supplementation, dietary calcium intake levels at baseline, and with or without vitamin D supplementation. We have updated the discussion on heterogeneity in the revised manuscript. (See Lines 394-397 on Pages 24 in the Main Text)

Thanks again for your comments, we have tried to analyze and explain the large heterogeneity through a variety of approaches, however, there may still remain some inadequacies. Please tell us directly if it needs further corrections, we will be very grateful and appreciate it, and try our best to revise this part of heterogeneity.

Reviewer #3 (Public Review):

This paper will be welcome for clinicians and researchers related to the field. The authors, applying a well-structured meta-analysis, showed that calcium supplementation or calcium intake during 20-35 years is better than the <20 years. The clinical impact is directly associated with improving the bone mass of the femoral neck, and thus proposes a window of intervention for osteoporosis treatment. The manuscript is very well prepared and represents a thorough analysis of available randomized controlled clinical trials, but a few issues require additional consideration.

We are very grateful for your considerate comments and for your recognition to our work in this study. Your comments are invaluable and have been very helpful in revising and improving our manuscript.

After a careful read of the literature, it is important to highlight that the paper is a statistically robust study with a well-delineated meta-analysis of youth-adult subjects. But, I would like better to understand why the authors didn't use other datasets such as WHO Global Index Medicus (Index Medicus for Africa, the Eastern Mediterranean Region, South-East Asia, and Western Pacific, and Latin America and the Caribbean Literature on Health Sciences, Index Medicus), ClinicalTrials.gov, and the WHO ICTRP.

Thank you so much for your thoughtful advice and your generosity in recommending these datasets to us. Based on your advice, we thoroughly searched these databases (the detailed search terms are provided in the Appendix File at the end of this Author Response). We have identified 23 potentially related studies and registered trials in these databases. After careful screening and review, however, no new studies were ultimately included in this meta-analysis. Some studies, which had not been completed, are recruiting subjects, and some studies were duplicates of the RCTs we had included. Finally, no new additional trials were included in our meta-analysis. The detailed screening process and the reasons for exclusion are showed in Figure 1. These three additional global databases will provide us with more comprehensive information for our future studies, thank you very much for your suggestions and guidance.

Figure 1. Flow chart of search and selection

References: 1. ID: emr-156089 (https://pesquisa.bvsalud.org/gim/resource/en/emr-156089) 2. ID: wpr-270003 (https://pesquisa.bvsalud.org/gim/resource/en/wpr-270003) 3. ID: lil-243754 (https://pesquisa.bvsalud.org/gim/resource/en/lil-243754) 4. ID: sea-23757 (https://pesquisa.bvsalud.org/gim/resource/en/sea-23757) 5. ID: NCT00067925 (https://clinicaltrials.gov/ct2/show/NCT00067925?term=NCT00067925&draw=2&rank=1) 6. ID: NCT00979511 (https://clinicaltrials.gov/ct2/show/NCT00979511?term=NCT00979511&draw=2&rank=1) 7. ID: NCT00065247 (https://clinicaltrials.gov/ct2/show/NCT00065247?term=NCT00065247&draw=2&rank=1) 8. Matkovic V, Landoll JD, Badenhop-Stevens NE, et al. Nutrition influences skeletal development from childhood to adulthood: a study of hip, spine, and forearm in adolescent females. J Nutr. 2004;134(3):701S-705S. doi:10.1093/jn/134.3.701S 9. Barger-Lux MJ, Davies KM, Heaney RP. Calcium supplementation does not augment bone gain in young women consuming diets moderately low in calcium. J Nutr. 2005;135(10):2362-2366. doi:10.1093/jn/135.10.2362 10. Cornes R, Sintes C, Peña A, et al. Daily Intake of a Functional Synbiotic Yogurt Increases Calcium Absorption in Young Adult Women. J Nutr. 2022;152(7):1647-1654. doi:10.1093/jn/nxac088 11. ID: NCT00063011 (https://clinicaltrials.gov/ct2/show/NCT00063011?term=NCT00063011&draw=2&rank=1) 12. ID: NCT00063024 (https://clinicaltrials.gov/ct2/show/NCT00063024?term=NCT00063024&draw=2&rank=1) 13. ID: NCT01857154 (https://clinicaltrials.gov/ct2/show/NCT01857154?term=NCT01857154&draw=2&rank=1) 14. ID: NCT00067600 (https://clinicaltrials.gov/ct2/show/NCT00067600?term=NCT00067600&draw=2&rank=1) 15. ID: NCT00063037 (https://clinicaltrials.gov/ct2/show/NCT00063037?term=NCT00063037&draw=2&rank=1) 16. ID: NCT00063050 (https://clinicaltrials.gov/ct2/show/NCT00063050?term=NCT00063050&draw=2&rank=1) 17. ID: TCTR20190624002 (https://trialsearch.who.int/Trial2.aspx?TrialID=TCTR20190624002) 18. ID: JPRN-UMIN000024182 (https://trialsearch.who.int/Trial2.aspx?TrialID=JPRN-UMIN000024182) 19. ID: NCT02636348 (https://trialsearch.who.int/Trial2.aspx?TrialID=NCT02636348) 20. ID: ACTRN 12612000374864 (https://trialsearch.who.int/Trial2.aspx?TrialID=ACTRN12612000374864) 21. ID: NCT01732328 (https://trialsearch.who.int/Trial2.aspx?TrialID=NCT01732328) 22. ID: ISRCTN28836000 (https://trialsearch.who.int/Trial2.aspx?TrialID=ISRCTN28836000) 23. ID: ISRCTN84437785 (https://trialsearch.who.int/Trial2.aspx?TrialID=ISRCTN84437785)

We have also updated the literature search section and the flow chart in the main text of the revised manuscript, as follows:

We applied search strategies to the following electronic bibliographic databases without language restrictions: PubMed, EMBASE, ProQuest, CENTRAL (Cochrane Central Register of Controlled Trials), WHO Global Index Medicus, Clinical Trials.gov, WHO ICTRP, China National Knowledge Infrastructure and Wanfang Data in April 2021 and updated the search in July 2022 for eligible studies addressing the effect of calcium or calcium supplementation, milk or dairy products with BMD or BMC as endpoints. (see Lines 80-85 on Page 5 and Figure 1 in the Main Text)

The manuscript compares two sources of participants (in line 233) evaluating the effect of improvements on the femoral neck being "obviously stronger in Western countries than in Asian countries". But, I didn't identify if the searches were conducted applying language restrictions. This is important because we can be considering the entire world or specific countries.

We are extremely grateful for your great patience and for your kind suggestions. We did not apply any language restrictions during the search process, as documented in the protocol of PROSPERO (CRD42021251275, https://www.crd.york.ac.uk/prospero/display_record.php?RecordID=251275). Following your suggestion, we have added a description of this in the revised manuscript. (See Lines 80-81 on Page 5 in the Main Text)

During the search process, we did identify five eligible articles from the Chinese databases including China National Knowledge Infrastructure (CNKI, https://www.cnki.net) and WanFang Data (https://www.wanfangdata.com.cn). However, we confirmed that these five studies were duplicates of the articles from the PubMed (PMID: 15230999; PMID: 17627404; PMID: 18296324; PMID: 20044757; PMID: 20460227). For those possibly relevant studies published in other languages than Chinese or English, the full text was downloaded and translated using DeepL translation website (https://www.deepl.com/translator) and then carefully reviewed. Ultimately, all included studies that met the inclusion and exclusion criteria were published in English. In view of this, after a systematic and comprehensive search, especially with the addition of your suggested databases, we could assume that our current study has incorporated all original researches in this field worldwide, rather than only from specific countries or regions.

To explore whether the effects of calcium supplementation differ across different population regions, we performed subgroup analyses. Prior to the analysis, we hypothesized that the effect might be slightly better, or at least not worse, in populations with lower baseline dietary calcium intakes (lower baseline BMD/BMC levels) than that in populations with higher baseline dietary calcium intakes (higher baseline BMD/BMC levels). However, the results showed that the improvement effects on BMD at the femoral neck and total body and BMC at the femoral neck and lumbar spine were obviously stronger in Western countries than in Asian countries. These findings are likely to be contrary to our common sense, which is, that under normal circumstances, the effects of calcium supplementation should be more obvious in people with lower calcium intakes than in those with higher calcium intakes. Therefore, this issue needs to be tested and confirmed in future trials.

The manuscript does not describe which version was used with the RoB tool.

Thank you for your suggestion. As you mentioned, we completed the description of RoB tool in the Methods section, as follows:

The quality of the included RCTs was assessed independently by two reviewers (SYL, HNJ) based on the Revised Cochrane Risk-of-Bias Tool for Randomized Trials (RoB 2 tool, version 22 August 2019), and each item was graded as low risk, high risk and some concerns. (See Lines 101-103 on Page 6 in the Main Text)

Figures and Supplementary: No critique.

Thanks for your kind comments and for your recognition to our work in this study.

Appendix 1

Search strategy • WHO Global Index Medicus:

(tw:(calcium)) OR (mj:(calcium)) OR (tw:(calcium carbonate)) OR (tw:(calcium citrate)) OR (tw:(calcium pills)) OR (tw:(calcium supplement)) OR (tw:(Ca2)) OR (tw:(dairy product)) OR (tw:(milk)) OR (tw:(yogurt)) OR (tw:(cheese)) OR (tw:(dietary supplement)) AND (tw:(bone density)) OR (tw:(bone mineral density)) OR (tw:(bone mineral content))

• ClinicalTrials.gov

(calcium) OR (calcium supplementation) OR (milk) OR (dairy product) OR (yogurt) OR (cheese) Applied Filters: Interventional (clinical trial); Child (birth–17); Adult (18–64)

• WHO ICTRP

(calcium) OR (milk) OR (dairy) OR (yogurt) OR (cheese) in the Intervention

Author Response

Reviewer #2 (Public Review):

The authors explored if and how Piezo1 regulated mechanical stiffness and inflammatory signals, thereby directing the differentiation of TH1 and Treg cells in cancer. They showed the genetic deletion of Piezo1, a mechanosensory ion channel, in dendritic cells, promoted tumor growth in a mouse model. Piezo1ΔDC mice showed an increase in Tregs and a decrease in IFNg+ Th1 cells in the MC38 tumor tissue. They showed TGFbR2-pSmad3 and IL-12Rb2-pStat4 signaling axis were involved in this process. Moreover, they suggested cooperation between Piezo1-SIRT1-HIF1a-glycolysis metabolism pathway and calcium-Piezo1-calcineurin-NFAT signaling pathway in DCs.

The authors have never directly tested the relationship between Piezo1 and DC stiffness. The authors claimed that "Piezo1 integrates innate inflammatory signals and mechanical stiffness signals". But what they showed were independent experiments of inflammatory stimulus (LPS) or stiffness stimulus (50kPa hydrogel). Do these two stimuli work together to induce Piezo1 signaling and contribute to Piezo-mediated differentiation of Th1 and Treg cells?

Following the reviewer’s suggestions and comments, we included the new data showing that different stiffness conditions or/and LPS can change Piezo1 expression in human DC cells (Fig. 7C). Accordingly, we also the revised the title and text and added the discussions in the revised manuscript.

Author Response

Reviewer #1 (Public Review):

The tools and approaches in this manuscript are of broad interest, not only to protein engineers but also to the many researchers using genome-editing reagents. However, putting the work in the context of previous research, both through changing the writing and additional experiments, will be critical for taking advantage of that widespread applicability.

Strengths:

Overall, the data support the conclusions of the manuscript.

The most exciting product of this work is an engineered nuclease, Nsp2-SmuCas9, that has high activity and specificity in human cells and a relaxed PAM preference for a single C base. This chimeric enzyme can efficiently induce indels at endogenous sites. While other works have presented nucleases with minimal PAM preferences, Nsp2-SmuCas9 is a useful alternative and may be preferred. It is also more compact than the standard SpCas9, making it appealing for gene therapy applications.

Technologically, the presented approach of screening orthologs for new specificities and making chimeras to achieve further diversity is a good way to develop new genome-editing reagents. The authors used appropriate methods, such as GUIDE-seq, to complete their goals. Extending beyond the GFP-activation assay to determine activity at endogenous targets enhanced the value of the results.

Conceptually, it was important information to the field that proteins with very high sequence identity (93%) can have divergent PAM preferences. Through their engineering, the authors clearly demonstrate the advantage of characterizing such close orthologs with diverse amino acids in the area of PAM recognition.

Weaknesses:

1) An overall weakness with the work is that it is not clear how the activity level of the relaxed PAM enzyme, Nsp2-SmuCas9, compares to existing enzymes. Is it much better than the SpCas9 that has almost no PAM preference (SpRY) or the NGN PAM (SpG)? How does it compare to the most commonly used SpCas9 nuclease, which is known to be active in a wide variety of biological contexts? The activity assessment at endogenous sites seemed to have a long timeline, as the indel rate was measured 5 days after transfection. Clarifying the effectiveness of this new nuclease would increase the impact of this work.

We sincerely thank the reviewer for the constructive comments on our manuscript. Following reviewer’s suggestions, we compared the editing efficiency of Nsp2Cas9, Nsp2-SmuCas9, SpCas9, SpCas9-NG, and SpCas9-RY side-by-side. Overall, the editing efficiency was low this time probably due to low transfection efficiency. The results revealed that SpCas9 was the most active enzyme. Nsp2Cas9, SpCas9-NG, and SpCas9-RY displayed similar activity. Nsp2-SmuCas9 displayed lower activities than other Cas9 variants (Figure 5C).

2) In the presentation of the manuscript, there are several weaknesses. First, while it is true that allele-specific disruption is an important application of new CRISPR proteins, there are many other reasons why they would be useful. The specific focus on this single application throughout the abstract, introduction and discussion takes away from the widespread utility of these new tools. The writing would be more compelling if it targeted a broader audience. Allele-specific targeting is also possible beyond the PAM site if the mutation is in a position with high specificity.

Many thanks for the reviewer’s suggestions. Following reviewer’s suggestions, we emphasize the widespread utility of these new tools throughout the abstract, introduction, and discussion in the revised manuscript. Allele-specific targeting is only mentioned in the discussion.

3) Second, the introduction is further missing a discussion of other research engineering new PAM specificity or even completely removing specificity. A more convincing narrative would include reasoning for why characterizing naturally occurring orthologs is a powerful and important approach. This information is in the discussion, but it would be helpful for the reader if these points were in the introduction.

Many thanks for the reviewer’s comments. Following reviewer’s suggestions, we added other research engineering new PAM specificity in the introduction. We also included reasoning for why characterizing naturally occurring orthologs is a powerful and important approach.

“Engineered Cas9 variants with flexible PAMs can increase targeting scope. For example, SaCas9 was engineered to accept an NNNRRT PAM [1]; SpCas9 was engineered to accept almost all PAMs [2], but this strategy is time-consuming, and often comes at a cost of reduced on-target activity. Another strategy is to harness natural Cas9 nucleases for genome editing. We have developed several closely related Cas9 orthologs for genome editing [3, 4]. The advantage of developing tools from closely related Cas9 orthologs is that they can exchange the PAM-interacting (PI) domain. If an ortholog recognizes a particular PAM but does not work efficiently in human cells, we can use this ortholog PI to replace another ortholog PI to generate a chimeric Cas9.”

4) A second concern with the presentation and analysis of the findings is a minimal connection to the structural context of the discoveries. Many readers will likely be interested in how the specificity shifts are occurring in these orthologs, which could be remedied by supplementary figures of homology models.

We totally agree with the referee that structural models would help readers better understand the specificity shifts occurring in these orthologs. We have generated calculated structural models of these orthologs in complex with sgRNA and DNA using the crystal structure of Nme1Cas9 (PDB ID: 6JDV). Some specificity shifts can be well explained by these structural models. When the amino acid near the 5 position of the PAM is histidine, its side chain forms a potential hydrogen bond with the 6-hydroxyl group of guanine. Replacement of this guanine by cytosine or thymine would cause a major clash, whereas adenine lacks the hydroxyl group to form hydrogen bond with the histidine (Figure 2-figure supplement 2A). Likewise, an aspartate at 5 position of the PAM would favor a specific recognition of cytosine via hydrogen bonding with its 4-amine group, but not of other bases that may either result in major clash or abolish the hydrogen bond (Figure 2-figure supplement 2B). Similar explanation applies also to the apparent specificity between glutamine and adenine at the 8 position of the PAM on the target sequence (Figure 2-figure supplement 2C).

5) Along the same lines, further structural analysis of the failures would be helpful for those embarking on similar projects. Are there any differences in the sequence or structure of the 4/29 orthologs that were not functional in the GFP-activation assay compared to those that were?

Sequence alignment indicates that the four inactive orthologs possess intact active sites. In the predicted structural models of these orthologs, we did not observe local conformational variations that preclude the interaction with sgRNA or DNA. Sequence alignment indicates that the four inactive orthologs possess intact active sites. In the predicted structural models of these orthologs, we did not observe local conformational variations that preclude the interaction with sgRNA or DNA. We speculate that specific modifications of Cas9s in mammalian cells may occur, leading to the loss of enzymatic activities of the 4 orthologs.

Calculated structural models of AseCas9, Hpa1Cas9, MspCas9, and PlaCas9. Overall calculated structures of AseCas9, Hpa1Cas9, MspCas9, and PlaCas9 with sgRNA and dsDNA.

6) Similarly, it was surprising that the Nsp2-NarCas9 chimera was not active, and it would be helpful if the authors could speculate based on the differences between SmuCas9 and NarCas9, such as at the interface of the domains that were fused. Structural models of the fusions would help the reader to visualize the strategy. Exploring the failures and challenges is important for understanding the generalizability of the presented approach.

Following reviewer’s comments, we generated structural models of Nsp2-NarCas9, Nsp2-SmuCas9, and NarCas9 using the crystal structure of highly homologous Nme1Cas9 in complex with sgRNA and dsDNA (PDB ID: 6JDV) as the template by SWISS-MODEL. By superimposing these models, we noticed that residues G1035, K1037 and T1038 of Nsp2-NarCas9 chimera protrude towards the DNA molecule, which would prevent the binding with DNA and thereby abolishing the editing activity (Figure 4-figure supplement 2A). In comparison, Nsp2-SmuCas9 and NarCas9, which possess the Cas activity, show no protrusion at the corresponding position (Figure 4-figure supplement 2B-C).

7) Finally, the final sequence of Nsp2-SmuCas9 fusion, as well as other enzymes such as the failed Nsp2-NarCas9, are not obvious in the manuscript. I may have missed them, but I also did not see the primers used in the Methods section. Addgene submission is also encouraged and would be of great value to the scientific community.

Thank you for your suggestions. The final sequence of Nsp2-SmuCas9, as well as other enzymes, have been provided in Supplemental file 1. The primers for chimera proteins were listed in Supplemental file 1. We will submit plasmids to Addgene soon.

Author Response

Reviewer #1 (Public Review):

The authors of this study adopted Cas9-mediated enrichment of target locus and Nanopore long-read sequencing to accurately count repeat numbers in the CNBP gene, which is notorious for precise calling before. They also compared their result with that of the conventional approach, validating their approach. It is an interesting read and shows a pathway that a clinic can take in the near future.

However, this paper's novel contributions need to be emphasised as there are some papers that utilized Nanopore sequencing to elucidate short repeats (https://pubmed.ncbi.nlm.nih.gov/35245110/; https://bmcmedgenomics.biomedcentral.com/articles/10.1186/s12920-020-00853-3).

The reviewer is correct that ONT sequencing had been already utilized for the analysis of the microsatellite within the CNBP gene (Stevanovski et al. 2021; Mitsuhashi et al. 2021), however this was confined to CNBP alleles in the normal range only. Moreover, the approaches utilized present some critical drawbacks. The work of Mitsuhashi and colleagues exploited ONT whole genome sequencing, that is not applicable in the routine due to the very high costs. The group of Stevanovski utilized the recently introduced “Read Until” feature of ONT sequencing for the analysis of microsatellites in 37 disease-associated loci. This allows selective sequencing of pre-defined target DNA molecules, thus enabling a targeted sequencing with similar advantages of the Cas9 mediated sequencing presented hereby. However, enrichment levels achieved by “Read Until” (5x) are consistently lower than those obtained with the Cas9 approach (500x), due to higher background. This may constitute an important issue when dealing with extremely long CNBP alleles that can be disadvantaged in sequencing as compared to shorter contaminating fragments (Shruti V Iyer, BioRxiv 2022).

These aspects, underlying the advantages of the Cas9 mediated sequencing presented, hereby have been now reported in the “Discussion”section (Lines 337-348).

Another issue is the clinical utility of the approach. Although it is precise, it is not totally clear whether this accuracy is required in clinical practice, as the repeat status does not completely correlate with phenotypic severity.

The genotype-phenotype issue in DM2 is still an open question and relies on a single study from Day et al. (2003; PMID:12601109) in which Southern blot analysis was used to determine the length of the DM2 mutation. Because of the extremely large size of the CCTG expansions and somatic instability of the repeat, Southern blot fails to detect the DM2 mutation in about 20% of known carriers, whose expansion length remains undeterminable. Moreover, detectable expanded alleles can appear as single discrete bands, multiple bands, or smears with no indication of the degree of mosaicism. The absence of precise genotype-phenotype correlation can be thus largely due to the technical difficulties in analysing such expansions in details. Despite a clinical utility of the presented approach would not be thus immediate due to lack of knowledge, we believe that the use of long read sequencing in large cohorts of DM2 patients could definitively clarify if information about the length, the composition and the degree of mosaicism of the DM2 mutation are associated with the severity of the DM2 clinical phenotype and/or with the disease age at onset.

Considerations related to the clinical utility of the approach have been now included in the “Discussion” section (lines 294-300 and lines 420-428).

Lastly, it is not clear about the familial cases (A1-A4). What are their relationships and why their copy numbers are not exactly the same? Is it because of extreme recombination and variation even in a family or just represent limited accuracy?

Cases A1-A4 derived from a large consanguineous DM2 family, whose pedigree has been now reported in Figure S1. The extreme variability in the (CCTG) and (TCTG) copy numbers within the family is typical of DM2 patients, as reported in Day et al., 2003. A tendency towards contractions rather than expansion of the CCTG array can also been observed in this family, in agreement with literature data. The meiotic instability of the (CCTG)n and (TCTG)n distal tract is probably due to unequal recombination events and errors during DNA replication/repair of this highly repetitive region, which give rise to somatic and germinal mosaicism. If we consider the variability in the number of (TG)v, this likely reflects a limited accuracy of the method, as discussed for the healthy alleles (Table 2). The 5’ (TG)v and (TCTG)w arrays are indeed supposed to be polymorphic in the general population but stable in the same individual and in the meiotic transmissions. Consistently, we now show in Figure S4 that all family members show an equivalent pattern of TG repetitions. Such small inconsistences probably reflect ONT sequencing errors and could be addressed by using the most recent base-calling algorithm and eventually the more accurate Q20+ chemistry. According to the Reviewer’s observations, all these aspects have been discussed more deeply in the manuscript, with the support of the additional Figure S1 and S4 (see Results lines 215-219 and Discussion lines 364-368)

They lack a validation cohort, with prospective patients.

The reviewer is correct, this is a pilot study on a limited number of DM2 patients. We are aware that a validation including a larger cohort of DM2 patients would be desirable to further confirm our results. This limitation of the study has been clearly indicated in the “Discussion” section” (lines 385-392). Unfortunately, the majority of available DNA samples derive from retrospective analyses and the DNA quantity/quality was not always sufficient for ONT sequencing. We are planning to collect at least 30 novel DNA samples from prospective DM2 cases, either sporadic or familiar. However, the limited number of DM2 patients referring to our centre (about 1-2 pts/month) and the low incidence of DM2 in the Italian population (Vanacore et al., 2016) will make this collection and validation not feasible in the short time.

Author Response

Reviewer #1 (Public Review):

The manuscript by Dr Riley and colleagues reports a novel link between molecular clock operative in skeletal muscle and titin mRNA, encoding for essential regulator of sarcomere length and muscular strength. Surprisingly, this clock-mediated regulation of titin occurs at the level of splicing, as demonstrated by SDS-VAGE analyses of skeletal muscle from muscle-specific Bmal1KO mice compared to Bmal1wt counterpart. Concomitant with switch of predominant isoform of titin, skeletal muscle of muscle specific Bmal1KO mice exhibited irregular sarcomere length. Moreover, the authors show that this shift of titin splice is causal for such sarcomere length irregularity and for altered sarcomere length in muscle from the mice with compromised clock function. Importantly, the authors provide compelling evidence that Rbm20, encoding for RNA-binding protein that mediates splicing of titin, is cooperatively regulated by Bmal1-Clock heterodimer and MyoD, via enhancer element in intron 1 of Rbm20, thus identifying Rbm20 as a novel direct clock-regulated gene in the skeletal muscle. Strikingly, rescue of Rbm20 in muscle specific Bmal1KO animals' results in rescue of titin splicing pattern and protein size, suggesting that Rbm20 mediates the regulatory effect of Bmal1 on titin splicing and represents a mechanistic link between the clock and regulator of sarcomere length and regularity.

We thank reviewer 1 for the very kind comments. We agree that the circadian regulation of titin in any capacity is surprising. We are excited about the implications of our work for cardiac muscle and its therapeutic potential in human skeletal muscle.

Reviewer #2 (Public Review):

In this work the authors investigated whether deleting the BMAL1 gene, an integral component of the cellular clock that drives the circadian rhythms of cells, affects the giant protein titin. They report that deleting BMAL1 in skeletal muscle alters the splicing of titin and that this might underlie an increase in sarcomere length dispersion. They show that the effect is through the titin splicing factor RBM20. This work has high novelty and has the potential to add to our understanding of muscle physiology. It is unclear whether splicing of skeletal muscle titin indeed undergoes a circadian rhythm. This could be easily checked using protein gels or RNA seq in muscle samples collected at different times of the day.

We appreciate the question and recognize that our original manuscript did not clearly outline that the circadian clock regulates both rhythmic and non-rhythmic gene expression. In this study, the target of the muscle clock is expression of Rbm20 mRNA which is not a rhythmically expressed gene in muscle. This has now been addressed in the manuscript.

Based on the estimated titin turnover and incorporation rates of titin (Cadar et al., 2014), we do not believe that skeletal muscle titin splicing undergoes a circadian rhythm. However, we believe our data highlights the growing recognition of the molecular clock in regulating non-rhythmic processes. We have added data from a chronic phase advance model of circadian disruption with wildtype mice and identify that disrupted circadian rhythms are sufficient to change Rbm20 expression in skeletal muscle (Figure 5).

This work would be more convincing if the sarcomere length dispersion was investigated in greater detail. Showing this in one muscle type only (TA), in muscles fixed at one length only, and not showing sarcomere length dispersion in the rescue experiment of Figure 6, is rather limited.

We agree that our analysis of sarcomere length dispersion across joint angles would be interesting but we think it is beyond the scope of this study. As noted above, the premise of this study emerged from our early work in which we found that skeletal muscle from 2 different genetic mouse models of circadian disruption, Bmal1 KO mice as well as the Clock mutant mice, exhibit decreased maximum specific force with significant disruptions to sarcomere structure (Andrews et al., PNAS, 107 (44) 19090-19095 2010). The primary focus of this study was to address the mechanistic link between the muscle circadian clock, its transcriptional targets with a focus on sarcomere structure and our first clue was with the expression of titin isoforms. We included analysis of sarcomere length as an outcome measure because it is a fundamental feature of skeletal muscle, it has links to mechanical function and it is a structure that can be modified by titin spliceforms.

A small increase in sarcomere length variation as suggested in Figure 2 is unlikely to have a great functional consequence. If it were, how can muscles that express naturally long titin isoforms (soleus, EDL, diaphragm, etc), function well?

We did not intend to suggest that we see an increase in sarcomere length in Figure 2 and have clarified the figure and text accordingly. The change we see is related to the variability of sarcomere length; we do not see any change in the average sarcomere length. The topic of titin spliceform specialization and the contribution to sarcomere structure and function across different muscle groups (soleus vs. EDL vs. Diaphragm) is a really interesting question but beyond the scope of this study.

Reviewer #3 (Public Review):

This manuscript is using an inducible and skeletal muscle specific Bmal1 knockout mouse model (iMSBmal1-/-) that was published previously by the same group. In this study, they utilized the same mouse model and further investigated the effect of a core molecular clock gene Bmal1 on isoform switching of a giant sarcomeric protein titin and sarcomere length change resulted from titin isoform switching. Lance A. Riley et al found that iMSBmal1-/- mouse TA muscle expressed more longer titin due to additional exon inclusion of Ttn mRNA compared to iMSBmal+/+ mice. They observed that sarcomere length did not significantly change but more variable in iMSBmal1-/- muscle compared to iMSBmal+/+ muscle. In addition, they identified significant exon inclusion in the proximal Ig region, so they measured the proximal Ig length domain and confirmed that proximal Ig domain was significantly longer in iMSBmal1-/- muscle. Subsequently, they experimentally generated a shorter titin in C2C12 myotubes and observed that the shorter titin led to the shorter sarcomere length. Since RBM20 is a major regulator of Ttn splicing, they determined RBM20 expression level, and found that RBM20 expression was significantly lower in iMSBmal1-/- muscle. The reduced RBM20 expression was regulated by the molecular clock controlled transcriptional factor MyoD1. By performing a rescue experiment in vivo, the authors found that rescue of RBM20 in iMSBmal1-/- TA muscle restored titin isoform expression, however, they did not measure whether sarcomere length was restored. These data provide new information that the molecular cascades in the circadian clock mechanism regulate RBM20 expression and downstream titin isoform switching and sarcomere length change. Although the conclusion of this manuscript is mostly supported by the data, some aspects of experimental design and data analysis need be clarified and extended.

Strengths:

This paper links the circadian rhythms to skeletal muscle structure and function through a new molecular cascade: the core clock component Bmal1-transcription factor MyoD1-RBM20 expression-titin isoform switching-sarcomere length change.

Utilization of muscle specific bmal1 knockout mice could rule out the confounding factors from the molecular clock in other cell types

The authors performed the RNA sequencing and label free LC-MS analyses to determine the exon inclusion and exclusion through a side-by-side comparison which is a new approach to identify individual alternative spliced exons via both mRNA level and protein level.

We agree that the side-by-side analysis from RNAseq and LC-MS data are novel and provides a foundation for others wanting to study both titin mRNA and protein. In this version, we have expanded this work to include samples from our Rbm20 rescue model (Figure 6). Similarly, to our approach in the muscle specific Bmal1 knockout model, these results confirm our RNA-seq results and indicate that LC-MS is a suitable method to measure titin protein isoform. We note that while more work is needed to confirm the broad utility of the LC-MC approach, it may be a suitable alternative to RNA-seq for measuring region-specific, and possibly exon-specific, changes in titin isoform expression.

Weaknesses:

Both RBM20 expression and titin isoform expression varies in different skeletal muscles. The authors only detected their expression in TA muscle. It is not clear why the authors only chose TA muscle.

The reviewer, like Reviewer 2, raises a good point about muscle specificity as this is a significant challenge for research in the field of skeletal muscle. As we noted above, our primary focus was on the TA because our goal was to study the molecular links between the muscle circadian clock and titin expression with inclusion of analysis of a structural outcome, sarcomere length variability. This muscle is well suited for the combination of approaches employed. We recognize the limits of using a single muscle, but we note that the we used ChIPseq data that provided the initial clues that CLOCK and BMAL1 bind to a site within intron 1 of the Rbm20 gene came from gastrocnemius and not TA muscle samples . Our targeted ChIP-PCR confirms that CLOCK and BMAL1 bind to the same intron 1 location from TA muscle samples. In addition, we have included data from quadriceps and TA muscles in our chronic jet lag model in which we use an environmental manipulation to disrupt the muscle clocks. We believe that the edits to the text and inclusion of this data strengthen and extends our findings to other muscles through circadian disruption and not only a genetic knockout model.

The sarcomere length data are self-contradictory. The authors stated that sarcomere length was not significantly changed in muscle specific KO mice in Line 149, however, in Line 163, the measurements showed significantly longer in muscle specific KO muscle. The significance is also indicated in Figures 2C and 3B.

We apologize for the miscommunication. The significance indicated in Figure 2C refers to the significant difference in variability of sarcomere length and not a significant difference in sarcomere length. The difference in Figure 3B is to indicate a slightly longer but significantly different from control sarcomere length, but also a significant difference in sarcomere length variability. To make this difference clear, we have changed the symbol for significantly different variability from * to # in both Figures 2C and 3B. We hope this clarifies our findings.

Manipulating titin size using U7 snRNPs linking to the changes in sarcomere length and overexpressing RBM20 to switch titin size are the concepts that have been proved. These data do not directly support the impact of muscle specific Bmal1 KO on ttn splicing and RBM20 expression

We agree that the use of U7 snRNPs does not directly support the impact of muscle specific Bmal1 KO on titin splicing and RBM20 expression; however, that was not the goal of this set of experiments. Several papers have recently indicated titin’s role as a sarcomeric ruler (Tonino 2017, Brynnel 2018), but none of them have investigated the proximal Ig domain that we identified as regulated by the circadian clock disruption. Because of this, we thought it necessary to show this region specifically contributes to sarcomere length using our cell culture model. Further, we think this point strengthens our study as it suggests that in the absence of a clock effect, altering the proximal Ig domain of titin directly alters sarcomere length adding to the growing evidence base that titin acts as a sarcomeric ruler. We have edited the text of the results and the discussion to clarify this point.

There is no evidence to show if interrupted circadian rhythms in mice change RBM20 expression and ttn splicing, which is critical to validate the concept that circadian rhythms are linked to Ttn splicing through RBM20.

We recognize this concern and have performed a new study in which we used a model of chronic jet lag in normal adult C57BL6 mice as a model to disrupt the muscle clock (Wolff, Duncan and Esser, JAP 2013). This new data has been added in Figure 5 and shows that by altering the lights on: lights off schedule every 4 days for 8 weeks, mimicking repeated jet lag, we disrupt Rbm20 expression in TA and gastrocnemius muscle (note, this is new data for both the muscle and clock fields). Concomitant with changes in clock gene expression we reported in 2013, we found that mRNA expression of Rbm20 is altered as well. These findings confirm that normal muscle clock disruption is sufficient to alter expression of Rbm20.

Author Response

Reviewer #2 (Public Review):

Detomasi et al investigated the mechanism behind allorecognition in the filamentous fungus Neuraspora crassa. Previous work had identified two proteins cwr-1 and cwr-2 that control recognition of haplotype and the following cell wall dissolution and subsequent fusion of hyphae. This work is a systematic study of the role of cwr-1 in the allorecognition of six haplogroups. Cwr-1 is predicted to be a chitin-active lytic polysaccharide monooxygenase belonging to the AA11 enzyme family. The activity of the isolated cwr-1 enzyme on chitin is confirmed and it is shown that the catalytic domain is sufficient to confer an allorecognition checkpoint. Surprisingly, and in contrast to previously published data, enzyme activity of cwr-1 is not required. This is shown by the introduction of mutant cwr-1 lacking key residues for activity in a cwr-1 deletion strain followed by screening for fusion events with an incompatible cwr-2 allele.

The strength of this study is the rigor by which all experiments have been designed and carried out. The data sets from the biological assays are complete and treated appropriately with statistical tools. The enzymology is for the most part very comprehensive with eg. full-length mass spectrometry to verify the mutant enzymes. The enzyme activity assays using chitin as substrate are carried out at a high standard using HPAEC detection of soluble products.

Because of the highly surprising conclusion that the active domain but not the active site is required, the weakness of the manuscript lies in the inability to explain this finding.

The term "moonlighting" to describe the phenomenon, is not a very good one. I would recommend changing the title of the paper accordingly. There are already published studies that describe proteins (termed X325) that are highly similar to lytic polysaccharide monooxygenases (both in the overall fold and in the coordination of a single copper atom) that have a clear biological function but no detectable catalytic activity.

Moonlighting proteins comprise a subset of multifunctional proteins in which one polypeptide chain exhibits more than one physiologically relevant biochemical or biophysical function (Jeffery CJ. 1999 Moonlighting Proteins. Trends Biochem. Sci. 24, 8–11 doi:10.1016/S0968-0004(98)01335-8). CWR-1 fits this description. It is predicted to be a PMO and indeed utilizes chitin as a substrate and yields expected PMO-derived oxidative products, thus is clearly definable as a PMO. CWR-1 also is directly involved in allorecognition and as our paper shows, the chitin catalytic activity has nothing to do with allorecognition. So as defined, CWR-1 is a “moonlighting” protein. There does not appear to be another PMO that falls under this definition. The closest one would be GbpA, however activity on polysaccharides present on mucin has not been ruled out, so we decided to remove this comment from the manuscript. The “X325” family PMO-type proteins have an alternate activity, but not two separate activities within the same polypeptide. Although we do not yet know what physiological role is played by the chitin activity in N. crassa, it is not required to know this to conform to the definition. Thus, CWR-1 conforms to the moonlighting definition. We slightly changed the title of the manuscript to be less cumbersome.

Author Response

Reviewer #3 (Public Review):

Liu et al. investigated the role of Epac2, the "other" less studied cAMP effector (compared to the classical PKA) in dopamine release and cocaine reinforcement using slice electrochemistry, behavior, and in vivo imaging in dopamine neuron-specific Epac2 conditional knockout mice (confirmed by elegant single-cell RT-PCR). Epac2 genetic deletion (Epac2 cKO) or pharmacological inhibition (using the Epac2 antagonist ESI-05, i.p.) reduced cocaine (under both fixed and progressive ratio schedules) but not sucrose, self-administration, supporting an essential role for Epac2 in cocaine reinforcement but not natural reward. Cyclic voltammetry on striatal slices demonstrated that evoked DA release was reduced in Epac2 cKO mice and enhanced by the Epac2 activator S-220 or the PKA activator 6-Bnz independently. Using in vivo chemogenetics and fiber photometry (with the DA fluorescent sensor GRABDA2M), authors showed that DCZ activation of VTA DA neurons expressing rM3D(Gs) increased NAc DA release and cocaine SA in Epac2 cKO mice (rescuing), whereas inhibition of VTA DA neurons expressing hM4D(Gi) decreased DA release and cocaine SA in WT mice (mimicking). Based on these experiments, the authors concluded that Epac2 in midbrain DA neurons contributes to cocaine reinforcement via enhancement of DA release.

The experiments are generally rigorous and the conclusions are mostly well supported by data, but some aspects of behavioral experiments and data analysis need to be clarified or extended.

1) The chemogenetic rescue experiments in Fig. 7 suggested that enhancing DA release in Epac2 cKO mice rescued cocaine SA in mutant mice, but did not necessarily demonstrate that Epac2 mediates this process, thus a causal mechanistic link is missing. This is an important point to clarify because the central theme of the work is that Epac2 regulates cocaine SA via DA release. In addition, it's unclear if chemogenetic activation of DA neurons also enhances sucrose reward. A potentially positive result would not affect the conclusion that enhancing DA release can rescue cocaine SA in mutant mice but will affect the interpretation and specificity of the rescue data.

The reviewer’s viewpoint is well taken. We agree that Gs-DREADD activation may restore the Epac2-cKO-induced decrease in dopamine release, but not other deficits caused by Epac2 deletion. We acknowledge the limitations of our DREADD experiments (see our response to Reviewer 2 above). Please also see our response to question 2 below.

In the revised manuscript, we provided representative temporal patterns of FR1 sucrose self-administration in WT and Epac2-cKO mice, which did not display significant differences between genotypes (see newly added Figure 3 – figure supplement 2). To prevent excessive sucrose intake, sessions ended if the maximum number (64) of reinforcers were earned during the 1-hour training session. Almost all wild-type and Epac2-cKO mice had approached this maximum level near the end of the 10-day training. While testing if chemogenetic activation of VTA dopamine neurons enhances sucrose self-administration is, in principle, a good idea, such enhancement would likely lead to a ceiling effect, making the detection of potential differences between genotypes difficult.

2) Relatedly, chemogenetic inhibition experiments in Fig 8 showed that inhibiting DA neurons reduced DA release and cocaine SA in WT mice, which suggested that the strength of DA transmission was a regulator of cocaine SA. This is expected given the essential role of DA transmission in reward in general, but it did not provide strong insights regarding the specific roles of Epac2 in the process.

An ideal experiment would be to examine whether viral expression of Epac2 in VTA dopamine neurons in Epac2-cKO mice could restore cocaine self-administration to the level of WT mice. However, our lab is not equipped to do this type of study at its current capacity, but we are very interested in exploring this exciting experiment in the future.

3) Fig 7B. DCZ-induced DA releases enhancement in the fiber photometry recording seems to only last for ~30 min, well short of the duration of a cocaine SA session (3 hrs). It's unclear how this transient DA release enhancement could cause the prolonged cocaine SA behavior.

We appreciate the insight from the Reviewer. We have included the time course of dopamine transients following DCZ injection (now Fig. 6B,C). Although the DCZ-induced enhancement of DA transients was most robust during the first 30 min, an enhancement persisted for the duration of fiber photometry recording (1 hour after DCZ injection). In the original study in which DCZ was developed as a DREADD ligand (Nagai et al., 2020), in vivo two-photon imaging of somatosensory cortex neurons that co-expressed Gq-DREADD (hM3Dq) and GCaMP6 revealed that i.p. injection of DCZ led to a rapid increase in GCaMP6 activity in mice that peaked at about 10 min and plateaued for at least 150 min (see Fig. 4 in that paper). Although Gs-DREADDs may respond to DCZ differently, it appears that DCZ induces long-lasting activation of DREADDs expressed in the brain. We have added a brief discussion in the Results section of the revised manuscript (page 12, lines 262-265).

4) Fig. 9. working hypothesis: hM4D(Gi) and hM3D(Gs) are shown to inhibit and enhance synaptic vesicle docking, which is not accurate. These DREADDS presumably regulate neuronal excitability, which in turn affects SV release.

We agree with the reviewer and have removed synaptic vesicle docking from the model (now Figure 8).

Author Response

Reviewer #1 (Public Review):

“The authors suggest that they uncovered two distinct phases of how the posterior axial identity is controlled; the first involving TBXT/Wnt to generate posterior 'uncommitted progenitors', which then go on to generate NCCs, and the second involving FGF to impart posterior axial identity onto CNS/spinal cord cells.”

Based on our new data we have slightly modified our model: (i) TBXT controls posterior axial identity acquisition in NMP precursors and both their trunk NC and CNS spinal cord derivatives; (ii) this early, TBXT-driven posteriorisation phase appears to be WNT dependent; (iii) a subsequent TBXT/WNT-independent phase of Hox cluster regulation occurring during the transition of NMPs towards their NC/spinal cord derivatives is controlled predominantly by FGF signalling. This model is shown in Figure 9 in the revised manuscript.

“I am not convinced that their data show this; it is equally possible that NMPs are heterogeneous and the effects observed simply reflect a differential response of cells or selection. Since the authors largely analyse their data by qPCR it is difficult to disentangle this.”

We believe that the inclusion of new data defining the emergence of NMP derivatives at the single cell level through analysis of key trunk lineage-specific markers (HOXC9, SOX10, SOX1, SOX2) via immunostaining and image analysis/flow cytometry (see Figure 3-figure supplement 1, Figure 4C-D, Figure 5-figure supplement 1, Figure 7D-E in revised manuscript) should address the reviewer’s point. See also our response to the editorial comments above. It should be note that the vast majority of day 3 hESC-derived NMPs (>95%) is positive for TBXT protein expression based on antibody staining and thus the starting population for the generation of trunk NC/spinal cord progenitors can be considered largely homogeneous when it comes to the expression of this transcription factor.

“The authors include some expression data in mouse to support their in vitro findings. However, these need to be explained and integrated better.”

We hope that breaking down figure 4 and the related text into two parts has improved the integration of the in vivo data in the revised version of the manuscript.

Reviewer #2 (Public Review):

“The fact that the regimes are distinct makes the comparisons of neural crest versus spinal cord difficult to interpret as the cells have been exposed for different amounts of time to WNT and FGF when they asses the Hox code in neural crest or spinal cord cells. Specially because the spinal cord induction protocol involves four additional days of culture with FGF and CHIR, and the cells after seven days are not mature neural progenitors.

To address this point, we employed “neutral”, extrinsic signal-free culture conditions that drive NMPs towards a mixture of early pre-neural spinal cord progenitors and mutually exclusive SOX1+HOXC9+ CNS spinal cord and SOX10+HOXC9+ NC populations. This facilitated the effective assessment of cell fate and posterior axial identity acquisition simultaneously in both NMP-derived spinal cord and NC cells, during discrete time windows of TBXT knockdown (Figure 4 in revised manuscript). For details see our response above.

Likewise, the authors have previously shown that such a treatment induces the expression of dorsal neural tube/early neural crest markers”.

Although we have no evidence of SOX10 expression in cultures generated from NMPs following WNT and FGF agonist treatment for 4 days indicating absence of definitive NC cells, we opted to remove the “CNS” references when describing this cell population to accommodate for the possibility that it may be NC-potent given its previously described dorsal neural tube/early NC character (Cooper et al, 2022; Wind et al., 2021).

“It would be good to see some quality controls on the percentages of neural crest progenitors or spinal cord neural progenitors that they get in each signalling regime. Can the authors separate neural progenitor cells and neural crest cells (for example by FACS sorting with specific markers) to confirm the cell-type specific expression of the HOX genes in these experiments?”.

As mentioned above, we have now included immunostaining data quantifying thoroughly the induction of trunk SOX1+HOXC9+ CNS spinal cord and SOX10+HOXC9+ NC cells under different culture conditions/TBXT levels (see Figure 4C-D, Figure 5-figure supplement 1, Figure 7 and Figure 7-figure supplement 1).

“In the neural crest differentiation protocol, there is a slight, non-significant upregulation of neural progenitor markers following TBXT knockdown, can the authors quantify the percentage of neural cells in their cultures to see how much of the observed effect is specific to neural crest cells?”

We have quantified the emergence of SOX1+ CNS spinal cord progenitor cells in NMPderived trunk NC cultures using both FACS/intracellular staining and immunostaining/image analysis but their numbers are too small (2-3% of total cells with no statistically significant difference between control and TBXT knockdown cells, see Figure 3-figure supplement 1) to extract any meaningful conclusions on the effect of TBXT depletion on them. However, quantification of SOX1+HOXC9+ cells generated from NMPs upon culture in “neutral” basal conditions revealed that TBXT depletion results in a decrease in their number in addition to its established impact on trunk NC (see Figure 4C-D in revised manuscript).

“Previous work from the lab showed that a 3-day FGF/CHIR treatment of hESCs followed by a two-day incubation on basal medium is sufficient to induce neural progenitors that express Hox genes of posterior identity (PMID: 25157815). Can the authors draw the same conclusions for the spinal cord cells with this protocol if they deplete TBXT during the first three days and assay at day 7 the cells on basal medium, or if they deplete TBXT during the last four days of the protocol? The comparison of the 3-day FGF/CHIR regime followed by basal medium treatment versus the continuous FGF/CHIR for a 7-day period may help clarify the temporal and cell-type specific effects of the HOX code via TBXT/FGF on the neural crest and/or spinal cord cells”.

We have carried out this experiment as suggested by the reviewer (Figure 4C-D/line numbers 226-256 in the revised manuscript), for details see our responses above.

“In their data, it seems that anterior HOX genes (PG1-5) as well as other posterior HOX (PG6-9) are expressed in wild-type posterior neural crest and early spinal cord cells. Can HOX genes that mark posterior cranial, vagal or trunk identities be co-expressed in trunk neural crest or spinal cord cells? Is it possible that the differentiations generate cells that have different axial identities? I wonder if this interpretation comes from the normalization. Perhaps the authors could clarify if the levels of expression of the 3' Hox genes are higher or lower than 5' Hox genes in their differentiations”.

Co-expression of HOX paralogous group (PG) (1-5) and (6-9) transcripts does occur in the posterior part of the mouse embryo around E9.5, both in the NMP-containing tailbud region (Gouti et al, 2017) as well as in differentiated posterior neural/neural crest cells e.g. for Hoxb1 expression in E9.5 mouse embryos see (Arenkiel et al, 2003; Glaser et al, 2006); for Hoxc9 expression see (Bel et al, 1998). Thus, the presence of HOXPG(1-5) transcripts in HOXC9+ trunk NC cells is not surprising and in line with what has been reported previously in other studies describing the generation of posterior NC/spinal cord cell types from hESC/NMPs (Frith et al., 2018; Hackland et al, 2019; Lippmann et al, 2015; Mouilleau et al, 2021). Alternatively, the simultaneous detection of transcripts belonging to both HOXPG(1-5) and HOXPG(6-9) could indicate the co-emergence of a separate population of posterior cranial/cardiac/vagal NC cells during trunk NC differentiation. Moreover, the detection of HOX transcripts does not always correlate with corresponding protein positivity (Faustino Martins et al, 2020) pointing to the existence of post-transcriptional/-translational mechanisms controlling HOX protein expression. Unfortunately, we have not identified reliable (in our hands) antibodies against HOXPG(1-5) members that we can use together with HOXC9 in order to distinguish between these possibilities.

“In the experiments where the authors asses if TBXT binds directly or indirectly to the HOX clusters, the authors compare pluripotent cells with hNMPs. This data confirms that TBXT acts as an activator in hNMPs and that it binds to regions in the HOX clusters. Do the HOX regions overlap with known enhancers for the HOX genes for neural crest or spinal cord?”

We have included new ATAC-seq data mapping chromatin accessibility in day 8 trunk NC cells generated from TBXT-depleted and control hESC-derived NMPs. These data, combined with the ATAC-seq and TBXT ChIP-seq analyses from day 3 hESC-derived NMPs, indicate that TBXT controls chromatin accessibility in trunk NC-specific enhancers within HOX clusters, both directly through genomic binding, and indirectly possibly by influencing expression of other key transcriptional regulators such as CDX2. For details see Figure 8-figure supplement 2 and Appendix Table S9 and line numbers 458-482 in the revised manuscript.

“As they see distinct temporal phases of TBXT activity on spinal cord progenitors versus neural crest cells, the authors should test if there are changes in accessibility or TBXT binding in neural crest and spinal cord cells in the HOX locus and/or genome-wide. This comparison may help identify cell-type specific TBXT targets (perhaps acting with distinct coactivators) that are key in the two distinct phases of posterior axial identity control”.

As mentioned above, we have added new ATAC-seq data from analysis of trunk NC cells derived from TBXT knockdown shRNA hESC-derived NMPs in the presence and absence of Tet. These data can be found in Figure 8-figure supplement 2 and Appendix Table S9 in the revised manuscript. As expected, ATAC-seq analysis of pre-neural CNS spinal cord progenitors generated from TBXT knockdown shRNA hESC-derived NMPs in the presence and absence of Tet showed no significant differences in chromatin accessibility between the two conditions again our gene expression data (Figure 6 in revised manuscript). These data were not included in the new manuscript version but they are publicly available as part of our revised GEO submission (GSE184227). Mapping of TBXT genomic binding in NMP-derived trunk NC cells/spinal cord progenitors is not feasible due to the very low/absent expression of TBXT protein in these cell populations. See also our response to the editor’s suggestions.

“In the experiments where the authors examine the signalling pathway dependence of HOX expression during the transition in the neural crest differentiation protocol, it appears that CHIR/LDN treatment induces the highest levels of HOX expression (FIG 3F). Also, there is an increased expression of SOX1 while SOX10 expression is not detected "pointing to a role for BMP signalling in steering NMPs/dorsal pre-neural progenitors toward a NC fate in agreement with previous observations". The results may indicate that WNT and BMP inhibition may induce HOX gene expression in neural cells irrespective of FGF. How do the authors interpret this? How does it affect their final model where FGF (and not WNT) drives the expression of HOX genes in late pre-neural spinal cord progenitors?”.

Based on our data and published work, we speculate that during the transition of hESCderived NMPs towards trunk NC cell, cultures still exhibit autocrine and/or paracrine FGF signalling even in the absence of exogenous FGF agonist supplementation. This is supported by previous reports showing the expression of the active, phosphorylated version of the FGF effector ERK1/2 in differentiating pluripotent stem cells cultured in FGF-free media (Diaz-Cuadros et al, 2020; Stavridis et al, 2007; Ying et al, 2003). This endogenous FGF activity is probably sufficient for the maintenance of HOX gene expression in these cells, while exogenous BMP signalling stimulation is required for the induction of a NC fate. Given the reported antagonism between these two pathways during early neural/NC induction (Anderson et al, 2016; Marchal et al, 2009), treatment with the BMP inhibitor LDN193189 results in FGF signalling potentiation, which in turn leads to increased HOX gene expression and a switch toward a CNS neurectodermal fate at the expense of NC. Further work is needed to mechanistically dissect this hypothesis, which is beyond the scope of this manuscript.

“The identity of the cells in the inhibition of WNT or FGF treatments during the final four days towards spinal cord cells experiments is unclear. It would be very useful if the authors could characterize what cell types emerge after the treatments. In principle, I would expect that these treatments would generate different progenitor types (FGF inhibition may presumably give rise to mesoderm cells, whereas WNT inhibited may be pre-neural). Why would the authors expect these different cell types to have similar levels of expression of WNT targets or Hox genes?”

The inclusion of the new immunostaining data and the quantification of the proportions of SOX2+HOXC9+ emerging upon various WNT/FGF inhibitor treatments (Figure 7D-E in revised manuscript) has now enabled us to define the role of these signalling pathways in controlling HOX gene expression specifically in pre-neural spinal progenitors thus confirming our conclusions from the qPCR data without any bias introduced from contaminating, nonneural HOXC9+ cells.

Author Response

Reviewer #1 (Public Review):

Jones et al. investigated the relationship between scale free neural dynamics and scale free behavioral dynamics in mice. An extensive prior literature has documented scale free events in both cortical activity and animal behavior, but the possibility of a direct correspondence between the two has not been established. To test this link, the authors took advantage of previously published recordings of calcium events in thousands of neurons in mouse visual cortex and simultaneous behavioral data. They find that scale free-ness in spontaneous behavior co occurs with scale free neuronal dynamics. The authors show that scale free neural activity emerges from subsets of the larger population - the larger population contains anticorrelated subsets that cancel out one another's contribution to population-level events. The authors propose an updated model of the critical brain hypothesis that accounts for the obscuring impact of large populations on nested subsets that generate scale free activity. The possibility that scale free activity, and specifically criticality, may serve as a unifying theory of brain organization has suffered from a lack of high-resolution connection between observations of neuronal statistics and brain function. By bridging theory, neural data, and behavioral dynamics, these data add a valuable contribution to fields interested in cortical dynamics and spontaneous behavior, and specifically to the intersection of statistical physics and neuroscience.

Strengths:

This paper is notably well written and thorough.

The authors have taken a cutting-edge, high-density dataset and propose a data-driven revision to the status-quo theory of criticality. More specifically, due to the observed anticorrelated dynamics of large populations of neurons (which doesn't fit with traditional theories of criticality), the authors present a clever new model that reveals critical dynamics nested within the summary population behavior.

The conclusions are supported by the data.

Avalanching in subsets of neurons makes a lot of sense - this observation supports the idea that multiple, independent, ongoing processes coexist in intertwined subsets of larger networks. Even if this is wrong, it's supported well by the current data and offers a plausible framework on which scale free dynamics might emerge when considered at the levels of millions or billions of neurons.

The authors present a new algorithm for power law fitting that circumvents issues in the KS test that is the basis of most work in the field.

Weaknesses:

This paper is technically sound and does not have major flaws, in my opinion. However, I would like to see a detailed and thoughtful reflection on the role that 3 Hz Ca imaging might play in the conclusions that the authors derive. While the dataset in question offers many neurons, this approach is, from other perspectives, impoverished - calcium intrinsically misses spikes, a 3 Hz sampling rate is two orders of magnitude slower than an action potential, and the recordings are relatively short for amassing substantial observations of low probability (large) avalanches. The authors carefully point out that other studies fail to account for some of the novel observations that are central to their conclusions. My speculative concern is that some of this disconnect may reflect optophysiological constraints. One argument against this is that a truly scale free system should be observable at any temporal or spatial scale and still give rise to the same sets of power laws. This quickly falls apart when applied to biological systems which are neither infinite in time nor space. As a result, the severe mismatch between the spatial resolution (single cell) and the temporal resolution (3 Hz) of the dataset, combined with filtering intrinsic to calcium imaging, raises the possibility that the conclusions are influenced by the methods. Ultimately, I'm pointing to an observer effect, and I do not think this disqualifies or undermines the novelty or potential value of this work. I would simply encourage the authors to consider this carefully in the discussion.

R1a: We quite agree with the reviewer that reconciling different scales of measurement is an important and interesting question. One clue comes from Stringer et al’s original paper (2019 Science). They analyzed time-resolved spike data (from Neuropixel recordings) alongside the Ca imaging data we analyzed here. They showed that if the ephys spike data was analyzed with coarse time resolution (300 ms time bins, analogous to the Ca imaging data), then the anticorrelated activity became apparent (50/50 positive/negative loadings of PC1). When analyzed at faster time scales, anticorrelations were not apparent (mostly positive loadings of PC1). This interesting point was shown in their Supplementary Fig 12.

This finding suggests that our findings about anticorrelated neural groups may be relevant only at coarse time scales. Moreover, this point suggests that avalanche statistics may differ when analyzed at very different time scales, because the cancelation of anticorrelated groups may not be an important factor at faster timescales.

In our revised manuscript, we explored this point further by analyzing spike data from Stringer et al 2019. We focused on the spikes recorded from one local population (one Neuropixel probe). We first took the spike times of ~300 neurons and convolved them with a fast rise/slow fall, like typical Ca transient. Then we downsampled to 3 Hz sample rate. Next, we deconvolved using the same methods as those used by Stringer et al (OASIS nonnegative deconvolution). And finally, we z-scored the resulting activity, as we did with the Ca imaging data. With this Ca-like signal in hand, we analyzed avalanches in four ways and compared the results. The four ways were: 1) the original time-resolved spikes (5 ms resolution), 2) the original spikes binned at 330 ms time res, 3) the full population of slow Ca-like signal, and 4) a correlated subset of neurons from the slow Ca-like signal. Based on the results of this new analysis (now in Figs S3 and S4), we found several interesting points that help reconcile potential differences between fast ephys and slow Ca signals:

1. In agreement with Sup Fig 12 from Stringer et al, anticorrelations are minimal in the fast, time-resolved spike data, but can be dominant in the slow, Ca-like signal.

2. Avalanche size distributions of spikes at fast timescales can exhibit a nice power law, consistent with previous results with exponents near -2 (e.g. Ma et al Neuron 2019, Fontenele et al PRL 2019). But, the same data at slow time scales exhibited poor power-laws when the entire population was considered together.

3. The slow time scale data could exhibit a better power law if subsets of neurons were considered, just like our main findings based on Ca imaging. This point was the same using coarse time-binned spike data and the slow Ca-like signals, which gives us some confidence that deconvolution does not miss too many spikes.

In our opinion, a more thorough understanding of how scale-free dynamics differs across timescales will require a whole other paper, but we think these new results in our Figs S3 and S4 provide some reassurance that our results can be reconciled with previous work on scale free neural activity at faster timescales.

Reviewer #2 (Public Review):

The overall goal of the paper is to link spontaneous neural activity and certain aspects of spontaneous behavior using a publicly available dataset in which 10,000 neurons in mouse visual cortex were imaged at 3 Hz with single-cell resolution. Through careful analysis of the degree to which bouts of behavior and bouts of neural activity are described (or not) by power-law distributions, the authors largely achieve these goals. More specifically, the key findings are that (a) the size of bouts of whisking, running, eye movements, and pupil dilation are often well-fit by a power-law distribution over several decades, (b) subsets of neurons that are highly correlated with one of these behavioral metrics will also exhibit power-law distributed event sizes, (c) neuron clusters that are uncorrelated with behavior tend to not be scale-free, (d) crackling relationships are generally not found (i.e. size with duration exponent (if there is scaling) was not predicted by size power-law and duration power-law), (e) bouts of behavior could be linked to bouts of neural activity. In the second portion of the paper, the authors develop a computational model with sets of correlated and anti-correlated neurons, which can be accomplished under a relatively small subset of connection architectures: out of the hundreds of thousands of networks simulated, only 31 generated scale-free subsets/non-scale-free population/anti correlated e-cells/anti-correlated i-cells in agreement with the experimental recordings.

The data analysis is careful and rigorous, especially in the attention to fitting power laws, determining how many decades of scaling are observed, and acknowledging when a power-law fit is not justified. In my view, there are two weaknesses of the paper, related to how the results connect to past work and to the set-up and conclusions drawn from the computational modeling, and I discuss those in detail below. While my comments are extensive, this is due to high interest. I do think that the authors make an important connection between scale-free distributions of neural activity and behavior, and that their use of computational modeling generates some interesting mechanistic hypotheses to explore in future work.

My first general reservation is in the relationship to past work and the overall novelty. The authors state in the introduction, "according to the prevailing view, scale-free ongoing neural activity is interpreted as 'background' activity, not directly linked to behavior." It would be helpful to have some specific references here, as several recent papers (including the Stringer et al. 2019 paper from which these data were taken, but also papers from McCormick lab and (Anne) Churchland lab) showed a correlation between spontaneous activity and spontaneous facial behaviors. To my knowledge, the sorts of fidgety behavior analyzed in this paper have not been shown to be scale-free, and so (a) is a new result, but once we know this, it seems that (e) follows because we fully expect some neurons to correlate with some behavior.

R2a: We agree with the reviewer that our original introductory, motivating arguments needed improvement. We have now rewritten the last 2 paragraphs of the introduction. We hope we have now laid out our argument more clearly, with more appropriate supporting citations. In brief, the logic is this:

1. Previous theory, modeling, and experiments on the topic of scale-free neural activity suggest that this phenomenon is an autonomous, internally generated thing, independent of anything the body is doing.

2. Relatively new experiments (including those by Churchland’s lab and McCormmick’s lab: Stringer 2019; Salkoff 2020; Clancy 2019; Musall 2019) suggest a different picture with a link between spontaneous behaviors and ongoing cortical activity, but these studies did not address any questions about scale-free-ness.

3. Moreover, these new experiments show that behavioral variables only manage to explain about 10-30% of ongoing activity.

4. Is this behaviorally-explainable 10-30% scale-free or perhaps the scale-free aspects of cortical dynamics fall withing the other 70-90%. Our goal is to find out.

Digging a bit more on this issue, I would argue that results (b) and (c) also follow. By selecting subsets of neurons with very high cross-correlation, an effective latent variable has emerged. For example, the activity rasters of these subsets are similar to a population in which each neuron fires with the same time-varying rate (i.e., a heterogeneous Poisson process). Such models have been previously shown to be able to generate power-law distributed event sizes (see, eg., Touboul and Destexhe, 2017; also work by Priesemann). With this in mind, if you select from the entire population a set of neurons whose activity is effectively determined by a latent variable, do you not expect power laws in size distributions?

Our understanding is that not all Poisson processes with a time-varying rate will result in a power law. It is quite essential that the fluctuations in rate must themselves be power-law distributed. As a clear example of how this breaks down, consider a Poisson rate that varies according to a sine wave with fixed period and amplitude. In this case, the avalanche size distribution is definitely not scale-free, it would have a clear typical scale. Another point of view on this comes from some of the simplest models used to study criticality – e.g. all-to-all connected probabilistic binary neurons (like in Shew et al 2009 J Neurosi). These models do generate spiking with a time-varying Poisson rate when they are at criticality or away from criticality. But, only when the synaptic strength is tuned to criticality is the time-varying rate going to generate power-law distributed avalanches. I think the Priesmann & Shriki paper made this point as well.

My second reservation has to do with the generality of the conclusions drawn from the mechanistic model. One of the connectivity motifs identified appears to be i+ to e- and i- to e+, where potentially i+/i- are SOM and VIP (or really any specific inhibitory type) cells. The specific connections to subsets of excitatory cells appear to be important (based on the solid lines in Figure 8). This seems surprising: is there any experimental support for excitatory cells to preferentially receive inhibition from either SOM or VIP, but not both?

R2b: There is indeed direct experimental support for the competitive relationship between SOM, VIP, and functionally distinct groups of excitatory neurons. This was shown in the paper by Josh Trachtenberg’s group: Garcia-Junco-Clemente et al 2017. An inhibitory pull-push circuit in frontal cortex. Nat Neurosci 20:389–392. However, we emphasize that we also showed (lower left motif in Fig 8G) that a simpler model with only one inhibitory group is sufficient to explain the anticorrelations and scale-free dynamics we observe. We opted to highlight the model with two inhibitory groups since it can also account for the Garcia-Junco-Clemente et al results.

In the section where we describe the model, we state, “We considered two inhibitory groups, instead of just one, to account for previous reports of anticorrelations between VIP and SOM inhibitory neurons in addition to anticorrelations between groups of excitatory neurons (Garcia-Junco-Clemente et al., 2017).”

More broadly, I wonder if the neat diagrams drawn here are misleading. The sample raster, showing what appears to be the full simulation, certainly captures the correlated/anti-correlated pattern of the 100 cells most correlated with a seed cell and 100 cells most anti-correlated with it, but it does not contain the 11,000 cells in between with zero to moderate levels of correlation.

R2c: We agree that our original model has several limitations and that one of the most obvious features lacking in our model is asynchronous neurons (The limitations are now discussed more openly in the last paragraph of the model subsection). In the data from the Garcia-Junco-Clemente et al paper above there are many asynchronous neurons as well. To ameliorate this limitation, we have now created a modified model that now accounts for asynchronous neurons together with the competing anticorrelated neurons (now shown and described in Fig S9). We put this modified model in supplementary material and kept the simpler, original model in the main findings of our work, because the original model provides a simpler account of the features of the data we focused on in our work – i.e. anticorrelated scale-free fluctuations. The addition of the asynchronous population does not substantially change the behavior of the two anticorrelated groups in the original model.

We probably expect that the full covariance matrix has similar structure from any seed (see Meshulam et al. 2019, PRL, for an analysis of scaling of coarse-grained activity covariance), and this suggests multiple cross-over inhibition constraints, which seem like they could be hard to satisfy.

R2d: We agree that it remains an outstanding challenge to create a model that reproduces the full complexity of the covariance matrix. We feel that this challenge is beyond the scope of this paper, which is already arguably squeezing quite a lot into one manuscript (one reviewer already suggested removing figures!).

We added a paragraph at the end of the subsection about the model to emphasize this limitation of the model as well as other limitations. This new paragraph says:

While our model offers a simple explanation of anticorrelated scale-free dynamics, its simplicity comes with limitations. Perhaps the most obvious limitation of our model is that it does not include neurons with weak correlations to both e+ and e- (those neurons in the middle of the correlation spectrum shown in Fig 7B). In Fig S9, we show that our model can be modified in a simple way to include asynchronous neurons. Another limitation is that we assumed that all non-zero synaptic connections were equal in weight. We loosen this assumption allowing for variable weights in Fig S9, without changing the basic features of anticorrelated scale-free fluctuations. Future work might improve our model further by accounting for neurons with intermediate correlations.

The motifs identified in Fig. 8 likely exist, but I am left with many questions of what we learned about connectivity rules that would account for the full distribution of correlations. Would starting with an Erdos-Renyi network with slight over-representation of these motifs be sufficient? How important is the homogeneous connection weights from each pool assumption - would allowing connection weights with some dispersion change the results?

R2e: First, we emphasize that our specific goal with our model was to identify a possible mechanism for the anticorrelated scale-free fluctuations that played the key role in our analyses. We agree that this is not a complete account of all correlations, but this was not the goal of our work. Nonetheless, our new modified model in Fig S9 now accounts for additional neurons with weak correlations. However, we think that future theoretical/modeling work will be required to better account for the intermediate correlations that are also present in the experimental data.

We confirmed that an Erdo-Renyi network of E and I neurons can produce scale-free dynamics, but cannot produce substantial anticorrelated dynamics (Fig 8G, top right motif). Additionally, the parameter space study we performed with our model in Fig 8 showed that if the interactions between the two excitatory groups exceed a certain tipping point density, then the model behavior switches to behavior expected from an Erdos-Renyi network (Fig 8F). Finally, we have now confirmed that some non-uniformity of synaptic weights does not change the main results (Fig S9). In the model presented in Fig S9, the value of each non-zero connection weight was drawn from a uniform distribution [0,0.01] or [-0.01,0] for excitatory and inhibitory connections, respectively. All of these facts are described in the model subsection of the paper results.

As a whole, this paper has the potential to make an impact on how large-scale neural and behavioral recordings are analyzed and interpreted, which is of high interest to a large contingent of the field.

Reviewer #3 (Public Review):

The primary goal of this work is to link scale free dynamics, as measured by the distributions of event sizes and durations, of behavioral events and neuronal populations. The work uses recordings from Stringer et al. and focus on identifying scale-free models by fitting the log-log distribution of event sizes. Specifically, the authors take averages of correlated neural sub-populations and compute the scale-free characterization. Importantly, neither the full population average nor random uncorrelated subsets exhibited scaling free dynamics, only correlated subsets. The authors then work to relate the characterization of the neuronal activity to specific behavioral variables by testing the scale-free characteristics as a function of correlation with behavior. To explain their experimental observation, the authors turn to classic e-i network constructions as models of activity that could produce the observed data. The authors hypothesize that a winner-take-all e-i network can reproduce the activity profiles and therefore might be a viable candidate for further study. While well written, I find that there are a significant number of potential issues that should be clarified. Primarily I have main concerns: 1) The data processing seems to have the potential to distort features that may be important for this analysis (including missed detections and dynamic range), 2) The analysis jumps right to e-i network interactions, while there seems to be a much simpler, and more general explanation that seems like it could describe their observations (which has to do with the way they are averaging neurons), and 3) that the relationship between the neural and behavioral data could be further clarified by accounting for the lop-sidedness of the data statistics. I have included more details below about my concerns below.

Main points:

1) Limits of calcium imaging: There is a large uncertainty that is not accounted for in dealing with smaller events. In particular there are a number of studies now, both using paired electro-physiology and imaging [R1] and biophysical simulations [R2] that show that for small neural events are often not visible in the calcium signal. Moreover, this problem may be exacerbated by the fact that the imaging is at 3Hz, much lower than the more typical 10-30Hz imaging speeds. The effects of this missing data should be accounted for as could be a potential source of large errors in estimating the neural activity distributions.

R3a: We appreciate the concern here and agree that event size statistics could in principle be biased in some systematic way due to missed spikes due to deconvolution of Ca signals. To directly test this possibility, we performed a new analysis of spike data recorded with high time resolution electrophysiology. We began with forward-modeling process to create a low-time-resolution, Ca-like signal, using the same deconvolution algorithm (OASIS) that was used to generate the data we analyzed in our work here. In agreement with the reviewer’s concern, we found that spikes were sometimes missed, but the loss was not extreme and did not impact the neural event size statistics in a significant way compared to the ground truth we obtained directly from the original spike data (with no loss of spikes). This new work is now described in a new paragraph at the end of the subsection of results related to Fig 3 and in a new Fig S3. The new paragraph says…

Two concerns with the data analyzed here are that it was sampled at a slow time scale (3 Hz frame rate) and that the deconvolution methods used to obtain the data here from the raw GCAMP6s Ca imaging signals are likely to miss some activity (Huang et al., 2021). Since our analysis of neural events hinges on summing up activity across neurons, could it be that the missed activity creates systematic biases in our observed event size statistics? To address this question, we analyzed some time-resolved spike data (Neuropixel recording from Stringer et al 2019). Starting from the spike data, we created a slow signal, similar to that we analyzed here by convolving with a Ca-transient, down sampling, deconvolving, and z-scoring (Fig S3). We compared neural event size distributions to “ground truth” based on the original spike data (with no loss of spikes) and found that the neural event size distributions were very similar, with the same exponent and same power-law range (Fig S3). Thus, we conclude that our reported neural event size distributions are reliable.

However, although loss of spikes did not impact the event size distributions much, the time-scale of measurement did matter. As discussed above and shown in Fig S4, changing from 5 ms time resolution to 330 ms time resolution does change the exponent and the range of the power law. However, in the test data set we worked with, the existence of a power law was robust across time scales.

2) Correlations and power-laws in subsets. I have a number of concerns with how neurons are selected and partitioned to achieve scale-free dynamics. 2a) First, it's unclear why the averaging is required in the first place. This operation projects the entire population down in an incredibly lossy way and removes much of the complexity of the population activity.

R3b: Our population averaging approach is motivated by theoretical predictions and previous work. According to established theoretical accounts of scale-free population events (i.e. non-equilibrium critical phenomena in neural systems) such population-summed event sizes should have power law statistics if the system is near a critical point. This approach has been used in many previous studies of scale-free neural activity (e.g. all of those cited in the introduction in relation to scale-free neuronal avalanches). One of the main results of our study is that the existing theories and models of critical dynamics in neural systems fail to account for small subsets of neurons with scale-free activity amid a larger population that does not conform to these statistics. We could not make this conclusion if we did not test the predictions of those existing theories and models.

2b) Second, the authors state that it is highly curious that subsets of the population exhibit power laws while the entire population does not. While the discussion and hypothesizing about different e-i interactions is interesting I believe that there's a discussion to be had on a much more basic level of whether there are topology independent explanations, such as basic distributions of correlations between neurons that can explain the subnetwork averaging. Specifically, if the correlation to any given neuron falls off, e.g., with an exponential falloff (i.e., a Gaussian Process type covariance between neurons), it seems that similar effects should hold. This type of effect can be easily tested by generating null distributions using code bases such as [R3]. I believe that this is an important point, since local (broadly defined) correlations of neurons implying the observed subnetwork behavior means that many mechanisms that have local correlations but don't cluster in any meaningful way could also be responsible for the local averaging effect.

R3c: We appreciate the reviewer’s effort, trying out some code to generate a statistical model. We agree that we could create such a statistical model that describes the observed distribution of pairwise correlations among neurons. For instance, it would be trivial to directly measure the covariance matrix, mean activities, and autocorrelations of the experimental data, which would, of course, provide a very good statistical description of the data. It would also be simple to generate more approximate statistical descriptions of the data, using multivariate gaussians, similar to the code suggested by the reviewer. However, we emphasize, this would not meet the goal of our modeling effort, which is mechanistic, not statistical. The aim of our model was to identify a possible biophysical mechanism from which emerge certain observed statistical features of the data. We feel that a statistical model is not a suitable strategy to meet this aim. Nonetheless, we agree with the reviewer that clusters with sharp boundaries (like the distinction between e+ an e- in our model) are not necessary to reproduce the cancelation of anticorrelated neurons. In other words, we agree that sharp boundaries of the e+ and e- groups of our model are not crucial ingredients to match our observations.

2c) In general, the discussion of "two networks" seems like it relies on the correlation plot of Figure~7B. The decay away from the peak correlation is sharp, but there does not seem to be significant clustering in the anti-correlation population, instead a very slow decay away from zero. The authors do not show evidence of clustering in the neurons, nor any biophysical reason why e and i neurons are present in the imaging data.

R3d: First a small reminder: As stated in the paper, the data here is only showing activity of excitatory neurons. Inhibitory neurons are certainly present in V1, but they are not recorded in this data set. Thus we interpret our e+ and e- groups as two subsets of anticorrelated excitatory neurons, like those we observed in the experimental data. We agree that our simplified model treats the anticorrelated subsets as if they are clustered, but this clustering is certainly not required for any of the data analyses of experimental data. We expect that our model could be improved to allow for a less sharp boundary between e+ and e- groups, but we leave that for future work, because it is not essential to most of the results in the paper. This limitation of the model is now stated clearly in the last paragraph of the model subsection.

The alternative explanation (as mentioned in (b)) is that the there is a more continuous set of correlations among the neurons with the same result. In fact I tested this myself using [R3] to generate some data with the desired statistics, and the distribution of events seems to also describe this same observation. Obviously, the full test would need to use the same event identification code, and so I believe that it is quite important that the authors consider the much more generic explanation for the sub-network averaging effect.

R3e: As discussed above, we respectfully disagree that a statistical model is an acceptable replacement for a mechanistic model, since we are seeking to understand possible biophysical mechanisms. A statistical model is agnostic about mechanisms. We have nothing against statistical models, but in this case, they would not serve our goals.

To emphasize our point about the inadequacy of a statistical model for our goals, consider the following argument. Imagine we directly computed the mean activities, covariance matrix, and autocorrelations of all 10000 neurons from the real data. Then, we would have in hand an excellent statistical model of the data. We could then create a surrogate data set by drawing random numbers from a multivariate gaussian with same statistical description (e.g. using code like that offered by reviewer 3). This would, by construction, result in the same numbers of correlated and anticorrelated surrogate neurons. But what would this tell us about the biophysical mechanisms that might underlie these observations? Nothing, in our opinion.

2d) Another important aspect here is how single neurons behave. I didn't catch if single neurons were stated to exhibit a power law. If they do, then that would help in that there are different limiting behaviors to the averaging that pass through the observed stated numbers. If not, then there is an additional oddity that one must average neurons at all to obtain a power law.

R3f: We understand that our approach may seem odd from the point of view of central-limit-theorem-type argument. However, as mentioned above (reply R3b) and in our paper, there is a well-established history of theory and corresponding experimental tests for power-law distributed population events in neural systems near criticality. The prediction from theory is that the population summed activity will have power-law distributed events or fluctuations. That is the prediction that motivates our approach. In these theories, it is certainly not necessary that individual neurons have power-law fluctuations on their own. In most previous theories, it is necessary to consider the collective activity of many neurons before the power-law statistics become apparent, because each individual neurons contributes only a small part to the emergent, collective fluctuations. This phenomenon does not require that each individual neuron have power-law fluctuations.

At the risk of being pedantic, we feel obliged to point out that one cannot understand the peculiar scale-free statistics that occur at criticality by considering the behavior of individual elements of the system; hence the notion that critical phenomena are “emergent”. This important fact is not trivial and is, for example, why there was a Nobel prize awarded in physics for developing theoretical understanding of critical phenomena.

3) There is something that seems off about the range of \beta values inferred with the ranges of \tau and $\alpha$. With \tau in [0.9,1.1], then the denominator 1-\tau is in [-0.1, 0.1], which the authors state means that \beta (found to be in [2,2.4]) is not near \beta_{crackling} = (\alpha-1)/(1-\tau). It seems as this is the opposite, as the possible values of the \beta_{crackling} is huge due to the denominator, and so \beta is in the range of possible \beta_{crackling} almost vacuously. Was this statement just poorly worded?

R3g: The point here is that theory of crackling noise predicts that the fit value of beta should be equal to (1-alpha)/(1-tau). In other words, a confirmation of the theory would have all the points on the unity line in the rightmost panels of Fig9D and 9E, not scattered by more than an order of magnitude around the unity line. (We now state this explicitly in the text where Fig 9 is discussed.) Broad scatter around the unity line means the theory prediction did not hold. This is well established in previous studies of scale-free brain dynamics and crackling noise theory (see for example Ma et al Neuron 2019, Shew et al Nature Physics 2015, Friedman et al PRL 2012). A clearer single example of the failure of the theory to predict beta is shown in Fig 5A,B, and C.

4) Connection between brain and behavior:

4a) It is not clear if there is more to what the authors are trying to say with the specifics of the scale free fits for behavior. From what I can see those results are used to motivate the neural studies, but aside from that the details of those ranges don't seem to come up again.

R3h: The reviewer is correct, the primary point in Fig 2 is that scale-free behavioral statistics often exist. Beyond this point about existence, reporting of the specific exponents and ranges is just standard practice for this kind of analysis; a natural question to ask after claiming that we find scale behavior is “what are the exponents and ranges”. We would be remiss not to report those numbers.

4b) Given that the primary connection between neuronal and behavioral activity seems to be Figure~4. The distribution of points in these plots seem to be very lopsided, in that some plots have large ranges of few-to-no data points. It would be very helpful to get a sense of the distribution of points which are a bit hard to see given the overlapping points and super-imposed lines.

R3i: We agree that this whitespace in the figure panels is a somewhat awkward, but we chose to keep the horizontal axis the same for all panels of Fig 4B, because this shows that not all behaviors, and not all animals had the same range of behavioral correlations. We felt that hiding this was a bit misleading, so we kept the white space.

4c) Neural activity correlated with some behavior variables can sometimes be the most active subset of neurons. This could potentially skew the maximum sizes of events and give behaviorally correlated subsets an unfair advantage in terms of the scale-free range.

Author Response

Reviewer #1 (Public Review):

In this article, the authors are trying to ascertain how emigrated SVZ cells can be beneficial - via neuroreplacement or neuroprotection. They provide evidence for the latter and also show that it is primarily precursors and not differentiated cells that migrate to photo-thrombotic cortical models of stroke.

The writing is lucid and the flow of the experiments logical. The images and quality of data are high and the depth of investigation appropriate (eg 100 cells examined per marker in Figure 1). The methods are clearly described. They appropriately control for changes in cortical lesion size. The photo-thrombotic lesion is a good choice in terms of controlling lesion placement and size.

A distinctive advantage of this paper is they show that reducing SVZ cytogenesis in the stroke model diminishes recovery, especially behavioural (single seed reaching behavior). This essential experiment has been remarkably under-utilized in the field.

The 2-photon imaging of dendric spines after stroke combined with multi-exposure speckle imaging is a technical tour-de-force especially since they combine it with ganciclovir-induced loss of cytogenesis and behavioural assays. Importantly, they show that SVZ cells are needed for full spine plasticity.

They are correct to examine the SVZ response in aging as it diminishes dramatically in animal models but in humans is associated with more strokes. As expected, they show reduced SVZ proliferation after stroke. This was associated with significantly worse performance in the seed-reaching task and depleting SVZ precursors with ganciclovir did not make it worse.

The viral VEGF delivery rescue experiment is fantastic. Behavior, blood vessel growth, and spine density are all rescued.

The idea that SVZ cells are beneficial via mechanisms other than cell replacement is not really that new. For example, neural stem cells from the SVZ have been shown to reduce inflammation and thereby be neuroprotective as the authors themselves acknowledge and cite (Pluchino et al., 2005).

The fact that it is primarily precursor cells that migrate towards the stroke does not mean that cell replacement does not occur. The precursors could gradually differentiate (even after 6 weeks post-injury) into more mature cells that do replace cells lost to injury. Also, the two events are not mutually exclusive.

Our findings indicate that there is no appreciable differentiation of SVZ-derived cells up to 6 weeks after stroke. By this time, we find complete recovery of behavioral deficits. While it is conceivable that cells may differentiate after this timepoint, such a phenomenon would not be contributing to recovery.

Overall this is an interesting addition to the literature and methodologically it is quite strong. It is sure to generate follow on studies showing how different growth factors may be secreted by SVZ cells in various models of neurological disease.

Reviewer #3 (Public Review):

Williamson et al. have investigated the role of cells derived from a neural stem cell (NSC) region of the adult mouse brain called the subventricular zone (SVZ) in a model of stroke. The authors labeled SVZ cells with Nestin-CreER and the Ai14 (tdTomato) reporter, induced cortical infarcts 4 weeks later, then analyzed brains 2 weeks thereafter. Most of the tdTomato+ cells in the peri-infarct regions were not neurons but less differentiated neural precursor cells. They then ablated proliferating NSCs in the SVZ with GFAP-TK mice and ganciclovir (GCV) administration, and this reduced SVZ-derived peri-stroke cells and impaired motor recovery. Older mice have less proliferation in the SVZ, and these older mice have fewer peri-infarct SVZ-derived cells and worse recovery than younger mice. Using multi-exposure speckle imaging (MESI) and 2 photon imaging, the authors found that ablation of proliferating SVZ cells reduced vascular remodeling and synaptic turnover in peri-infarct areas. Immunohistochemical analysis revealed the expression of VEGF, BDNF, GDNF, and FGF2. The authors selected VEGF for functional studies, conditionally knocking out VEGF in SVZ cells and finding that this reduced recovery and neuronal spine density. Finally, the authors expressed VEGF by AAV vectors in mice with ablated SVZ, finding that VEGF could improve repair and recovery after stroke.

The results presented in the paper support some of the authors' general conclusions and may be of interest to investigators of adult mouse SVZ. The use of genetic labels for lineage analysis and studies of VEGF conditional knockout in SVZ cells are technical strengths of the study. The results support the idea that VEGF in SVZ cells is important for recovery from stroke in younger adult mice. However, the impact of the work may be somewhat limited, as outlined below.

1. It is already well known that VEGF is an important aspect of stroke recovery (at least in rodent models), and that ectopic expression of VEGF can be beneficial. Showing that some of the VEGF in peri-stroke regions might come from SVZ-derived cells would be a relatively incremental discovery.

We disagree. In our view, the identification of SVZ-derived cells as a major cellular source of an important trophic factor for recovery is itself an important finding. We also demonstrate that VEGF produced by this cell population is necessary for effective neural repair and recovery, while replacement of VEGF is sufficient to induce repair and recovery in mice lacking this cell population. Moreover, these findings provide a compelling explanation for the worsening of recovery and diminishment of repair that occurs with age (i.e., loss of VEGF signaling from the neural stem cell lineage). Finally, the demonstration that replacing VEGF rescues deficits that accompany loss of SVZ stem cells provides rationale for the replacement of neural stem cell lineage factors as a potential treatment.

The molecular mechanism aside, our main goal was to understand the function of SVZ cytogenesis in stroke recovery. Our findings that 1) the majority of cells arising from the SVZ after stroke remain in an undifferentiated state, 2) these cells facilitate neuronal and vascular reparative processes in order to promote recovery, and 3) very few new neurons are produced during the recovery phase, provide a new and unexpected understanding of the purpose of post-injury cytogenesis. The dogma of past literature is that neural stem cells produce new neurons that mature and integrate into damaged circuits after injury. An implication of this dogma is that neuronal replacement after stroke is an important treatment target. Accordingly, substantial effort has been devoted to developing cell transplantation and conversion treatment strategies to create new neurons. Our study reframes the function of newborn cells in stroke recovery and provides a compelling rationale against treatment strategies aimed at replacing neurons, instead demonstrating that trophic factor mediated repair and remodeling of spared tissue is sufficient for profound recovery of function. To emphasize these important findings, we have expanded our discussion (lines 338-378).

1. Furthermore, while it seems clear that the VEGF conditional knockout (VEGF-cKO) in SVZ cells reduces behavioral recovery and certain histological measures, it is not clear that these impairments are due to a lack of VEGF delivery from the SVZ cells. It is possible that VEGF-cKO changed the proportion of SVZ cells that arrive in the peri-stroke region. It is also possible that VEGF-cKO makes these cells impaired in the expression of other trophic factors.

We disagree with this interpretation. We used a cell type-specific, inducible knockout of VEGF to examine the function of VEGF produced by the adult neural stem cell lineage after stroke. We show in Figure 6E that numbers of lineage traced cells are not different between control and cKO mice. We have added new data, as Figure 6 – figure supplement 2, showing that the proportion of Ascl1-expressing cells is not different between groups, indicating that there is no change in the amount of differentiation. We have also added staining demonstrating that VEGF cKO cells still express GDNF, BDNF, and FGF-2 (Figure 6 – figure supplement 2). Notably, we did not detect a decrease in these three proteins in peri-infarct regions in mice in which neural stem cells were ablated, suggesting that while SVZ-derived cells do produce them, their production is small relative to other cell types. VEGF is thus unique in that large quantities of it are produced by SVZ-derived cells. We also provide evidence for direct effects of VEGF on other cell types (rather than cell-autonomous effects of VEGF regulating other factors in SVZ-derived cells that then act on other cell types) since restoring VEGF in mice with ablated neural stem cells rescued repair and recovery. Importantly, even if VEGF cKO led to perturbed expression of some other proteins, our conclusion would still be that VEGF produced by SVZ-derived cells is crucial for promoting repair and recovery.

1. The cytogenic response to stroke was not characterized in much detail at the cellular level. Essentially only one time point (2 weeks) was selected for immunohistochemistry (Fig. 1), and so the dynamics of this response cannot be evaluated. Does the proportion of cell types change over time? Are migratory cells more homogeneous and then diversify after arrival to the peri-stroke region? At longer time points, do these SVZ-derived cells still exist? Such an analysis is important to the story since the behavior was evaluated at a range of time points (3-28 days after stroke), and recovery was noted as early as 7 days. Are SVZ-derived cells already at the peri-stroke area after 7 days? If they are not already there, then how would the recovery be explained? The behavioral recovery also continues to improve at 28 days; are SVZ-derived cells still present in large numbers at that time? How would the authors explain continued recovery if the SVZ-derived cell population drops away after 2 weeks?

Thank you for these suggestions – we agree that these are important points to address. In our original submission we provided evidence that there is no significant differentiation into neurons even 6 weeks after stroke. We have added additional data (Figure 1-figure supplement 2) in which we assessed expression of a range of markers at 6 weeks post-stroke, a time by which recovery is typically complete in this model. These new data show that cell type distribution of lineage traced cells at 6 weeks is highly similar to the 2-week timepoint and show that little differentiation occurs during the course of recovery. We have also included new data quantifying numbers of SVZ-derived cells in peri-infarct cortex at 1, 2, and 6 weeks post-stroke. These data show that lineage traced cells are abundant by day 7 and numbers increase progressively to 6 weeks, suggesting that these cells are present when we initially detect functional improvement, survive, and are continuously produced during the course of recovery. Finally, we have added data showing that the proportion of Ascl1-expressing cells does not change from 1 to 6 weeks, which is consistent with the idea that there are no dynamic changes in cell phenotype during recovery.

1. The SVZ-derived peri-stroke cells were not characterized in much detail at the molecular/transcriptomic level. The authors studied 4 trophic factors by antibody staining, but there are many other potential genes that may contribute to the effect. Transcriptomic analyses of SVZ-derived peri-stroke cells (e.g., by single-cell RNA-seq) may provide deeper insights into potential mechanisms.

We acknowledge that single-cell RNA sequencing of SVZ-derived cells may reveal other interesting molecular mechanisms, but such a study could easily stand on its own. There are also technical limitations, such as the population of cells being relatively small, that would create difficulty in generating such a dataset. Instead, we focused on protein-level expression of a small cohort of factors that could be potentially involved based on our initial findings and past literature. In particular, we focused on examining proteins known to potently drive angiogenesis, axon outgrowth, and/or synapse formation given our findings of deficient vascular and synaptic repair in mice lacking cytogenesis. Even if single cell sequencing provided new molecular targets, the ensuing workflow would mirror what we have done in our study (validation of protein level expression, loss-of-function manipulation, gain-of-function manipulation). The magnitude of deficits in VEGF cKO mice did not completely match that seen in mice in which neural stem cells were ablated, making it likely that SVZ-derived cells also contribute to recovery by other mechanisms. We have added to the discussion: “Importantly, these past studies have identified an array of factors produced by precursor cells depending on context. It is possible that multiple factors produced by SVZ-derived cells promote recovery after stroke. This is suggested by our finding that recovery is worse in mice with ablated neural stem cells compared with VEGF cKO mice. Thus, future studies could examine other molecular targets. These efforts could be aided by techniques such as single-cell RNA sequencing.” (lines 338 - 343).

1. The significance of this work for understanding stroke in human patients is unclear since the adult human brain SVZ is essentially devoid of neurogenic stem cells. Thus, although some of the observations in this paper are interesting, the cytogenic response to stroke described here may not occur in human patients.

We disagree for several reasons. First, while there is an ongoing debate on whether neurogenesis or neural stem cells persist in adult humans, this debate has not been resolved. At least in our opinion, the preponderance of evidence is in support of persistent cytogenesis and neural stem cells in the adult human SVZ due to convincing data across many studies (e.g., PMID: 10328940, 9809557, 14973487, 11333968, 10870078, 24561062). While it appears that neural stem cell proliferation declines with aging, as in rodents, there is evidence of increased SVZ proliferation and cytogenesis in response to stroke in adult and elderly humans (e.g., PMID: 20054008, 16924107, 17167100, 20104652). Thus, although it is exceedingly difficult to study in humans, it is likely that neural stem cells persist in the adult human brain and can respond to injury by producing new cells. One reason for the somewhat sparse evidence of post-stroke cytogenesis in humans may be that the focus of past studies has been on finding new neurons. Importantly, our study demonstrates that other cells types, especially undifferentiated precursors, arise from the SVZ after stroke in far greater numbers than neurons, which may spur further examination of the phenomenon in humans.

Second, while stroke incidence increases with age, stroke is not uncommon in the young. Moreover, incidence of stroke in the young is increasing (PMID: 32015089). It is generally accepted that young humans have intact neural stem cells, and the phenomenon we describe in our study shows clear benefits of SVZ cytogenesis in young mice.

Third, our study provides evidence that “neurogenic” capacity of neural stem cells may not be important for the beneficial functions of cytogenesis after injury. The overwhelming majority studies in humans and mice have focused on “neurogenesis”. Our study demonstrates that undifferentiated precursors constitute the majority of SVZ-derived cells after stroke and identifies Ascl1 as a marker of them, which may be useful for identifying these cells in humans.

Fourth, if neural stem cell numbers are substantially reduced in aged humans, as in rodents, our study provides clear rationale for the development of treatments to restore stem cell numbers/activation or limit their decline with aging.

Fifth, our study not only identifies VEGF as a mechanism by which SVZ-derived cells promote repair and recovery after stroke, but also demonstrates that replacing VEGF is sufficient to improve repair and recovery in mice lacking neural stem cells. Thus, even if the argument that cytogenesis does not occur in adult or elderly humans is true, our study shows that identification and replacement of factors produced by the neural stem cell lineage, such as VEGF, could be a reasonable treatment strategy with clear translational potential.

In order to more clearly state these points in the manuscript, we have expanded our discussion of them.

Author Response

Reviewer #1 (Public Review):

In this study, Scalabrino et al. show persistent cone-mediated RGC signaling despite changes in cone morphology and density with rod degeneration in CNGB1 mouse model of retinitis pigmentosa. The authors use a linear-nonlinear receptive field model to measure functional changes (spatial and temporal filters and gain) across the RGC populations with space-time separable receptive fields. At mesopic and photopic conditions, receptive field changes were minor until rod death exceeded 50%; while response gain decreased with photoreceptor degeneration. Using information theory, the authors evaluated the fidelity of RGC signaling demonstrated that mutual information decreased with rod loss, but cone-mediated RGC signaling was relatively stable and was more robust for natural movies than artificial stimulus. This work reveals the preservation of cone function and a robustness in encoding natural movies across degeneration. This manuscript is the first demonstration of using information theory to evaluate the effects of neural degeneration on sensory coding. The study uses a systematic evaluation of rod and cone function in this model of rod degeneration to make the following findings: (1) cone function persists for 5-7 months, (2) spatial and temporal changes to the ganglion cell receptive fields were not monotonic with time, (3) mutual information between spikes and photopic stimuli remained relatively constant up to 3-5 months, and (4) information rates were higher for natural movies than for checkerboard noise stimuli.

The strengths of this paper include the following:

A systemic evaluation of potentially confusing data. The authors do an excellent job of organizing the results in terms of light levels and time points. The results themselves are confusing and difficult to draw across metrics, but the data are presented as clearly as possible. The work is especially well executed and presented.

The insight that cone responses remain relatively stable despite rod loss. The study clearly demonstrates that despite cone loss and morphological changes, cone-mediated responses remain robust and functional.

The application of information theory to degeneration is the first of its kind and the study clearly shows the utility of the metric.

The results are thoughtfully interpreted.

We thank the reviewer for these comments.

The weaknesses of this study include the following:

The inability to follow the same ganglion cell types over time is a major weakness that could confound the interpretation in terms of whether the changes are happening from artifacts of the recording method or from dynamic changes in the pooled population of ganglion cells. Is there even a single cell class, for example the ON-OFF direction-selective ganglion cells, that this group has so well quantified on the MEA, that the study could track over time, in addition to examining the pooled population changes over time? Tracking a single cell type for each of the metrics would make the population data more convincing or could clearly show that not all ganglion cells follow the population trend.

As suggested by the reviewer, we have added a cell type that is tracked through all the analyses: ON brisk sustained RGCs. Example receptive field mosaics, temporal receptive fields, and spike train autocorrelation functions for WT and 4M Cngb1neo/neo animals are shown in Figure 2-figure supplement 1E-F. These RGCs follow the trends displayed by the larger populations of RGCs in each analysis. We chose this cell type because they are readily identified by their spike train autocorrelation functions compared to other RGC types and they have approximately space-time separable receptive fields (RFs). There are many text changes associated with adding an analysis of the ON Brisk sustained RGCs (see lines 202-207; 227-229; 264-267, etc).

We chose not to focus on direction selective RGCs because we are analyzing the spatial and temporal RFs of RGCs in Figures 3-5 and direction-selective RGCs do not have space-time separable RFs (see example in Figure 2C-D). Thus, those cells could not be used to track those receptive field properties across degeneration. Also, we did not collect responses to drifting gratings or bar responses across a range of speeds or contrasts, so we are unable to reliably distinguish the different types of direction-selective RGCs (e.g., ON vs ON-OFF) from these data.

While the non-monotonic changes are interesting, they are also difficult to make sense of. Can the authors speculate in the Discussion what could be underlying mechanisms that give rise to non-monotonic changes. In the absence of potential mechanisms, the concern of recording artifacts arises.

Thank you for raising this point. We have added some speculation for the cause of these non-monotonic changes in the Discussion (lines 455-462). “While we do not know why non-monotonic changes are occurring for some RF properties, they largely occurred in the 3-5M range. During this time, there is a transient decrease in the rate of rod death (4-5M) and cone death begins (Figure 1). Consequently, there may be complex changes to retinal circuitry as the retina reacts to a temporary stabilization in rod numbers and an acceleration in cone death. Intracellular studies of the light-driven synaptic currents impinging onto bipolar cells and RGCs during this time will be important for understanding the origin of these non-monotonic changes in RF properties.”

The mutual information calculation seems to be correlated with the spike rate despite the argument made in Fig 10E-F. Can the authors show this directly by calculating the bits per spike in Figures 8 and 9? Of all the metrics, the gain function and the mutual information seem to be more consistent with each other. Can the authors demonstrate or refute a connection between the spike rate and information rates?

We added a supplementary figure to each of the information figures (see for Figures 8-10 figure supplement 1) showing the trends hold after dividing the information rate by the spike rate. Certainly, changing spike rates are contributing, but there are also clear changes in the bits/spike plots (Figure 8-figure supplement 1D; Figure 9-figure supplement 1D, Figure 10-figure supplement 1D).

Can the authors provide an explanation for why the mutual information calculation remains stable despite lower SNR and lower gain, especially after the contributions of oscillations have been ruled out?

The mutual information depends more strongly on the precision of spiking (both in terms of time and spike number within a small time bin) than the mean spike rate (averaged over the stimulus). Diminishing the total number of spikes (because of reduced gain) will have a relatively small effect on the information rate if the spike trains continue to exhibit low variability (high precision). Indeed, spike generation by RGCs is distinctly sub-Poisson (Berry, Warland, and Meister 1997), indicating it can exhibit relatively high information rates even when spike rates are relatively low. We clarified this in Results at lines 493-496.

Lack of age-matched WT controls to accompany the different time points. It is known that photoreceptor degeneration can occur naturally in WT mice. Though the authors have used controls pooled from across the ages used in the CNGB1 mutants, it would be informative to know if there are age-dependent changes in any of the metrics for WT mice.

WT recordings were pooled from retinas from littermate control mice between 2 and 7 months of age (n=3 2M, n=1 each 4M, 6M, 7M). We have added data points from individual retinal recordings to the figure supplements for Figure 2-6 and 8-10 to illustrate the consistency between these recordings, which allowed us to confidently pool the results.

Can the authors elaborate on why cone function persists despite the rod loss and morphological changes? This is unique for other models of rod loss and is worth extra discussion.

This is something we are also very interested in, but outside the scope of this study. The Sampath Lab (co-author and collaborator) has data from single cell recordings in late stage rd10 retinas that show abnormal cone signaling (and structure similar to the 7M Cngb1neo/neo cones), yet relatively normal cone bipolar cell and horizontal cell responses. Thus, somehow there is either compensation or a high level of redundancy in the transmission of signals from cones to 2nd-order neurons that makes the responses of the 2nd-order neurons robust to deteriorating cone function. These results suggest our observations in Cngb1neo/neo mice are not unique to this model of RP. Future experiments are needed to understand how this compensation is occurring.

Reviewer #2 (Public Review):

In this study, the authors assess the decline of retinal function in a mouse model of slow photoreceptor degeneration - the Cngb1neo/neo. Rod loss occurs between 1-7 months and complete cone loss occurs by 8-9 months. The authors characterize cone loss in the first 7 months and find that 70% of cones are still there at 7 months, though their outer segments are highly degraded. They then use MEA recordings to characterize retinal function using a variety of measures. First, they use spike-triggered averaging to determine the spatial and temporal receptive fields, restricting this analysis to RGCs that have separable spatial and temporal receptive fields. They find that both rod and cone receptive fields are surprisingly intact over the first 5 months, identifying primarily a reduction in contrast response functions (and a reduction in the number of rods that are light responsive-though this is not quantified). Second, they show that oscillatory activity does not appear until after photoreceptors are completely deteriorated-in sharp contrast to other PR degeneration models (e.g. rd10) in which oscillatory activity appears while there are still light-evoked responses. Third, they use information theory to assess the reliability of signaling. When examining the 10% of RGCs with the highest information rates they see a significant decrease at mesoscopic light levels, while information rates were mostly stable at photopic light levels. Finally, they showed that at photopic light levels, the mutant retinas conveyed more information about natural movies than a repeating checkerboard, and this was maintained across light levels.

My primary question is whether this represents a significant advance. There have been many studies regarding the changing retinal circuits in various rodent models of photoreceptor degeneration. The authors make a few arguments regarding the uniqueness of this study.

One is that this is a novel analysis that is not limited to particular cell types but rather characterized the retinal as a "whole". But in this point is also its weakness. First, one cannot speak to the retinal as a "whole" since they state that there is a reduction in the number of light-responsive cells across degeneration - yet they do not quantify it. This seems incredibly important to know because even presuming the remaining cells have perfect receptive field structure if only 10% of cells are left, assessing the receptive fields of only the remaining cells is clearly not a characterization of the retention of visual function.

We never claim that we have assessed the “retina as a whole”. We do state that we are measuring certain features of RGC signaling that reflect the “net changes” induced by photoreceptor degeneration (e.g., changes in photoreceptor function, retinal rewiring, homeostatic mechanisms, etc.) on those features. In fact, we are explicit that we are only measuring certain RF properties in certain RGC types, such as the linear spatial and temporal RFs in cells with space-time separable RFs: Figure 2 makes this point explicitly. We do not measure changes in direction-selectivity, object motion sensitivity, orientation selectivity, edge detection, looming detection, luminance encoding, chromatic opponency, contrast adaptation, motion reversal signaling, etc., because doing so would produce a manuscript with at least one figure for every RGC type (e.g., 45 figures). This would clearly be an unreasonable amount for a single study.

We agree with the Reviewer that explicitly quantifying the number of light responsive RGCs is important, and we now include this information as a function of degeneration time point in Figure 2-figure supplement 1. Under photopic conditions, this fraction is quite stable until 5M and then begins to deteriorate. We also observe a decrease in the number of RGCs with space-time separable RFs at 5M (Figure 2F), suggesting (but not proving) that these RGCs are representative of changes across all RGCs. We also described these results in the Results (lines 167-174).

Second, it is hard to assess whether this mouse model is better than existing models for human disease. Their phenotype is different than the rat model of this same disease. It also shows a lack of oscillatory activity that is apparent in rd models.

We are not making the claim that this model is better than other models. Each model has value. However, because the degeneration in this model is relatively slow, it may be more representative of changes that occur in slower forms of human retinal degeneration (emphasis on “may be”). This is a discussion point, not something that we are aiming to prove. We also believe the utility of a model depends on the questions being asked. In this case, we aimed to track changes over time during photoreceptor loss to better understand the extent to which retinal output is impaired.

Also, retinitis pigmentosa is a heterogenous disease with a spectrum of phenotypes that may or may not be genotype specific. A patient with a PDE6B mutation presents with differing phenotypes than a patient with CNGB1 mutation, despite both having an RP diagnosis. It is fallacy to assume a mouse is the exact same as a human, just as it is incorrect to assume clinical presentations are identical for all patients for one broad disease that is known to have a diverse set of underlying causes. Studying a range of models is thus essential to understanding the disease. Given that mutations causing RP have different impacts on retinal signaling, we believe it is important to contextualize findings to their mutation. We make this point in Discussion: Comparison to previous studies of RGC signaling in retinitis pigmentosa (beginning on line 436).

Finally, the model we study does not lack oscillatory activity, it simply arises later than in rd1 or rd10 mice and does so only after all the photoreceptors have died (Figure 7). To our knowledge, it is not clear when or even if RGCs exhibit oscillations in human patients with RP. We discuss why oscillation might arise at different time points in different genetic models of RP in lines 555-570.

Reviewer #3 (Public Review):

In the manuscript by Scalabrino et al. a rigorous characterization of the functionality of retinal ganglion cells in a mouse model of rod photoreceptor degeneration is presented. The authors analyzed the degeneration of cone photoreceptors, which is known to be linked to rod degeneration. Based on the time course of cone degeneration they investigated the functional properties of retinal ganglion cells aged between 1 month and seven months.

The most interesting finding is robust preservation of functional properties, as reflected in little changes of the receptive fields (spatial and temporal characteristics) or signaling fidelity/information rate. In contrast to other mouse models, the present one shows no oscillatory activity until a complete loss of cone photoreceptors occurred at an age of nine months.

Although the receptive fields of retinal ganglion cells remain nearly intact, the number of ganglion cells with identifiable receptive fields decreases significantly with age (Fig.2F). Could the authors comment, if this might imply a "patchy" vision?

Visual field loss is a predominant clinical observation in patients with retinitis pigmentosa, including those with Cngb1 mutations. We connect to this observation in the Discussion at lines 521-529: “At the latest stages of photoreceptor degeneration in the Cngb1neo/neo mice (5-7M), we did observe a decrease in the fraction of RGCs with spike rates that were strongly modulated by checkerboard noise (Supplemental Figure 2). It is possible these RGCs were losing their light response completely, or that changes in their light response properties made them relatively unresponsive to checkerboard noise. If the former, it is possible that light responsive RGCs are becoming sparser at the later stages of degeneration which may result in inhomogeneous, or “patchy”, visual sensitivity described by RP patients (see reviews by Hull et al., 2017; Nassisi et al., 2021).”

Reviewer #4 (Public Review):

Scalabrino et al. report the remarkable persistence of cone-driven retinal ganglion cell responses in a mouse model of retinitis pigmentosa (i.e., Cngb1 KO mice). The authors first map the time course of primary rod and secondary cone degeneration in Cngb1 KO mice. Approximately 30% of rods are gone at one month (1M), and all rods are lost by 7M in Cngb1 KO retinas. The cone morphology changes progressively as rods degenerate, cone outer segments shrink and are largely absent by 5M. Cones die between 8-9M. Scalabrino et al. next perform multielectrode array recordings from wild-type and Cngb1 KO retinas from 1M to 5M in mesopic and photopic stimulus conditions. They find that spatiotemporal receptive fields remain relatively stable in the face of photoreceptor degeneration, whereas contrast gain gradually decreases. Oscillatory spontaneous ganglion cell activity emerges late (~9M) in Cngb1 KO mice compared to other retinal degeneration models. Finally, the authors analyze mutual information between stimuli (white noise and naturalistic movies) and ganglion cell spikes trains and find that the encoding of the most informative ganglion cells is preserved relatively late into photoreceptor degeneration and that information rates decline less in photopic vs. mesopic conditions and for naturalistic movies vs. white noise stimuli.

Overall, this is an exciting study that shows remarkable preservation of cone-driven ganglion cell light responses in advanced stages of a retinitis pigmentosa model when most rods have died, and cone morphologies are dramatically altered. The results are presented clearly in the text and figures and are scholarly discussed. Nonetheless, the authors should address a few specific comments to clarify and better support some of the conclusions they draw.

Specific comments:

1) In describing the results on information encoding, the authors write and show data (panels A of Figures 8-10) that suggest that most ganglion cells, even in recordings from wild-type retinas, respond unreliably to white noise stimuli and naturalistic movies. Why does such a large fraction of cells have such low repeat reliability? Does this reflect unreliable spike detection and sorting, poor cell or tissue health, or true variability in the responses of healthy retinal ganglion cells. The latter does not seem to align with results from patch-clamp recordings targeted to specific ganglion cell types. The limited repeat reliability also raises questions about how well the linear-nonlinear model, which the authors use to compare responses between wild-type and Cngb1 KO mice of different ages, predicts the responses of these cells. Comparing model parameters (receptive field size, temporal filtering, and contrast sensitivity) between genotypes and ages only makes sense if the model is a good description in the acquired datasets.

We agree with the reviewer that this is an important point to be clear about. In Figures 8-10 some RGCs exhibit high repeatability, some exhibit low repeatability as quantified by their information rates. The reviewer is concerned about those cells with low repeatability and the ability of capturing their responses with an LN model. This is a valid concern, but to be clear, we are not fitting an LN model to cells with low information rates. In Figures 3-6, where an LN model is being used to estimate the spatial and temporal components of the RFs, we are fitting a subset of all the RGCs: those with space-time separable RFs (see Figure 2). Those particular cells exhibit high information rates and highly reproducible responses, and an LN model captures ~60% of the explainable variance in the spike rate (see Figure 2-figure supplement 1A-B; also see lines 157-151). This is typical for LN models that approximately predict the responses of RGCs to checkerboard noise. Thus, we think the LN model reasonably captures the responses of cells for which we use the LN model. The information rate estimates include these cells as well as other cells that are not well described by an LN model. Note, the LN model is not used to calculate the mutual information rates. We have added text in the Results (lines 324-327) to clarify this.

In addition, the information rates we estimated in mouse are consistent with past studies from guinea pig (Koch et al, 2004 and Koch et al, 2006). We think cells with very low repeatability are not well driven by checkerboard noise or the particular 10s natural movies we showed. We have updated the example neurons to better reflect the reliability of the cells near the median of the MI distributions in Figures 8-10.

2) The authors should, maybe in figure supplements and parts of the main figures, break results down by recordings. Inter-experimental variability has been well documented (e.g., Shah et al. Neuron 2022, Zhao et al Sci Rep 2020), and it would be reassuring to see that the conclusions drawn by the authors are supported by statistics in which n = number of recordings (e.g., there is a somewhat difficult to explain broadening of temporal filters in 4M Cngb1 KO retinas that recover by 5M).

We agree that inter-experiment variability can be large and is important to control for. We now show all the analyses broken down by experiment in Supplemental Figures (2, 3, 4, 5, 6, 8, 9, and 10) for each analysis. None of the trends we describe or highlight in the manuscript were driven by inter-experiment variability.

3) At different points in their manuscript, the authors conclude that their results "suggest that homeostatic mechanisms in the retina serve to compensate for deteriorating photoreceptors" (or similar). I think that this may well be the case. However, in its present form, the study provides no evidence that retinal circuits in Cngb1 KO mice change to preserve function compared to the alternative that the observed stability is evidence for functional redundancy or resilience in retinal circuits (as they are) without the need for adjustments. Distinguishing between these alternatives would be conceptually important. For example, Care et al. Cell Rep 2019 and Care et al. Cell Rep 2020 used partial stimulation to activate fewer photoreceptors and compare light responses in downstream neurons to those in retinas with fewer photoreceptors. Other studies have directly observed changes in circuit wiring in models of retinal degeneration. If the authors cannot provide experimental evidence for homeostatic changes, it would be good to reflect this in the interpretation and discussion.

The reviewer raises a terrific point and potential alternative interpretation. We agree. We have not been able to identify an equivalent analysis to that in Care et al. 2019 that we can run that will cleanly distinguish between these two possibilities, without doing many more experiments across timepoints of degeneration. We have thus rewritten portions of the Introduction and the Discussion to recognize the potential of this alternative interpretation.

Introduction (lines 39-44): Alternatively, homeostatic plasticity or redundancy in retinal circuitry may compensate for photoreceptor loss (Care et al., 2020; Lee et al., 2021; Shen et al., 2020). Such mechanisms could facilitate reliable signaling at the level of retinal output, despite deterioration in photoreceptor function. Identifying the extent to which changes in photoreceptor morphology impact retinal output will inform treatment timepoints for gene therapies aimed at halting rod loss to preserve cone-mediated vision.

Discussion (lines 514-520): There are two potential classes of mechanisms for this compensation. First, homeostatic plasticity has been documented in models of photoreceptor loss in which the retina remodels to preserve signal transmission (Care et al., 2019; Keck et al., 2013, 2011, 2008; Leinonen et al., 2020; Shen et al., 2020). Alternatively, functional redundancy within the circuit could explain how robust retinal signaling is retained longer than the changes in cone morphology would suggest (Care et al., 2020). This study did not distinguish between the two compensation models.

4) The authors do not attempt to classify retinal ganglion cells into functional types as functional changes from degeneration may confound such classifications. However, it would be beneficial to separate some categorical response types (direction-selective ON-OFF and ON ganglion cells, maybe orientation-selective [horizontal, vertical, ON, OFF] ganglion cells) and compare how their responsiveness, reliability, and information encoding change with degeneration. This would provide additional insights and address concerns that changes caused by degeneration may be obscured by the differences between ganglion cell types in the present analysis.

We agree. We now track ON brisk sustained RGCs across degeneration time points for the RF analyses and mutual information analyses. These RGCs are likely the ON sustained alpha cells because they generate very large spikes on the MEA as would be expected for cells with large somata. Example receptive field mosaics, temporal receptive fields, and spike train autocorrelation functions for WT and 4M Cngb1neo/neo animals are shown in Figure 2-figure supplement 1E-F. These RGCs follow the trends displayed by the larger populations of RGCs in each analysis. We chose this cell type because they are readily identified by their spike train autocorrelation functions compared to other RGC types and they have approximately space-time separable receptive fields (RFs). There are many text changes associated with adding an analysis of the ON Brisk sustained RGCs (see lines 202-207; 227-229; 264-267, etc).

We chose not to focus on direction selective RGCs because we are analyzing the spatial and temporal RFs of RGCs in Figures 3-5 and direction-selective RGCs do not have space-time separable RFs (see example in Figure 2C-D). Thus, those cells could not be used to track those receptive field properties across degeneration. Also, we did not collect responses to drifting gratings or bar responses across a range of speeds or contrasts, so we are unable to reliably distinguish the different types of direction-selective RGCs (e.g., ON vs ON-OFF) from these data.

Author Response:

Reviewer 2 (Public Review):

Weaknesses 1. I had difficulty following the ANOVA results for Figure 1. I assume ANOVA was performed with factors of session and block. However, a single F statistic is reported. I do not know what this is referring to. It would be more appropriate to either perform repeated measures ANOVA with session and block as factors for each dependent variable or even better, multiple analyses of variance for the three dependent measures concurrently. Then report the univariate ANOVA results for each dependent measure. The graphs in Figure 1 (C-E) suggest a main effect of block, but as reported, I cannot tell if this is the case. Further, why was sex not included as an ANOVA factor?

For the sake of transparency, we had included plots showing sessions split by each block whereas statistics related to the right side bar plots where data are collapsed across risk (which was done to minimize effects from ‘missing’ data). We appreciate that this may have caused confusion. In the revised manuscript we specify the exact figure for each statistical result and have added a better description in the methods and updated the statistics (Table 1) with the ANOVA and post-hoc results.

Previously we had used a mixed effects model because one subject did not complete any risk trials in session 3 but in the revised manuscript, we decided to remove that subjects’ sessions to permit RM ANOVA. As requested by the reviewer, we performed a multivariate analysis on risk and no risk trials. Because of the repeated measures design we opted to utilize the multiple RM package developed by Friedrich et al. 2019, which permits multivariate analysis on repeated measures data with minimal assumptions and bootstrapped p-values for small sample sizes. We found significant interactions for session (or treatment) and risk (see tables below). This justifies the two-way univariate ANOVA which is now reported in the rest of the manuscript. Sex differences were not included in the ANOVA because the study was not intended to assess sex differences but, rather, was designed according to NIH requirements for inclusion of males and females.

Note: MATS test was utilized based on author recommendations in Friedrich et al., (2019) for when test violates singularity, which was reported. To replicate use a random seed of 8675309.

Package link: https://rdrr.io/github/smn74/MANOVA.RM/man/multRM.html Publication: Friedrich, S., Konietschke, F., & Pauly, M. (2019). Resampling-based analysis of multivariate data and repeated measures designs with the R package MANOVA. RM. R J., 11(2), 380.

1. The authors describe session 1 as characterized by 'overgeneralization' due to increased reward latencies. I do not follow this logic. Generalization typically refers to a situation in which a response to one action or cue extends to a second, similar action or cue. In the authors' design, there is only one cue and one action. I do not see how generalization is relevant here.

This wording has been changed to “non-specific” in the results and discussion.

1. The authors consistently report dmPFC and VTA 'neural activity'. The authors did not record neural activity. The authors recorded changes in fluorescence due to calcium influx into neurons. Even if these changes have similar properties to neural activity measured with single-unit recording, the authors did not record neural activity in this manuscript.

We do not imply that we recorded unit activity in these studies and state in the introduction that fiber photometry is an indirect measure of neural activity. We have also reworded much of the text in the manuscript to use “calcium activity.”

1. Comparing the patterns in Figures 2 and 3, it appears that dmPFC change in fluorescence was similar in non-shocked and shock trials up until shock delivery. However, the VTA patterns differ. No cue differences were observed for sessions 1-3 on shock trials (Figure 3A), yet differences were observed on non-shocked trials (Figure 2F). Further, changes in fluorescence between sessions 1 and 2/3 appeared to emerge just as foot shock would have been delivered. A split should be evident in Figure 3B - but it is not. Were these differences caused by sampling issues due to foot shock trials being rarer?

We agree, although some of this could be because footshock trials were collapsed across blocks 2 and 3 (as no differences in shock response was observed between blocks). Nevertheless, we have added a caveat about cue responses to the results (see page 11-bottom and 15-top). Regarding the lack of a split in Figure 3A – this difference may be due to shock onset time. The permutation tests indicate the differences in action activity in Figure 2B emerge about 0.5 – 0.8 seconds after action which is when the shock begins. So it is not surprising the results in 2F do not match well with 3A given the rapid and robust response to the footshock.

1. Similar to Figure 1, I could not follow the ANOVA results for the effects of diazepam treatment on trials completed, action latency and reward latency (Figure 4). Related, from what session do the bar plot data in Figure 4B come from? Is it the average of the 6% and 10% blocks? I cannot tell.

Please see our response in comment 1 for relevant analysis to this comment. Yes average of risk blocks is the average of 6 and 10%. Better explanation of what bar plot data represent are now explained in the methods.

1. For the diazepam experiment, did all rats receive saline and diazepam injections in separate sessions? If so, were these sessions counterbalanced? And further, how did the session numbers relate to sessions 1-3 of the first study? All of these details are extremely relevant to interpreting the results and comparing them to the first study, as session # appeared to be an important factor. For example - the decrease in dmPFC fluorescence to reward during the No-Risk block appeared to better match the fluorescent pattern seen in sessions 1 and 2 of the first experiment. In which case, the saline vs. diazepam difference was due to saline rats not showing the expected pattern of fluorescence.

Subjects received saline and diazepam in separate sessions. Furthermore, diazepam was not tested until animals had at least 3 sessions of training (range of sessions 4-8). Clarification has been added to the methods.

The new AUC analysis for Reviewer 1 allows for better assessment of the potential differences between earlier sessions and saline (see figure 7- supplements 2 and 3). We also found the effect with reward and diazepam perplexing and somewhat modest. However, even after comparing only Saline and Session 3 PFC AUC data we found no significant effect of session or session*risk interaction for action or reward (F values < 1.3, p values >.27).

1. The authors seem convinced that fiber photometry is a surrogate for neural activity. Although significant correlation coefficients are found during action and reward, these values hover around 0.6 for the dmPFC and 0.75 for the VTA. Further, no correlations are observed for cue periods. A strength of the calcium imaging approach is that it permits the monitoring of specific neural populations. This would have been very valuable for the VTA, in which dopamine and GABA neurons must show very different patterns of activity. Opting for fiber photometry and then using a pan-neuronal approach fails to leverage the strength of the approach.

The parent paper (Park & Moghaddam, 2017) used unit recording in this task (including reporting data from dopamine and non-dopamine VTA units). We assure the reviewer that we do not claim that fiber photometry is a perfect surrogate for direct recording of neural activity. However, a key question we wanted to answer in this study was whether the response of PFC and VTA to the footshock changes during task acquisition (please see last paragraph of introduction), hence the choice to use fiber photometry. We note in the results and discussion that this approach is not optimal for detecting cue or other rapid responses (see page 15 and 23).

Reviewer 3 (Public Review):

Probably the biggest overall issue is that it is unclear what is being learned specifically. There is no probe test at the end to dissociate the direct impact of shock from its learned impact. And the blocks are not signaled in some other way. And though there seems to be some evidence that the shock effects get more pronounced with a session, it is not clear if the rats are really learning to associate specific shock risks with the particular trials. Indeed with so few sessions and so few actual shocks, this seems really unlikely, especially since without an independent cue, the shock and its frequency is the cue for the block switch. It seems especially unlikely that there is a strong dichotomy in the rats model of the environment between 6% and 10% blocks. This may be quite relevant for understanding foraging under risk. But I think it means some of the language in the paper about contingencies and the like should be avoided.

While the parent paper (Park & Moghaddam, 2017) delved more deeply into this question we agree that what exactly is learned may be difficult to ascertain. To address this (please also see response to reviewer #1’s first comment), we have toned down our use of the “contingency learning” throughout the manuscript and use the word contingency in relation to the underlying reinforcement/punishment schedules.

The second issue I had was that I had some trouble lining up the claims in the results with what appeared to be meaningful differences in the figures. Just looking at it, it seems to me that VTA shows higher activities at higher shocks, particularly at the time of reward but also when comparing safe vs risky anyway for the cue and action periods. DmPFC shows a similar pattern in the reward period. […] But these results are not described at all like this. The focus is on the action period only and on ramping? I don't really see ramping. it says "Anxiogenic contingencies also did not influence the phasic response to reward...". But fig 3 seems to show clearly different reward responses? The characterization of the change is particularly important since to me it looks like the diazepam essentially normalizes these features of the response. This makes sense to me […].

We initially believed that much of the differences in reward (with the exception of Session 2 in the PFC) were from carryover of differences in the peri-action period. However upon quantifying these responses again using AUC change scores to adjust for pre-event differences in the signal, we observed small reward related increases (data are in Figure 7 – supplements 2/3) and have updated results and the discussion.

Although some lessening of reward response may be apparent across the diazepam session in the VTA (Figure 7 – supplement 2/3G), we do not have statistical support for this as no significant differences were observed in permutation comparisons to saline and only session 3 deviated from the first session for the reward period in the AUC analyses.

Author Response

Reviewer 3

This papers builds on a previous publication from the same group that showed compartmentalisation model of beta-cell fuel metabolism in which plasma membrane-localized pyruvate kinase is sufficient to close KATP channels required for insulin secretion. In this current manuscript the authors identified the PK isoforms involved in this process using tissue specific KO mouse models. Using excised patch-clamp experiments, they demonstrated that although redundant in their function both the constitutively active PKm1 and allosterically PKm2 are associated with the PM and locally regulate KATP channel closure. Further, the authors showed that the mitochondrial PEP carboxylase (PCK2) is essential for amino acids to promote an increase in cytosolic ATP/ADP and closure of KATP channels. Therefore, this study very nicely demonstrates that he distinct response of PK isoforms to the mitochondrial and glycolytic sources of PEP impacts beta cell nutrient preference and affects the oscillatory cycle regulating secretion. These findings do provide new mechanistic information about the control of the regulated secretory pathway and will be of interest to broader audience.

Strength<br /> The major strength of the study is the use of tissue/isoform specific KO mouse models. Although limited by constitutive KOs with compensatory increase in other isoforms, the authors have achieved what they were set out to do i.e identify the PK isoform involved in the regulation of PM ATP generation and regulation of KATP channel closure. Their experimental rigorosity including the ability to perform the excised patch clamp experiments and use of PKa to show the specific effect of the allosterically regulated PKM2 are also strength.

Weakness<br /> It is not clear from the manuscript what the "littermate controls" are used in all the experiments. Given the limitations of the cre lox system, it is really important to clearly show what controls have been used and their phenotypes (and the rationale for pooling the different controls if that is what is done here).

Response: We apologize that this was unclear. Littermate Ins1-Cre controls were used for the PKm1-βKO and PKm2-βKO models, whereas floxed controls (i.e. Pck2f/f) were used for the PCK2-βKO. This is described in the first paragraph of the results section as well as the methods.

The data adds to our understanding of the role of PM localised PK on the regulated exocytosis pathway however the claim that these findings question the canonical mitochondrial ATP coupled to KATP channel closure is not fully supported by the data especially given glucose induced insulin secretion is not affected by any of the KO models.

Response: Had we performed experiments that fully block flux through pyruvate kinase, we expect that glucose-stimulated insulin secretion would be impaired if not eliminated. However, as this experiment would prevent both glycolytic and mitochondrial ATP production, it would not address whether a mitochondrially-derived increase in cytosolic ATP/ADP is the primary mechanism of KATP channel closure, as proposed by the canonical model.

Due to the redundant response of PKm1 and PKm2 to glucose, isoform-specific deletion allowed us to test whether a fuel-stimulated rise in cytosolic ATP/ADP is sufficient to close KATP channels in healthy β-cells (i.e. in the absence of glucose intolerance) using a protocol of low glucose and amino acid stimulation. Our findings show that raising cytosolic ATP/ADP with amino acids is insufficient to close KATP channels in the absence of PK activity or PCK2, indicating that KATP channels are regulated primarily by PEP that provides ATP via plasma membrane-associated PK rather than mitochondrially-derived ATP. In these experiments, insulin secretion shows the expected reduction in both the β-cell PCK2 and PKm1 knockout models.

In the discussion, we point out that mitochondrially-derived ATP is likely important for buffering this plasma membrane-compartmentalized KATP closure by pyruvate kinase. However, on balance, our data argue that glycolysis preferentially closes KATP channels, as previously shown in cardiac myocytes (Lamp and Weiss, Science 1987).

Author Response:

Reviewer #1:

Charpentier et al. use facial recognition technology to show that mothers in a group of mandrills lead their offspring to associate with phenotypically similar offspring. Mandrills are a species of primate that live in large, matrilineal troops, with a single, dominant male that fathers the majority of the offspring. Male breeder turnover and extra-pair mating by females can lead to variation in relatedness between group members and the potential for kin-selected benefits from preferentially cooperating with closer relatives within the group. The authors argue that the strategy of influencing the social network of their offspring could be favoured by "second-order kin selection", a mechanism by which inclusive fitness benefits are accrued to female actors through kin-selected benefits to their offspring. This interpretation is supported by a theoretical model.

The paper highlights a previously unappreciated mechanism for favouring association between non-kin in social groups and also contributes a nice insight into the complexity of social interactions in a relatively understudied wild primate species. The conclusions are strengthened by data showing associations between mothers were not influenced by the facial similarity of their offspring -- this suggests that mothers are making decisions based on the appearance of offspring and not their mothers.

Some remaining questions regarding the strength of the authors' interpretation exist: Given the challenges of studying mandrills in the field, the fact that the study reports data from a single group is understandable but potential issues remain with the independence of data points. There may be an additional issue arising from the fact that this troop is semi-captive.

The study group is not semi-captive. Instead, it originated from two release events of a few captive individuals into the wild (in 2002 and 2006). The population is now composed of more than 250 individuals and all of them, except for 7 founder females (<3%), were born in the wild. In addition, the study group is not fed and occasionally wanders into a fenced protected area. Fences of the park do not represent a boundary for mandrills and most of the time (c.a. 80% of days), the study group ranges outside the park. We have clarified this misunderstanding.

Regarding the independence of data points, we would be grateful if this reviewer could clarify her/his thoughts. As a tentative response, we indeed have access to a single (although large) study group, but that’s unfortunately often the case when studying primates or other large mammals. Regarding our study questions, we have clearly demonstrated increased nepotism among paternally related mandrills in two different social groups (Charpentier et al. 2007: semi-captive mandrills; Charpentier et al. 2020: wild mandrills). More generally, we do not see any parsimonious explanations for why the studied mandrills would behave or experienced selective pressures that may have differently shaped their genetic structure and social organization compared to other wild mandrill groups.

The number of genotyped offspring is relatively small (n = 15) and paternity is inferred from the identity of the dominant male. However, the authors also refer to the fact that it's normal for female mandrills to mate with several males during ovulation.

Indeed, both sexes mate promiscuously during the mating season. We have very recently (June 2022) obtained new genetic profiles for a subset of the study infants (it took two years to obtain these data). We have now increased our sample size of infants with a known father, from 15 to 32. With these new data, we were able to distinguish between four categories of infant-infant dyads: those sharing the same father (PHS), those not sharing the same father (not PHS), those conceived during the same alpha male tenure, and those that were not (both infants with unknown dads). The graph below shows the average facial distance among individuals for each of these four categories. It shows that infants conceived during the same alpha male tenure are significantly more similar to each other than infants sired by different fathers or during the tenure of different alpha males, but they are also significantly less similar to each other than infants born to the same father (the four categories are all significantly different from each other, except when comparing infants born to different fathers with those conceived during different alpha male tenures). As suggested by this reviewer, the fact that females mate predominantly with the alpha male, but to some extent also with other males, likely explains the difference between “same father” and “same alpha male tenure”. Importantly, however, considering all infants conceived during the same alpha male tenure as “PHS” is highly conservative. It is thus likely that knowing the paternity of every infant would produce even clearer effects (and indeed, increasing the data set from 15 to 32 strengthened this result). We have now updated this result (first model) based on this new sample.

What evidence is there to support a beneficial effect of nepotism in this species?

In mandrills, females who affiliate more (groom more/associate more) with their groupmates (kin or non-kin) during juvenility also reproduce 1 year earlier than those females that are poorly socially integrated (Charpentier et al. 2012). These results are similar to what is known in many mammalian species (see for review Snyder-Mackler et al. 2020). However, the positive effects of a rich social life are generally triggered by all group members, not only close kin. However, if beneficial social relationships impact the direct fitness of individuals, as reported in mandrills and other species, then kin selection theory predicts that these effects should further translate into indirect fitness benefits.

We have now added this relevant reference (Charpentier et al. 2012) in the revised version of our manuscript and present the results of this early study on mandrills.

What form could nepotism take and does it necessarily have to involve full sibs?

We are unsure why this reviewer is mentioning full-sibs here. For this reviewer information, on the 2556 study dyads (model 1 on the impact of maternal and paternal origins on facial distance), only one dyad was a full-sib pair. Full-sibs are therefore very rare in the study population due to male migration patterns and generally short alpha male tenures.

If a female did not associate with offspring as shown here, would nepotistic interactions simply arise between her offspring and offspring that were less facially similar?

We guess that facial similarity would not be a predictor of spatial association anymore. Indeed, we think that young mandrills do not use self-referent phenotype matching, precluding the self-evaluation of those infants that look like them. However, as stated below, we cannot fully exclude the possibility that other social partners, such as fathers, may also influence infant-infant relationships, although we think that this alternative mechanism is less parsimonious than the one we propose and test.

Reviewer #2:

This paper uses data on patterns of spatial association and facial similarity in mandrills to develop a new hypothesis for the evolution of kin recognition based on facial cues. Previous work on this system has shown that, among females, paternal half-sibs resemble each other visually more than maternal half-sisters do. The authors hypothesise that this paternally inherited facial similarity provides opportunities for kin selection, but it is unclear how offspring themselves could recognise kin using phenotype matching since they are unable to see their own face. One answer to this puzzle is that third parties -- mothers -- may promote social interactions between their own offspring and other offspring that resemble them since these other offspring are likely to share the same father. In support of this hypothesis, the authors find that mothers and offspring show spatial proximity to infants that are facially more similar than average. They also use an analytical evolutionary model to confirm the logic of this hypothesis. The model shows that mothers can gain inclusive fitness benefits by encouraging reciprocal social interaction among their offspring and other paternally-related offspring. They term this idea 'second-order' kin selection and identify a range of other circumstances in which it might play an important role in shaping the evolution of social behaviour.

The main strengths of the paper are the interesting mandrill data and the cutting-edge methods used to analyse facial similarity, which have stimulated the development of a theoretically interesting hypothesis about the evolution of facially based kin recognition. The theoretical model enhances the generality and rigour of the work. The paper will be of wide interest and the concept of second-order kin selection may be applicable to other social circumstances, such as interactions among in-laws in close-knit family groups. Thus, I can see that this paper will be a stimulus for future work.

We are grateful for these positive comments.

The data are, I think, rather overinterpreted in terms of the degree to which they support the hypothesis. The spatial proximity data are interesting, but on their own, they are not definitive support for the hypothesis or model. A more critical approach to the hypothesis, clearly setting out the limitations of the data, and what tests in future could be used to falsify the hypothesis or model, would make for a stronger paper.

We agree with this general comment and have addressed it by 1. Adding a model on grooming relationships between females and infants, 2. Toning down our interpretation throughout the manuscript and 3. Propose future directions of research.

Overall the authors have presented data that support a fascinating new mechanism by which natural selection can influence social interactions among the members of family groups, in potentially surprising ways. I also find it remarkable that 60 years after the development of the kin selection theory new implications of this theory are still being uncovered. The concept of second-order kin selection may prove important in understanding the evolution of social organisation and behaviour in species that live in groups containing a mixture of kin and non-kin, such as many primates and of course humans.

We are grateful to this reviewer for this very positive comment. We fully agree with the fact that 60 years after the kin selection theory has emerged, we are still discovering further implications!

Reviewer #3:

This is a very interesting and impressive manuscript. It is complex in its multiple components, and in some ways that makes it a difficult manuscript to evaluate. There is a lot in it, including empirical analyses of a face dataset and of behavioral association data, combined with a theoretical model.

We are very grateful for this positive comment and are glad that you liked our manuscript.

The three main findings are: 1) Paternal siblings look alike (similar to, and building on, a recent manuscript the authors published elsewhere); 2) Infants that are more facially similar tend to associate; and 3) mothers tend to be found in association with other unrelated infants that look more like their own infants. Such results are interesting, and indeed one potential interpretation, perhaps even the most likely, is that mothers are behaving in such a way that promotes association between their own infants and the paternal kin of their infants.

Nonetheless, the evidence provided is logically only consistent with the authors' hypothesis, rather than being strong direct evidence for it. As such, the current framing and indeed the title, "Primate mothers promote proximity between their offspring and infants who look like them", are both problematic. (In addition, the title should be about mandrills, not "primates", since this manuscript does not provide evidence from any other species.) The evidence provided is consistent with the hypothesis, but also consistent with other potential hypotheses. The evidence given to dismiss other potential hypotheses is not strong, and rests on the fact that many males are not around all year to influence things, and that "males that were present during a given reproductive cycle are not responsible for maintaining proximity with either infants or their mothers (MJEC and BRT, pers. obs.)".

We agree with this comment. Although, after examining several alternative mechanisms, in the light of the natural history of mandrills we are confident that the proposed mechanism is at work in that species, although we cannot firmly exclude some of these alternative mechanisms. To address this comment, we have changed the title of our manuscript that now reads “Mandrill mothers associate with infants who look like their own offspring using phenotype matching”. We have also included an additional model on grooming relationships (see response to R1) and have toned down the interpretation of our results throughout our revised manuscript. Finally, we have further discussed alternative scenario, in particular the one involving fathers (see details above).

My opinion is that these are really interesting analyses and data, which are being somewhat undermined by the insistence that only one hypothesis can explain the observed association patterns. It could easily be presented differently, as a demonstration that paternal siblings look alike and that they associate. The authors could then go on to explore different possible explanations for this using their association data, make the case that maternal behavior is the most plausible (but not the only) explanation, and present their model of how such behavior could bring fitness benefits.

In my view, such a presentation would be both more cautious and more appropriate, without in any way reducing the impact or importance of the data. In the current iteration, I think there are issues because the data do not provide sufficient support for the surety of the title and conclusion, as presented.

We think that the current organization of our manuscript was not that different from the one proposed here and follows a reasoning already proposed in a former manuscript (Charpentier et al. 2020). Indeed, we first start by reminding the reader what we already know from that previous studies: paternal siblings look alike and they associate. We then go on exploring different mechanisms. That being said, and as suggested, we have been more cautious in interpreting our results, that are indeed only correlative.

Author Response

Reviewer 1

In this manuscript, Hansen and coworkers make use of the powerful, single-molecule assay CoSMoS to study the recognition of the 5' splice site by the U1 snRNP. Specifically, they investigate how 5' splice site oligos interacts with purified U1 snRNP to isolate 5' splice sitebinding from other factors, including the CBC, BBP, and any other factors in whole cell extract that may impact binding; previous studies have investigated binding in vivo or in cellular extracts or with limited quantitative capabilities. The authors find evidence for a reversible, two-step, binding reaction in which a short-lived interaction precedes a longlived interaction and in which binding depends on the 5' splice site sequence and the 5' end of U1. The data further suggests a compelling kinetic framework for how U1 surveys nascent transcripts for a bona fide 5'SS; specifically, both authentic and inauthentic 5' splice sites form the short-lived complexes but whereas the inauthentic complex preferentially dissociates, the authentic complex preferentially proceeds to a stable complex. Using oligos with different mutations to limit base-pairing they find that at least six potential base-pairs are required for association but that a stretch of seven base-pairs, with a maximum of one mismatch, is required for the long-lived interaction, with residues near the 5' splice site playing more important roles and with length being a stronger predictor of complex lifetime than thermodynamics, with implications for splice site predictions.

The work focuses on the determinants and mechanism of the first and a pivotal step in splicing, in a manner that completes recent structural advances. The work extends findings presented in a previous publication from the lab (Larson and Hoskins, 2017) studying binding of U1 snRNP to the 5' splice site in extract. In that study, the authors provided early evidence of two-step U1 snRNP binding in the absence of the cap binding complex or the branch point binding protein, with a more stable state following a weaker state; although factors in the extract may have influenced binding, the results are not qualitatively different here. The authors also showed some evidence in the previous study that longer binding depended on crossing a threshold and did not increase further with greater stabilization. Still, this new work is of high quality with conclusions justified by the data and of significant interest to the splicing field and of general interest to those investigating binding of snRNPs to nucleic acid.

Specific Points:

1. To test and define the role of protein in the snRNP, the authors need to investigate the roles of Yhc1 and Luc7 in 5' splice site binding in this assay, particularly with respect to defining the basis of asymmetry and snRNP destasbilization.

See Reviewer Comment #1.

1. The similarity or difference of the two-step recognition mechanism described here to the recognition mechanisms of other nucleic acids by other RNP complexes is unclear. The authors need to put their findings into a larger context, relating their findings to studies of analogous systems described in the literature.

See Reviewer Comments #2 and #4

1. It is important that the authors address whether they can rule out that the exclusively long-lived complexes skip the short-lived conformation.

See Reviewer Comment #5. Overall, a model with reversible connection between the unbound state and the long-lived bound state (U->B*) is less likely to explain our data.

1. Given the co-transcriptional nature of many splicing events, the authors should discuss how recruitment by RNAP II might impact the two-step process. For example, fast dissociation by short duplexes might be countered by retention of U1 locally via RNP II.

See Reviewer Comment #4.

Reviewer 2

In this work, the authors use co-localization single-molecule spectroscopy (CoSMoS) to dissect the sequence-directed nature of pre-mRNA 5' splice site recognition by U1 snRNP using purified, surface-tethered U1 snRNP complexes and truncated substrate RNA oligonucleotides containing the 5'splice site (SS) consensus sequence. The senior author previously has extensively published on related findings using the CoSMoS approach (PMIDs 23569281, 24075986, 27244240), and the current work is a logical extension. Here the authors find that the U1 snRNP reversibly selects a suitable 5' SS in a sequencedependent, two-step mechanism. They derive a kinetic selection scheme that suggests initial base pairing at particular positions, followed by a commitment to a longer-lived complex that enters the chosen 5' SS into the splicing cycle. This type of scheme is widespread among nucleic acid-binding enzymes and sometimes referred to "conformational proofreading". The work could be further strengthened by making more connections to existing kinetic selection schemes for other enzymes.

In the following, major suggestions for improvements are summarized.

1. The model described in the paragraphs starting with line 262 through 280 to interpret the observation of long and short complex lifetimes is not entirely clear. There are at least two potential models that can be considered to fit the observations: a linear and a circular model. A linear model would be one where U1 and substrate RNA are not associated (state 1), then they partially associate (state 2), and finally they isomerize to the completely associated/fully hybridized complex (state 3). The circular model is the same, except that it would additionally allow switching between states 1 and 3 directly (bypassing the partially associated state). To differentiate between these two scenarios, the authors would have to vary the concentration of the RNA probe and see if there is a uniform change in a single kon rate or if two kon rates start to appear. These rate subpopulations would be much easier to detect by fitting with hidden Markov models. It would seem unjustified to decide between these two models without obtaining such additional supporting data.

See Reviewer Comment #5.

1. In the section describing U1/5'SS duplexes destabilization in U1 snRNP (line 281) an underlying assumption is that the binding of two RNAs (in the absence of the spliceosomal proteins) would share the same characteristics or trends as two identical RNAs incorporated into the U1 snRNP. While this may be a rhetorical device to increase the clarity/connection between the concepts of predicted binding free energies and the residence time of hybridized oligonucleotides, it does not address the possible reasons for the discrepancy observed in RNA oligonucleotide versus U1 snRNP binding. The authors should point to a reference and derive a physical model from the available cryo-EM structures to show that the U1 snRNA is, most likely, being constrained by its associated proteins in such a way that it increases the binding affinity to complementary RNA oligonucleotides.

See Reviewer Comment #2

1. While the two-factor authentication metaphor of Figure 7 is charming, it seems off-topic. Instead, the authors should review the literature for examples of short, exploratory binding events involving an RNA:protein complex, followed by more stable, accommodated binding events, see e.g., the work by Sarah Woodson on 30S ribosomal subunit assemble and on Hfq function, work on kinetic proofreading of the ribosome, work on Cas9-based recognition of its target site, and many others. A potential descriptive framework to be used here is that of "conformational proofreading".

See Reviewer Comment #4.

1. There is significant concern that the single molecule sampling rate used to acquire the CoSMoS data is too slow to accurately measure the shortest lifetimes observed, which are only ~10 seconds long. According to the Nyquist sampling criterion, the sampling rate needs to be (at least) twice the frequency of the event being measured, implying that the authors cannot meaningfully observe any lifetime shorter than ~10 seconds given their limited sampling rate. Further considering that at minimum two consecutive data points are needed for observing a 10 second lifetime, artifacts (e.g., camera noise) could make up a disproportionate amount of the signal observed in their data for these short lifetimes. For an accurate measurement, the authors need to repeat the experiments at a higher sampling rate to make sure that there are no faster, transient interactions than those currently reported, and that the values reported are accurate.

See Reviewer Comment #6.

1. The authors have chosen to extrapolate rates via exponential fitting to dwell time distributions. This is a reductive approach that ignores the relationship between consecutive events. It is strongly recommended that the authors consider using a hidden Markov modeling (HMM) approach instead. HMMs have long become the gold standard in single molecule biophysics. Even better, a Bayesian approach could help analyze entire datasets at the same time. In this reviewer's opinion, the ebFRET software package from the Gonzalez lab at Columbia University could, for example, work well here.

See Reviewer Comment #7

1. The manuscript would be majorly strengthened if the authors were testing their hypothesis that Yhc and Luc7 contribute to U1 snRNA:5'SS stabilization, by generating (e.g., temperature sensitive) mutant strains that allow them to interfere with this function of the two proteins, either in purified U1snRNPs or whole cell extracts. Alternatively, the authors could choose to test the role of trans-activing factors such as BBP/Mud 2. Without such data, and given the extensive work the authors have previously performed to already demonstrate that U1 snRNP binds to a 5'SS reversibly, with fast and slow dissociation events, one can argue that the current work falls somewhat short in providing major new biological insights. More generally, the plethora of recent cryo-EM structures gives a wonderful opportunity to ask incisive mechanistic questions, which the authors do not fully leverage.

See Reviewer Comment #1.

Reviewer 3

This study of U1 snRNP interaction with the 5'ss is an interesting and exciting piece of work. In particular, the data support two important conclusions of general importance to the field: 1) the association of the U1 snRNP with the 5'ss is largely determined by the snRNP itself and does not require other splicing factors and 2) the ability to form "productive" (i.e. longlived) interactions between the U1 snRNP and the 5'ss cannot be accurately predicted by base-pairing potential alone. This second point is particularly important as many algorithms for predicting splicing efficiency are based on base-pairing strength between the U1 snRNA and the 5'ss sequence. The data immediately suggest two additional questions.

1. The authors repeatedly speculate that the benefit of basepairing toward the 3' end is due to the activity of Yhc1. If this model is true, these 3' end basepairs should not influence binding for a U1 snRNP with a mutant Yhc1. Since the authors have used mutant Yhc1 in other studies it seems possible to test this prediction.

See Reviewer Comment #1.

1. Since splice sites are often "found" in the context of alternative or pseudo/near-cognate splice sites, it would be interesting to know how the "rules" identified in the experiments presented in this study influence splice site competition and whether both the short- and longlived states are subject to competition or, rather, only the short-lived complexes. Is it possible to repeat the CoSMoS experiment with two oligomer sequences of different colors?

See Reviewer Comment #3.

1. Finally, the authors should say more about the particular requirement for basepairing at position 6, especially in the context of the experiments in Figure 5. This is particularly striking as this position is not well conserved in natural 5'ss, at least compared to position 5.

See Reviewer Comment #8

Author Response

Reviewer 1

Bailon-Zambrano and colleagues were trying to answer the general question: what contributes to phenotypic variation when a gene of strong effect is mutated?

The work has several major strengths for answering this interesting question. First, they decided to study mef2ca in zebrafish for which they had previously shown that mutants displayed highly variable facial phenotypes. To learn how phenotypic variation depends on phenotypic severity, they realized they had studied more alleles, and so induced two more alleles to have three different types of molecular lesions (start codon mutation, premature stop codon, and full coding gene deletion). Investigating these alleles showed that increasingly severe alleles had more variation among individuals in the population but not necessarily more variation between the left and right sides of the face within individuals.

Over several years, these investigators had spent considerable effort to select lines of fish that segregate the start-codon mutation and have either severe or weak effects on facial phenotypes. wondered: what factors were selected out of the original genetic background that would increase or decrease phenotypic severity? They hypothesized that one or more of the five mef2 paralogs in zebrafish might help to ameliorate the phenotype in the low line or reciprocally intensify the phenotype in the high line. They studied expression of the mef2 paralogs in neural crest cells by single-cell transcriptomics. They found that paralogs were downregulated in the high-penetrance line with respect to an unselected line, a result expected if expression of the paralogs contributed to buffering phenotypic severity. This experiment has two weaknesses, first that the method only examined neural crest cells but we know that signals from the ectodermal and endodermal epithelia contribute to craniofacial morphologies by diffusible signals. If genes regulating craniofacial morphologies that act in epithelia had genetic variation that contributes to severity, those genes would not be investigated in these crest-only experiments. A minor problem (which is associated with the expense of the experiment) is that the scRNA-seq experiments compared only the high and unselected lines, not the low line. To address both problems, the investigators performed qPCR on RNAs extracted from whole heads of genetically mef2ca-wild types from the high and low line. In these qPCR experiments, however, they did not investigate the unselected line. Leaving out the low line in one approach and leaving out the unselected line in the other approach somewhat weakens the strength with which one can draw conclusions (e.g., the qPCR conclusion assumes that the unselected line would be intermediate between the two selected lines) but is unlikely to change the basic conclusions the authors drew. In addition, using whole heads in the qPCR experiments, while it has the advantage that it includes epithelia, does not distinguish between genes expressed only in the crest and genes expressed in other cell types, and these experiments did not test for any genes known to affect craniofacial development that are epithelium-specific.

In response to this comment, and those below, we removed the scRNA-seq comparing neural crest cells from unselected and high-penetrance strains. We replaced those data with new important results which considerably advance our model. We found significant paralog expression variation among unselected zebrafish families (Fig. 4D). These results strongly suggest that our breeding selected upon standing paralog variation the unselected parental strains. See more below.

Finally, in key experiments that are a major strength of the work and require significant effort, the researchers systematically made mutations in four of the five zebrafish mef2 paralogs (mef2aa, mef2b, mef2cb, and mef2d, all except mef2ab, which didn't become mutated despite significant effort) in the genetic background of the lowpenetrance strain and studied them in single homozygotes, in double mutants, and in various heterozygous combinations. These important experiments showed that some paralogs provided significant buffering in the low-penetrance strain, the strain that up-regulated expression of these paralogs. It would be helpful in the discussion to mention that mef2ab couldn't be mutated and a phrase added about what that means for the general conclusions - in the opinion of this reviewer, the impact of this is not great but it should be acknowledged.

We acknowledge that mef2ab couldn’t be mutated and consider what that means for the general conclusions in the text.

A strength of the experiments is that the workers quantified effects of various genotypes by focusing on the length of the symplectic, a convenient element for quantification both within single individuals and among fish in a population. It would be helpful to have a statement on the evidence that this measure is a good representative for other aspects of the phenotype.

We provide new data indicating that the symplectic cartilage length is significantly correlated with another mef2ca-associated phenotype (Fig. 1-figure supplement 2). See more below.

Finally, the paper presents a model for understanding the results presented that does a good job of summarizing the data and, importantly, suggests ways to move the analysis deeper. Missing from the description of the model is a discussion about whether the genetic variation that was selected and ultimately upregulated mef2 paralogs is in regulatory elements of the mef2 paralogs themselves or whether it might be in trans-acting transcriptional regulators that simultaneously regulate all mef2 paralogs due to the authors' hypothesized 'cryptic vestigial' functions.

We considerably revised the discussion, thoroughly considering both these possibilities.

This work is likely to have a significant impact on the fields of developmental biology, the interpretation of human mutational variation (in for example the concept of phenotypic expansion), and the way people think about the evolution of new morphologies over time. A brief comparison of the authors' results and interpretations to those of C.H. Waddington's concept of genetic assimilation would provide improved historical context and broaden the potential impact of the work.

We now include a discussion of our study in the context of Waddington’s genetic assimilation.

Reviewer 2

Bailon-Zambrano et al study the possible mechanisms that contribute to the oft-observed phenomenon that an individual mutation may be associated with variable expression of a phenotype. They focus on loss-of-function of the mef2ca gene of zebrafish, which is needed for the normal development of several craniofacial structures. They demonstrate that recessive putative loss-of-function mutant alleles of the mef2ca gene of zebrafish are associated with a range of expressivity. By focusing on one aspect of the mutant phenotype, the length of the symplectic cartilages that support the jaw, they find a correlation between the average strength of the phenotype of an allele (measured as reduction in length) and the extent of variability between mutant individuals that carry the allele. I am concerned about this conclusion and generalizations that may be drawn from focus on a single quantifiable character, the symplectic cartilage. Perhaps there is always a fixed variation in the length of this cartilage. As stronger alleles produce shorter cartilage pieces, variations in size may appear to be of greater significance when affecting shorter average length.

We now show that the symplectic cartilage length is a good proxy for other craniofacial phenotypes (Fig. 1figure supplement 2). Further, we clarify in the text that we use the coefficient of variation (standard deviation/mean) which is the accepted best practice for determining and comparing variation. We also use the F-test statistic which is the standard statistical method to test for equality of two variances. This test tells us if the standard deviations from two datasets are significantly different.

The authors hypothesize that one factor that contributes to the varied phenotypic expression of an allele (expressivity) is the co-expression of paralogs that may provide wildtype function and thus partially or wholly rescue the mutant phenotype. They test this hypothesis by "fixing" conditions where a single mutation may be expressed with low or high penetrance. By selective breeding based on phenotype, they create two sets of strains that carry an identical mef2ca mutation: one strain has high penetrance of the mutant phenotype and the other low penetrance. They then investigate the factors that are likely responsible for the high vs low penetrance. Historically we would call these factors "genetic modifiers". There is extensive literature on the nature of genetic modifiers and there are many current screens in both mice and Drosophila to identify genetic modifiers and uncover their nature, but there is little reference to these studies in the current manuscript. Further, there is previously published work that hypothesizes that one important function of paralogs in multicellular organisms is to provide a buffer to stabilize levels of gene expression needed for developmental decisions.

Following this reviewer’s suggestion, we now include many new references (increased from ~50 to >80) incorporating much of the important work leading up to our study. These include referencing both genetic modifier mutagenesis screens, paralogous buffering in other systems, and “natural” modifier studies that set the stage for our work.

The authors find that paralogs of the mef2ca gene are expressed in cells that normally express mef2ca, and that these paralogs are expressed at higher levels in the mutant strain with low penetrance than in the mutant strain with high penetrance. They say that selection for high penetrance of the mef2ca mutant phenotype "leads to down-regulation" of paralog expression. As the authors only show that paralog expression is at lower levels in high penetrance vs low penetrance strains, it is not clear what they mean by "down-regulation". Perhaps their breeding scheme has only "captured" what is natural variation and there is no active mechanism of "down-regulation". The authors need to clarify what they mean.

Thank you for this suggestion. We clarified that we do not mean active down or up regulation but rather selection on preexisting genetic variation. This conclusion is supported by new data (Fig. 4D).

The authors also find that individuals from the high penetrance strains that don't carry the mef2ca mutation (they are wildtype for this gene) sometimes exhibit mef2ca mutant characters. They suggest the reduced paralog expression is responsible for the occasional emergence of the mef2ca mutant characters. In contrast with this suggestion, the authors later claim the paralogs "have no function" in craniofacial development. The authors need to clarify their thoughts about what is paralog function in craniofacial development and why reduced paralog function might contribute to the expression of mef2ca mutant characters. This topic is worthy of discussion.

We considerably revised our discussion of this topic including our interpretation that the decreased expression of mef2ca in high penetrance strain led to the phenotypes we observe in mef2ca wild types from this strain. We also are more careful with our language, stating that the paralog mutants are indistinguishable from wild types, rather than stating that paralogs do not function in craniofacial development. In fact, they do function in craniofacial development, as buffers. Thank you for this suggestion that strengthened our manuscript.

The authors claim is there is both up-regulation of paralogs in low penetrance strains and down-regulation of paralogs in high penetrance strains. As they only compare steady state levels of expression in each strain, they can only reasonably conclude that there are differences - they seem to imply a mechanism and they need to be clear about what they are thinking.

Excellent point. In the revised manuscript, we are clear that there is not active up or down regulation but rather selection upon preexisting variation.

They hypothesize that paralog expression in the low penetrance strain masks the effects of loss of mef2ca. They test this by creating CRISPR-engineered mutations of two paralogs and examining the effects of the paralog mutations in wildtype fish or in fish carrying the mef2ca mutation. They find the putative loss-offunction mutations in the paralogs have no effect in wildtype backgrounds and conclude these paralog genes have no function in craniofacial development. However, the paralog mutations enhance the mutant phenotype in fish that carry the mef2ca mutation. This provides strong evidence consistent with the model that the elevated expression of the paralogs functions to reduce the severity of the phenotype associated with the mef2ca mutation.

Reviewer 3

In this elegant genetic study, Bailon-Zambrano et al. draw on classical genetic concepts to address the clinically pertinent question of how genetic variants in the same gene can yield wildly different phenotypes in different individuals. They focus on the Mef2c gene, which is required for craniofacial and cardiac development in humans and model organisms yet shows highly variable phenotypes across and within individuals. Previous work by this lab had established that zebrafish mef2ca craniofacial phenotypes are highly variable and, importantly, that this variability is heritable and can be selectively bred for low vs. high penetrance. The authors hypothesize that vestigial expression of paralogous genes variably compensates for loss of mef2ca, such that individuals with higher levels of paralogous genes will show lessened severity and vice versa. To test their hypothesis, they methodically quantify the penetrance, expressivity, and variability of all known mef2caassociated craniofacial phenotypes in fish carrying 1) different mef2ca mutations, 2) the same mutation but after selecting for high vs. low penetrance for many generations, and 3) mef2ca mutations combined with mutations in paralogous genes. They find that not only does allele severity directly correlate with variation, but also that different paralogs buffer the severity and variability of different craniofacial phenotypes. Another particularly interesting finding is that some of the craniofacial phenotypes are apparent even in mef2ca wildtypes from the high penetrance strain, which they explain by the very low expression of paralogs on this background. A weakness of the study is that the authors do not directly show whether paralog expression is increased in the low-penetrance strain relative to the initial, unselected genetic background. It is therefore not clear whether the selection for low penetrance worked in this manner, as the authors imply. Overall, the authors have achieved an important step forward in understanding the genetic basis for the high variability of human faces among both healthy individuals and those with craniofacial anomalies.

We can’t go back (over ten generations) to survey the original parental strain. However, we can use the unselected AB strain as a proxy for the initial unselected genetic background. In an important addition to the manuscript, we found significant paralog expression variation between unselected AB families (Fig. 4D). These results strongly suggesting there is cryptic, standing paralog expression variation that we selected upon. We would like to thank the reviewer for this excellent critique which motivated these important new experiments considerably advancing our model.

Author Response

Reviewer 1

Ting Tang et al. present the results of a species x genotype diversity experiment within BEF China. The authors assess the relative impacts of species and genotype diversity on community-level primary productivity of the trees and the potential mediation of this effect via interactions of plants with soil fungi and herbivores. The results show that both species and genotype diversity influence productivity via changes in herbivory, soil fungal diversity, and other unknown mechanisms. Most of the species diversity effects could be directly related to functional diversity, while genotype diversity effects were not well represented by the way functional diversity was measured in this study.

Thanks for the positive comments on the paper.

The study is based on an impressive experiment that will certainly allow achieving major insights into the role of genotype and species diversity on ecosystem functioning. However, there are some significant shortcomings in the methods that limit this study. In particular, the incomplete assessment of functional traits, herbivory, and fungal diversity across the subplots used for this study reduces statistical power. Specific measurements of traits, herbivory and fungal diversity in each plot would substantially simplify the design and the analyses and likely also reduce the unexplained variance observed in the study. However, this is nothing that can be changed now and has the likely explanation of feasibility constraints.

Thank you for the positive comments on the paper and the understanding of the feasibility constraints. In our study, functional traits of all the seed families of the four species across all the species × genetic diversity combinations were sampled, but to reduce circularity, we used the seed-family means across all tree diversity combinations to calculate functional diversity for every subplot instead of only using the functional trait measures obtained in that particular subplot. We have taken up the suggestion to also calculate functional diversity based on trait measurements of individual trees, but also here used data across all plots to reduce circularity. Additionally, we now acknowledge the incomplete assessment of herbivory in the Methods and state that fungal diversity in plant species mixtures was sampled on plot level because of feasibility constraints.

Lines 334–337: “To reduce circularity, we used the seed-family means across all species × genetic diversity combinations to calculate FDis values per subplot that did not only depend on the functional trait measures obtained in that particular subplot. Using traits measured in a particular subplot to calculate FDis for that subplot bears the risk that the measured traits reflect a response to the local environment, yet we want to use FDis as a predictor variable for the performance of that subplot.”

Lines 380–382: “The mean value of herbivore damage per species × genetic diversity level was used to fill in missing values in a few subplots with tree individuals lacking herbivory data (Table S3).”

Lines 385–388: “Soil fungal diversity was used as a proxy of unspecified trophic interactions. To be consistent with the species and genetic diversity treatment design, soil samples were taken on subplot level for the 1.1 and 1.4 diversity treatments, but, due to feasibility constraints, on plot level for the 4.1 and 4.4 diversity treatments in 2017.”

The writing of the manuscript is generally good. However, given the somewhat diffuse results obtained for genetic diversity effects, they receive a lot of attention in the discussion, while species diversity effects are little mentioned. This could be better balanced and also referred back to the hypotheses. For example, I miss the discussion of the very clear hypothesis that genotype diversity effects are positive in species monocultures but neutral in species mixtures. How do your results fit with this hypothesis? My general impression is that the study is very well framed, but lacks to stick to this frame in the discussion. I am aware that this might be a challenge with the results obtained, but worth trying.

Thank you for the positive comments on the writing and pointing out the unclear part of the genetic diversity effects. To better connect the discussion to our hypothesis that genotype diversity effects are “more important in species monocultures than in species mixtures” (lines 114–115), we have rewritten the corresponding Discussion section.

Lines 248–164: “In contrast of our second hypothesis, we found that the effects of genetic diversity via functional diversity and multi-trophic feedbacks were negative in species monocultures but positive in the species mixture (Fig. 5 and Fig. S3). We found genetic diversity had positive effects on tree functional diversity and soil fungal diversity, which supports the trade-offs between genetic and species diversity discussed in the previous section. However, the hypothesized positive effects of tree functional diversity on productivity turned negative in species monoculture. This result indicates that functional diversity may not have positive effects on the ecosystem functioning under low environmental heterogeneity, i.e. species monocultures in our study (Hillebrand and Matthiessen 2009). Therefore, our findings show that the different effects of genetic diversity on tree productivity between species monocultures and mixtures, not only depend on the different effects of genetic diversity on functional diversity and trophic interaction but also on the varied tree productivity consequences from functional diversity and trophic interaction on tree productivity between species monocultures and mixtures. Moreover, other aspects of tree genetic diversity seem to play an important role not only for productivity in tree species mixtures (see previous section) but also for productivity in tree species monocultures. These may include unmeasured functional traits such as root traits (Bardgett et al., 2014) or unknown mechanisms underpinning effects of tree genetic diversity.”

Given the complex results obtained, I also feel that the title and main message received in the abstract do not fully reflect the results. Genetic diversity effects on productivity, but also on herbivory and fungal diversity, are not general (e.g. Fig. 2) nor are all genetic diversity effects on productivity mediated by functional diversity and trophic feedback. I think the title and main message of the study should be articulated more precisely.

In this study we did not find direct effects of genetic diversity on tree productivity in the binary analyses (Fig. 2), but we did find indirect effects of genetic diversity on tree productivity via functional diversity and trophic feedbacks in the path analysis (Fig. 4). Now we have pointed this out in the Discussion.

Lines 201–204: “Although only species diversity but not genetic diversity was found to affect tree productivity in binary analyses, both kinds of diversity positively affected tree community productivity and trophic interactions via functional diversity according to our structural equation models (SEMs) depicted in the corresponding path-analysis diagrams (see Fig. 4).”

We agree that not all genetic diversity effects on productivity were mediated by functional diversity and trophic feedbacks. This may have been because we did not include all relevant functional traits and trophic interactions in this study. Nevertheless, our findings support the hypothesis that genetic diversity can affect productivity via functional diversity and trophic feedbacks and suggest more possibilities for further research. We have explained this in the Discussion.

Lines 230–238: “Even after accounting for tree functional diversity and trophic feedbacks, we still detected a direct negative effect of tree genetic diversity on tree productivity, while the direct effect of tree species diversity was fully explained by functional diversity and trophic feedbacks. This suggests that aspects of genetic diversity that do not contribute to functional diversity or trophic interactions as measured in this study may reduce ecosystem functioning, e.g. due to trade-offs between genetic diversity and species diversity. For example, it has been shown that in species-diverse grassland ecosystems, niche-complementarity between species can increase at the expense of reduced variation within species (van Moorsel et al., 2018; van Moorsel et al., 2019; Zuppinger-Dingley et al., 2014; Zvereva et al., 2012).”

Lines 260–264: “Moreover, other aspects of tree genetic diversity seem to play an important role not only for productivity in tree species mixtures (see previous section) but also for productivity in tree species monocultures. These may include unmeasured functional traits such as root traits (Bardgett et al., 2014) or unknown mechanisms underpinning effects of tree genetic diversity.”

Reviewer 2

This study aims to disentangle the contributions of genetic and species diversity to tree community fitness. It confirms the role of genetic diversity in functional and ecological traits but shows how these effects change when plant species diversity is increased, which can potentially add to our understanding of the interplay between plant diversity at various levels and community and ecosystem functions. It would be desirable to make emphasis whether differences between the effects of genetic and species diversity are comparable since they can act at complementary but different levels. It is hard to establish whether the effects of species diversity override the effects of genetic diversity by shared mechanisms; or whether a high species diversity reduces plant intraspecific interactions and the consequent effects of genetic diversity by density-dependent effects. However, this point has to be emphasized in the discussion.

Thank you for your positive comments on this paper. In the binary analyses in this paper, we used general linear mixed-model analysis to detect the effects of genetic diversity within species. Now we have clarified this in the Methods and the Results section. However, in Fig. 2 we also indicate the significance of the main effect of genetic diversity. We do not focus on this because of the interaction between species and genetic diversity. In statistical terms, fitting genetic diversity effects separately for species monocultures and mixture (2 degrees of freedom) is equivalent (i.e. has the same sum of squares) as fitting the main effect of genetic diversity (1 degree of freedom) and the interactions species x genetic diversity (1 degree of freedom).

Lines 415–424: “To determine how species and genetic diversity and their interaction affected tree functional diversity and trophic interactions, linear mixed-effects models (LMMs) were fitted with two types of contrast coding. In the first, we used the ordinary 2-way analysis of variance with interaction and in the second we replaced the genetic diversity main effect and the interaction with separate genetic diversity effects for species monocultures and the species mixture (Table S6). Note that as our design was orthogonal, fitting sequence did not matter in either of the codings. However, we focused our major analysis on the second type of coding to make it consistent with our hypotheses. Main effects of genetic diversity are presented in inset panels in Fig. 2. Our second contrast coding ensured that we tested the effects of genetic diversity separately in species monocultures and species mixture, but within the same analysis.”

Lines 120–121: “Using linear mixed-model analyses, we tested the effects of species diversity and genetic diversity within species on trophic interactions and community productivity.”

Meanwhile, to emphasize that species diversity and genetic diversity could affect each other, we discussed that the trade-offs between species and genetic diversity could contribute to the effects of tree diversity on tree community productivity. We also discussed that the different effects of genetic diversity between species monocultures and mixtures may occur because different biotic environments resulted from different species diversity.

Lines 232–238: “This suggests that aspects of genetic diversity that do not contribute to functional diversity or trophic interactions as measured in this study may reduce ecosystem functioning, e.g. due to trade-offs between genetic diversity and species diversity. For example, it has been shown that in species-diverse grassland ecosystems niche-complementarity between species can increase at the expense of reduced variation within species (van Moorsel et al., 2018; van Moorsel et al., 2019; Zuppinger-Dingley et al., 2014; Zvereva et al., 2012).”

Lines 250–260: “We found genetic diversity had positive effects on tree functional diversity and soil fungal diversity, which supports the trade-offs between genetic and species diversity discussed in the previous section. However, the hypothesized positive effects of tree functional diversity on productivity turned negative in species monoculture. This result indicates that functional diversity may not have positive effects on the ecosystem functioning under low environmental heterogeneity, i.e. species monocultures in our study (Hillebrand and Matthiessen 2009). Therefore, our findings show that the different effects of genetic diversity on tree productivity between species monocultures and mixtures, not only depend on the different effects of genetic diversity on functional diversity and trophic interaction but also on the varied tree productivity consequences from functional diversity and trophic interaction on tree productivity between species monocultures and mixtures.”

The experimental design has to be explained in more detail, in particular how plants were planted in the species monocultures. It is not stated whether the same or different species were used in the plots or in subplots. The design lacks proper replication for the treatment with high genetic diversity in species monocultures (n=2) which could lead to a biased result, especially if those plots were located in the same area.

Thank you for the valuable comments on the experiment design. In total, we used four species and eight seed families per species for the whole experiment, and now we have added a diagram of the experimental design to the supplementary material (Fig. S5) to show the species and seed-family information for every subplot. Furthermore, we have added a table to the supplementary material to indicate the occurrence time of each species and each seed family across all the tree diversity-treatment combinations (Table S2). The high genetic diversity in species monoculture (1.4 treatment) was replicated 2 times per species and thus had 8 replications (Fig. S5). However, because we did not have enough seedlings, we could only establish these treatments at subplot level and thus put the different species for the 1.4 treatment into only two plots. Now we have added more explanation of the plot design in the Methods part. The plot distribution was completely randomized across the experimental site and plots of the same treatments were mostly located at least 50 m from each other (see Fig. 1 from Bongers et al., 2020, pasted here further below). The reason that there are more plots for the 1.1 treatment is that typically in biodiversity experiments more plots are needed at the lowest diversity treatment because of the desire to have all seed families occurring in any mixture also present as monoculture. Regarding the point that the four diversity treatments varied between rather than within plots, we ensured that diversity effects were tested at the plot level by including plot as random-effects term in the mixed models.

Lines 305–323: “For each of the four species, we collected seeds from eight mother trees to allow for two replications of four-family mixtures per species. Furthermore, to avoid the effects of unequal representation of particular seed families and correlations between seed family presence and diversity treatments, we made sure that every seed family occurred the same number of times at each diversity level (see Table S2, small deviations from the rule were required where not enough seeds from a seed family could be obtained). Due to budget limitations and the number of replicates required per single seed family, the 1.1 and 1.4 diversity treatments were applied at subplot level (0.25 mu) and replicated 32 and 8 times, respectively. The 4.1 and 4.4 diversity treatments were applied at plot level (1 mu) and were replicated 8 and 6 times, respectively (Fig. S5; see also Fig. 1 in Bongers et al., 2020). To allow for simpler analysis, we obtained most community measures at subplot level also for the 4.1 and 4.4 diversity treatments and thereafter used the subplots for all tests of diversity effects on these community measures, including plots as error (i.e. random-effects) term for testing the diversity effects in the corresponding mixed models. In total, because one 1-mu plot could not be established due to logistic constraints, the number of subplots used was 92 (32 subplots of 1.1, 8 subplots of 1.4, 28 subplots of 4.1 and 24 subplots of 4.4 diversity treatment). Note that in biodiversity experiments lower richness levels represent more different communities and thus require more plots. For the highest richness level, where there is typically only one species composition, this same community is typically replicated multiple times, as we did here for the 4.4. diversity treatment.”

Author Response

Reviewer 1

Employing in vitro and Drosophila model, the authors interrogate which domain of Hsp27 binds to which region on Tau, and how these interactions facilitate the proteinaceous aggregation. They utilized various biochemical, biophysical, cellular, and genetic tools to dissect the association, and identified the structural basis for the specific recognition of Hsp27 to pathogenic p-Tau. Conceivably, Hsp27 may play some role in preventing Tau abnormal aggregation and p-Tau pathology in AD. Overall, the data support the main claim, especially, the biophysical data are very impressive. Nevertheless, the manuscript could be strengthened by complementary cellular or biochemical methods for validation. For example, the authors can use a stably transfected Tau cell line to interrogate Hsp27's role in its cellular aggregation or proteinaceous inclusions by immunoblotting. Immunofluorescent and immunohistochemical staining and IB with different antibodies may be conducted to validate the observations.

REPLY: We sincerely thank the reviewer for the positive assessment of our work, and for providing very insightful suggestions. We appreciate the reviewer for considering our biophysical data to be impressive. We totally agree with the reviewer that the work could be strengthened by complementary cellular methods for validation. In our work, we used the Drosophila tauopathy model, where expression of human TauR406W in the Drosophila nervous system leads to age-dependent neurodegeneration recapitulating some of the salient features of tauopathy in FTDP-171,2, to interrogate the role of Hsp27 in aggregation and proteinaceous inclusions of pTau.

In our Drosophila Tau model study, three different antibodies including a total Tau antibody 5A63, a pTauSer262 specific antibody4, and a hyper-phosphorylated Tau antibody AT8 that recognizes hyper-phosphorylation of Tau at Ser202 and Thr205 sites5 were used in western blot analysis to explore the role of Hsp27. As shown in Figure R1-1A and 1B, overexpression of Hsp27 significantly reduced the level of both pTauSer262 and hyper-phosphorylated Tau at both 2 and 10 days after eclosion (DAE). In addition, we further examined the morphology of the fly brain as well as the accumulation of hyper-phosphorylated Tau by immunofluorescence staining. Consistent with previous findings, brains with neuronal expression of TauR406W exhibited an accumulation of filamentous pTau and a reduction of brain neuropil size indicative of neurodegeneration (Figure R11C-F). Importantly, overexpression of Hsp27 restored the size of brain neuropil and suppressed the accumulation of filamentous pTau (Figure R1-1C-F), suggesting that Hsp27 protects against mutant TauR406W - induced neurodegeneration. Taken together, our Drosophila results show that Hsp27 protects against synaptic dysfunction in a Drosophila tauopathy model by reducing pTau aggregation, which well supports our biophysical data.

Figure R1-1 Hsp27 reduces pTau level and protects against pTau-induced synaptopathy in Drosophila. (This figure represents Fig. 2A-F in the revised manuscript) (A) Brain lysates of 2 and 10 days after eclosion (DAE) wild-type (WT) flies (lanes 1 and 6), flies expressing human Tau with GFP (lanes 4 and 9), or human Tau with Hsp27 (lanes 5 and 10) in the nervous system were probed with antibodies for disease-associated phospho-tau epitopes S262, Ser202/Thr205 (AT8), and total Tau (5A6). Actin was probed as a loading control. Brain lysates of flies carrying only UAS elements were loaded for control (lanes 2, 3, 7, and 8). (B) Quantification of protein fold changes in (A). The levels of Tau species were normalized to actin. Fold changes were normalized to the Tau+GFP group at 2 DAE. n = 3. (C) Brains of WT flies or flies expressing Tau+GFP or Tau+Hsp27 in the nervous system at 2 DAE were probed for AT8 (heatmap) and Hsp27 (green), and stained with DAPI (blue). Scale bar, 30 μm. (D-F) Quantification of the Hsp27 intensity (D, data normalized to WT), brain optic lobe size (E), and AT8 intensity (F, data normalized to the Tau+GFP group). n = 4.

Reviewer 2

Abnormal accumulation and aggregation of amyloid-β protein are one of the main pathological hallmarks of Alzheimer's disease. It is well known that molecular chaperones play central roles in regulating tau function and amyloid assembly in disease. In this manuscript, Zhang, Zhu, Lu, Liu, et al., have investigated that Hsp27, a member of the small heat shock protein, specifically binds to phosphorylated Tau, which prevents pTau fibrillation in vitro and in a Drosophila tauopathy model. Using NMR spectroscopy and cross-linking mass spectrometry, the authors found that the N-terminal domain of Hsp27 directly binds to phosphorylation sites of pTau. Overall, the study is important and provides the demonstration of interactions between Hsp27 and pTau.

REPLY: We sincerely thank the reviewer for the positive remarks of this work, and appreciate that the reviewer summarizes the major conclusions of our manuscript, and evaluates our work is important in the area of fundamental biology of the interaction between chaperones and clients, and its implications in AD pathology.

Author Response

Reviewer 2

The manuscript by Huisjes et al presented an open-source platform for the storage and processing of imaging data, particularly for single-molecule imaging experiments. Compared to sequencing data, which have a more standardized format for data storage, imaging data have more diverse formats due to the fact that different research labs tend to use different instruments and software (either commercial or home-built) for data collection and analysis. Manual input is almost always necessary at certain steps of data analysis. All these create difficulties in data storage and reproducibility. The authors provide a practical solution to this problem by the molecular archive suite, "Mars". This platform is integrated into imageJ/Fiji, and can be used for storing detailed description of experimental settings, performing standard imaging processing steps, and recording manual input information during data analysis. I judge this platform, if fully functional and generalizable, will be very useful to many labs who are using single-molecule imaging methods in the research.

Strength:

1. The work presented a fairly user friendly interface (using Fiji directly), and fairly detailed protocol and other documentations in a very nicely designed website. I was able to download and use it based on the tutorial.

2. It is integrated very well with Fiji, and some analysis modules are directly from existing Fiji analysis/plugins.

Weakness:

I invited one of my students to co-test the suite. We tried on both Mac and Windows systems, using the example FRET data set described in the manuscript and one of our own single-molecule images. We encountered some technical issues.

We are very happy with the overall positive assessment of the reviewer that Mars could offer a common format that helps to enforce reproducible analysis workflows that can easily be shared with others.

We are grateful for the additional feedback and testing done by the reviewer and her student. Ensuring that Mars works as expected on all computers and configurations is difficult given that we don’t have them at hand for testing ourselves. During the revision period, we have done more testing on more computer systems and we hope we have addressed the issues. We believe it will be impossible for us to guarantee that Mars works without problems on the first try for everyone. Therefore, Mars is a community partner on the Scientific Community Image Forum where users can report their problems in posts with the mars tag and we can help troubleshoot them (https://forum.image.sc/tag/mars). We believe this approach will offer the best support going forward. Nevertheless, we continue to make improvements and test to make sure all bugs we discover are addressed.

In the revision, we completely reworked the smFRET example workflow and added two additional workflows to address all the comments from the reviewers and reviewing editor. In addition to expanding the explanations, and troubleshooting information on the Mars documentation website, we also created a YouTube channel with tutorial and example videos (https://www.youtube.com/channel/UCkkYodMAeotj0aYxjw87pBQ). We go through the new dynamic smFRET workflow from start to finish in one of the videos provided (https://www.youtube.com/watch?v=JsyznI8APlQ). We hope this will make it clear what inputs and outputs are expected and how the workflow should proceed. This was done on a mac but we have also tested this workflow on windows without encountering problems.

Author Response

Reviewer 1

This article creates a formal definition of the 'informativeness' of a randomized clinical trial. This definition rests upon four characteristics: feasibility, reporting, importance, and risk of bias. The authors have conducted a retrospective review of trials from three disease areas and reported the application of their definition to these trials. Their primary finding is that about one quarter of the trials deemed to be eligible for assessment satisfied all four criteria, or, equivalently, about three quarters failed one or more of their criteria. Notably, industry‐sponsored studies were much more likely to be informative than nonindustry‐sponsored studies. It would be interesting to see a version of Figure 3 that categorizes by industry/non‐industry to see the differences in fall‐off between the four criterion.

Thank you for this suggestion. We have added an additional figure to the supplement, eFigure 1 ‐ The Cumulative Proportion of Trials Meeting Four Conditions of Informativeness by Sponsor.

We have also indicated the following in the legend of Table 1: (as related to study sponsor)

Lines 332 – 334 “Included within the designation “Other” are 7 trials that received funding from the U.S. National Institutes of Health (NIH) or other U.S. Federal agencies, and 60 trials that are nonindustry and non‐NIH/U.S. Federal agency funded.”

As the authors point out, the key limitations to this work are its inherent retrospective nature and subjectiveness of application, making any sort of prospective application of this idea all but impossible. Rather, this approach is useful as a 'thermometer' for the overall health of the type of trials satisfying the eligibility criteria of this metric. A secondary and inherent limitation of this measure is the sequential nature of the four criteria: only among the trials that have been determined to be feasible (the first criterion measured) can one measure reporting, importance, and lack of bias. And only among those trials that are both feasible and reported properly can one measure their importance and lack of bias, and so forth. Thus, except for feasibility, one cannot determine the proportion of all trials that were properly reported, were importance, or evinced lack of bias.

“Thermometer” is an apt metaphor. Please see response to Essential Revisions # 4 regarding the retrospective nature of our assessment.

The sequential nature of our assessment is indeed a limitation for readers wanting to know the fraction of trials fulfilling each of the four criteria. This reflects a compromise between our aspirations and our labor capacity. However, we emphasize that our pre‐specified primary outcome was the fraction of trials fulfilling all informativeness criteria. We have also elaborated upon the following in our limitations section:

Line 521 – 533 “Third, we used a longitudinal and sequential approach, since some of the conditions were only relevant once others had been met. For example, incorporation into a clinical synthesizing document can only occur once results have been reported. Our sequential approach enabled us to address our primary outcome with an economy of resources. However, our study does not enable an assessment of the proportion of trials fulfilling three of the four criteria in isolation from each other. In addition, changes in research practices or policy occurring over the last decade might produce different estimates for the proportion of randomized trials that are informative.”

Reviewer 2

The authors present a systematic review of 125 trials (in three disease areas: ischemic heart disease, diabetes mellitus and lung cancer) available on clinicaltrials.gov, with the goal of estimating how often clinical trials result in a meaningful impact on clinical practice (or policy or research decisions). This is a very interesting and important question which, if not approached carefully, could lead to results that are misleading and/or difficult to interpret.

Thank you!

To help reduce the potential for misleading results, the authors employed sensible criteria for inclusion of trials in this analysis (with trials being independently evaluated by multiple authors to determine whether they should be included). Once trials were selected, they had to be classified as "informative" or not. While such classification is, by definition, subjective, the authors attempted to make this process as objective as possible. They proposed a definition of "informative" based on four factors: feasibility (of achieving the target enrollment/completing the trial in a timely fashion), reporting (of results; either on clinicaltrials.gov or in a publication), importance (of the clinical question being addressed) and the quality of the design. As with the evaluation of trial inclusion, the authors independently evaluated each trial to determine informativeness.

The authors provide a thorough discussion of key issues that could affect the interpretability of a trial and include a nice discussion of the limitations of their research. To me, the major limitation of this analysis (which the authors acknowledge) is that "clinically interesting/informative" is subjective. It is possible that their criteria will miss informative trials (or classify truly non‐informative trials as informative). For example, while perhaps uncommon, a trial could be classified as non‐informative due to poor design selection, but could end up being truly informative due to overwhelmingly positive results. Also, the "importance" component of their classification criteria could lead to truly important "niche" trials being misclassified as non‐informative.

Thank you for this assessment. We agree that our measures of informativeness are imperfect. We hope that we have been forthright in the limitations of our approach. We believe that our first study limitation (lines 498 ‐ 513) outlines the issues highlighted above.

Reviewer 3

The paper describes an ingenious and painstakingly reported method of evaluating the informativeness of clinical trials. The authors have checked all the marks of robust, welldesigned and transparently reported research: the study is registered, deviations from the protocol are clearly laid out, the method is reported with transparency and all the necessary details, code and data are shared, independent raters were used etc. The result is a methodology of assessing informativeness of clinical trials, which I look forward to use in my own content area.

Thank you!

My only reserve, which I submit more for discussion than for other changes, is the reliance on clinicaltrials.gov. Sadly, and despite tremendous efforts from the developers of clinicaltrials.gov (one of the founders is an author of this paper and I am well‐aware of her unrelenting work to improve reporting of information on clinicaltrials.gov), this remains a resource where many trials are registered and reported in a patchy, incomplete or downright superficial and sloppy manner. For outcome reporting, the authors compensate this limitation by searching for and subsequently checking primary publications. However, for the feasibility surrogate this could be a problem. Also, for risk of bias, for the trials the authors had to rate themselves (i.e., ratings were not available in a high‐quality systematic review), what did the authors use, the publication or the record from the trial registry?

Thank you. We agree that the sources of data that we relied on for this assessment are imperfect.

We added the following to our limitations section:

Lines 534 ‐ 535 “Fourth, our evaluation is limited by the accuracy of information contained in the ClinicalTrials.gov registration record...”

We also added the following sentence to clarify the sources of our risk of bias assessment in eMethods 9:

Lines 996 – 998 “Information from both the primary study publication and the ClinicalTrials.gov registration record were used in our risk of bias assessments.”

In general, it seems like a problem for this sophisticated methodology might be the scarcity of publicly available information that is necessary to rate the proposed surrogates. Though the amount of work involved is already tremendous, the validity of the methodology would be improved by extracting information from a larger and more diverse pool of sources of information (e.g., protocols, regulatory documents, sponsor documents).

In that sense, maybe it would be interesting for the authors to comment on how their methodology would be improved by having access to clinical trial protocols and statistical analysis plans. Of course, one would also need to know what was prospective and what was changed in those protocols, i.e., having protocols and statistical analysis plans prospectively registered and publicly available. Having access to these documents would open interesting possibilities to assessing changes in primary outcomes, though as the authors say that evaluation would also require making a judgement as to whether the change was justified. Relatedly, perhaps registered reports could be a potential candidate for clinical trials that would also support a more accurate assessment of informativeness, per the authors' method, provided the protocol is made openly available.

Still related to protocols, were FDA documents consulted for pivotal trials, which again could give an indication of the protocol approved by the FDA and subsequent changes to it?

We appreciate this comment and suggestion! And thanks for acknowledging the work it took to derive our estimates. Please see our full response to Essential Revision # 2 above.

Author Response

Reviewer 2

The authors use the model of polyamine attraction and build on their previous observation that mated Drosophila females show increased attraction to polyamines that is outlasting a short term modulation of olfactory sensory neurons. Females do not require exposure to seminal fluid or sperm and do not need to start to ovulate for this change in preference. This is remarkable since the vast majority of female postmating changes in behavior have been shown to rely on sex peptide in the male seminal fluid. It also sets an exciting starting point for the present work, suggesting new mechanisms of how a female can adjust their behavior to mating state.

We thank the reviewer very much for their encouraging comments.

The authors find that females have to be able to smell odors detected by the Or system (but not polyamines) during mating in order to change their preference for polyamine.

Mushroom body Kenyon cells are required during mating and during choice behavior for the polyamine preference of mated females. Activation cVA responsive PAM-b1 neurons of the mushroom body is sufficient to replace the mating experience and change polyamine preference in virgin flies. Activation of the same neurons during mating abolishes the preference development. Other specific mushroom body neurons are required during the choice behavior to promote attraction in mated females or repress it in virgins. Calcium imaging of different mushroom body neurons does not uncover a clear difference in polyamine response between mated and virgin flies. Connectome mining and genetic silencing further indicates that circuit motifs in the lateral horn are also involved in the response to polyamines and might interact with mushroom body circuits.

While the exact circuits and mechanisms of plasticity that explain the change in postmating preference of polyamines remain to be discovered, this work makes substantial progress in identifying neurons that have a strong impact on development or expression of the preference. It is an exciting paradigm that invites further research.

This work explores a very interesting example of state-dependent behavioral change in Drosophila. Previously, state dependent changes in sensory neurons have been demonstrated- here, the authors tackle the experimentally much more challenging task of identifying changes in higher order processing areas. The data suggests that polyamine attraction is encoded by a recurrent network of mushroom body neurons. Although the authors do not demonstrate an exact mechanism by which mating/male exposure reconfigures this polyamine attraction network, they have made a substantial advance for our understanding how odor valence is encoded in a flexible and experience dependent way by identifying and characterizing the neuronal players and their roles in induction and expression of preference behavior.

Their experimental paradigm is special in that it is not a case of classical odor reward learning (mating could be the rewarding experience, but polyamine odor does not have to be present during mating to induce preference). It is also special in that it is a case of long lasting mating induced behavior change that is not dependent on sex peptide or other male seminal fluid proteins. The paradigm has thus great potential to uncover novel mechanisms of encoding experience and adaptively changing behavior.

Reviewer 3

Mating changes behavior of female fruit flies. Authors previously reported that putrescine-rich foods increase number of progenies per mated female and mated females detect putrescine with IR76b and IR41a and are attracted to putrescine odor (Hussain, Zhang et al., 2016). In another paper, authors reported that this change of putrescine preference is mediated by sex peptide receptor (SPR) and its ligand, myoinhibiotry peptides (MIPs; Hussain, Ucpunar et al., 2016). In yet another paper, authors reported that two types of dopaminergic neurons (DANs) which innervate alpha prime 3 (a'3) or beta prime 1 (b'1) compartment of the mushroom body (MB) show enhanced response to cVA, the male sex pheromone 11-cis-Vaccenyl acetate (Siju et al., 2020). The present study investigated neural circuits that potentially link these observations.

The authors first showed that putrescine-attraction in mated females is sustained over 7-days, which cannot be explained by SPR-MIP dependent mechanism that disappears in one week. Then they explored a factor that is transferred from males during copulation and required for putrescineattraction in mated females. They found that blocking synaptic transmission of cVA-sensitive OR67d olfactory receptor neurons during 24 hour period of pairing with males reduces putrescineattraction 3-5 days later (Figure 1). On the other hand, experiments with mutant flies lacking ability to generate eggs or sperms indicated that fertilization is not essential for the change in odor preference. In a proposed scenario, cVA transferred to the female during copulation activates DANs projecting to the b'1 and that in turn induces a shift in how the MB regulates the expression of polyamine odor preference, possibly by alternating activity of MB output neurons (MBONs) in the beta prime 2 (b'2) compartment.

Some data are in line with this scenario. Blocking synaptic transmissions of Kenyon cells during mating or odor preference test reduced attraction to putrescine (Figure 2). Activation of dopaminergic neurons projecting to the beta prime 1, gamma 3 and gamma 4 in virgin females promoted attraction to putrescine when tested 3-5 days later (Figure 3). Flies expressing shibire ts1 in the MBONs in the b'1 compartment showed reduced putrescine preference when females were mated at restrictive temperature (Figure 4). Using calcium imaging and EM connectome, authors also found candidate lateral horn output neurons that may mediate putrescine signals from olfactory projection neurons to the b'1 DANs.

This study utilized molecular genetic tools, behavioral experiments and calcium imaging to comprehensively investigate neural circuits from sensory neurons for cVA or putrescine to the learning circuits of the MB. Addressing points detailed below will strengthen a causal link between enhanced cVA response in beta prime 1 DANs and enhanced putrescine preference in mated females.

1) The MB is the center for olfactory associative learning. It is not so surprising that 24-hour long activation of any MB cell types have long-term consequence on fly's odor preference. As authors showed in Hussain et al., 2016 and Figure S1, mated females change preference to polyamines but not ammonium. Therefore, it is important to show odor specificity of the circuit manipulations to claim that phenomenon in mated females are recapitulated by each manipulation. Wang et al., 2003 (DOI:https://doi.org/10.1016/j.cub.2003.10.003) reported that blocking a broad set of Kenyon cells impairs innate odor attraction to fruit odors and diluted odors but not repulsion.

We very much appreciate the thorough comments of this reviewer. We have carried out the experiments suggested in the editor’s summary. Due to time and people limitations encountered by the lab’s move during the week of July 11, we were forced to prioritize the number and type of experiments we carried out for this revision.

We also agree that the change in odor preference due to manipulation of KCs during test is not a very surprising result. We do, however, strongly believe, that the result we received with the inhibition of KCs during mating is not expected. Previous studies using associative learning paradigms suggested that KCs are not essential during learning but only during test:

• McGuire, S. E., Le, P. T. & Davis, R. L. The Role of Drosophila Mushroom Body Signaling in Olfactory Memory. Science 293, 1330–1333 (2001).

• Schwaerzel, M., Heisenberg, M. & Zars, T. Extinction Antagonizes Olfactory Olfactory Memory at the Subcellular Level. Neuron 35, 951–960 (2002).

• Dubnau, J., Grady, L., Kitamoto, T. & Tully, T. Disruption of neurotransmission in Drosophila mushroom body blocks retrieval but not acquisition of memory. Nature 411, 476–480 (2001).).

Only a very recent study (currently only on BioRXiv, Pribbenow et al. 2022 (https://www.biorxiv.org/content/10.1101/2021.07.01.450776v2) showed that KC output is required during appetitive training suggesting that postsynaptic plasticity in KCs is needed to establish appetitive memories.

These new findings are in line with our results given that the KCs are likely providing the odor input to DANs and MBONs. We have included a paragraph in the discussion section.

2) Requirement of PAM-b'1 DANs for putrescine-attraction in mated females should be demonstrated. The authors suggested existence of alternative mechanisms that may mask requirement of PAM-b'1 (Figure 3B). In a previous study, the authors reported SPR-dependent mechanism. I suggest testing the requirement of PAM-b'1 DANs in SPR mutant background or oneweek after mating when SPR-dependent effect on sensory neurons disappear.

Please see response above to point 4 of the editorial summary. SPR mutants do not undergo the switch in polyamine odor preference. Therefore, SPR signaling likely presents this compensatory mechanism. Nevertheless, MBON-β’1 is required during mating for the transition from virgin to mated female behavior. In the future, we plan to analyze the relationship between SPR and this MBON in detail.

3) Activation phenotype of MB188B-split-GAL4/UAS-dTrpA1 cannot be ascribed to activation of PMA-b'1 alone because of additional expression in DANs projecting to gamam3 and gamma4 compartments. Run the same experiment with more PMA-b'1 specific driver line.

Please see response to point 3 of the editorial summary. We do observe a very high preference in virgins with the genetic background MB025B>TrpA1 even in the absence of temperature-mediated activation. Therefore, the experiment, unfortunately, provided no meaningful result. We have instead adjusted the text to include a possible role of γ3 and γ4.

4) Some of EM connections are too low to be considered (e.g. two in Figure S3 and five in Figure 5). Although these connections could be functional, previous EM connectome analysis typically set much higher threshold (e.g. 10 in Hulse et al., 2021 DOI: 10.7554/eLife.66039) to avoid considering artifacts.

We thank the reviewer for pointing this out. We have included this reference and the customary threshold of 10 in the methods section.

5) Data for Kenyon cells (Figure 2) and LHON (Figure 6) are interesting, but not directly related to other data regarding PAM-b'1 and MBON-b'1. Due to lack of long-term changes in MBON's odor responses in mated females (Figure 5), it is unclear what information needs to be read out from Kenyon cells and how does it affect processing of putrescine signals potentially carried by LHAD1b2.

We agree. In the revised version of the manuscript, we now show that LHAD1b2 neurons appear to undergo a change upon mating. Please see response to the editor’s summary, point 6.

Kenyon cell output during mating could be required for odor input and odor (i.e. cVA)-mediated activation of MBONs and DANs involved. This would be in line with our data in Fig. 1D,E where we show that ORCO and OR67d OSNs are required during mating to induce the change in behavior.

Author Response

Reviewer 1

Comment 1

Selecting appropriate Bioinformatics approaches to arrive at a consensus classification of SNVs can be labor intensive and misleading due to discordance in results from different programs. The authors evaluated 31 Bioinformatic or computational tools used for in silico prediction of single nucleotide variants (SNVs). They selected a filtered list of SNVs at the HBA1, HBA2, and HBB genes, and compared in silico prediction results with annotations based on evidence in literature and databases curated by an expert panel comprising coauthors of this study. They found both specificity and concordance among different tools lacking in certain aspects when thresholds are chosen to maximize the Matthews correlation (MCC) and thus proposed an improved strategy. For this, the authors focused on the top prediction algorithms and varied their decision thresholds separately for pathogenic and benign variant classification and optimized the predictive power of these tools by choosing thresholds that generated at least supporting strength likelihood ratios (LRs) to achieve balanced classification.

The authors have likely spent significant effort annotating the list of pathogenic or benign SNVs in adult globin genes by iteratively evaluating independent annotations submitted by experts and arriving at a consensus. These annotations when added to the database of SNVs might improve the breadth of knowledge on the pathogenicity of adult globin SNVs and likely lead to an improved prediction by the existing tools. Further, setting non-overlapping thresholds for pathogenic and benign variants seems to improve the balance in the prediction of some of the tools (with certain tradeoffs) in the context of the gene and the variant class. This is consistent with the findings of Wilcox et. al., while at the same time the authors have focused on globin variants and compared many more programs. Thus, while not a novel approach, the scale is expansive, and might guide future studies with the improved ACMG/AMP framework.

Response: We would like to thank the reviewer for the positive comments and for appreciating the potential impact of the manuscript.

Comment 2:

However, there are certain caveats from my perspective and these need to be explained or improved.

• The authors' approach relies heavily on the revised consensus annotations which, from my understanding, is essentially being considered as a "truth dataset", whereas variants are classified in silico according to existing annotations in the databases. The binary classification metrics compare the in silico predictions to the authors' annotations and these showed low specificity but higher sensitivity and accuracy indicating that many benign variants were misclassified as pathogenic. The authors have not clearly mentioned whether the "observed_pathogenecity" information in the input dataset in supplementary file 2 is from the Ithagenes database or the authors' reannotations. Hence, if a significant number of pathogenic variants were reannotated as benign by the expert panel, that will likely result in the tools misclassifying them as pathogenic since the tools rely on database annotations.

Response: The IthaGenes database did not provide an annotation about the clinical impact of each globin gene variant before this study. Nevertheless, as part of this study, an initial annotation was provided based on the information already annotated in the database and the pathogenicity criteria defined for this study (pg 7). This initial set was subsequently provided to the experts that proceeded with confirmation or reclassification of each variant’s pathogenicity using a Delphi approach. The final classification was used for the study and is now also included in IthaGenes. This process is now clarified in the Methodology (pg. 7-8; lines 145-147 & 155-160), while the initial and final classification are provided in the dataset file (Supplementary File 2; sheet “Input-Full dataset”). In addition, Supplementary Figure 1 illustrates the changes in pathogenicity annotation after the expert evaluation, demonstrating that annotation of benign variants to pathogenic and vice versa was minimal.

We consider the final annotation as the best available evidence regarding the pathogenicity of globin gene variants due to the involvement of experts responsible for molecular diagnosis of haemoglobinopathies in five countries worldwide and the use of a Delphi approach for the variant pathogenicity.

Comment 3

• The results and measure of success focus on different benchmarks for the two major analyses the authors performed. While they generated a lot of data, they have not attempted to explore and present all facets of the data for each analysis. For instance, to assess the predictive power of the 31 tools initially, the authors focus on benchmark metrics for binary classification such as Accuracy, Sensitivity, Specificity and MCC. However, in the later improved approach, the focus is on LRs but the effect of separate thresholds for pathogenic and benign classification on accuracy, sensitivity, and specificity and MCC are not explored in the results instead just mentioning PPV for certain variant types, tools, and genes.

Response: In the latter improved approach, we do not use a binary prediction, but instead we trichotomize the problem to define different thresholds for each pathogenicity class. Therefore, benchmark metrics like MCC are not informative as many of the variants are not classified (i.e., they are classified as VUS) due to the grey zone between the benign and pathogenic thresholds. The benign and pathogenic thresholds are derived from two different binary classifiers, with their corresponding binary metrics provided in Supplementary File 3. We have now included the sensitivity and specificity of the pathogenic and benign classifiers, respectively, in Table 2 and we discuss them in pg 15-16 (lines 338-343).

Moreover, Table 2 presents the analysis on the full dataset and, also, in different subsets of the dataset, based on variant type (missense/non-missense) and globin genes.

Comment 4

• There is a general trade-off to altering thresholds to increase specificity which leads to reduced accuracy and sensitivity. Thus, in this case, the improved approach suggested by the authors increases specificity but there is a simultaneous reduction in accuracy and sensitivity thus leading to the potentially higher misclassification of pathogenic variants as benign. One has to consider then, whether this is ideal in the case of globins where an in silico misclassification of pathogenicity can be easily verified by subsequent diagnostic testing to confirm whether the variant actually affects hemoglobin. Overclassification of pathogenicity in the case of globins is thus not necessarily a major problem since they will not directly lead to patients receiving treatment before additional confirmatory tests. However, misclassification of pathogenic variants as benign will pose greater harm to individuals at risk of disease.

Response: The reduction of accuracy in the improved approach is not due to the misclassification of pathogenic variants as benign, but instead due to misclassification of benign or pathogenic variants as VUS. The reviewer is correct the LR-based approach decreases the accuracy of the method, but at the same time it increases the confidence of a pathogenic or benign classification. This is the basis of the Bayesian ACMG/AMP framework. We further clarify this point on pg 17 (lines 384-386).

Misclassification of benign or pathogenic variants as VUS will not have a significant impact on variant classification. However, we do not agree that overclassification of pathogenic variants is not a major issue, because many countries provide prevention programmes based on prenatal screening (see IthaMaps: https://ithanet.eu/db/ithamaps?hc=3). Therefore, a misclassified benign or VUS variant as pathogenic can lead to unnecessary abortions, preimplantation genetic diagnosis tests and can have devastating psychological and economic impact on lives of affected individuals

Comment 5

• This is a largely descriptive study of the performance of various programs, but the authors did not attempt to explain why according to them the various tools performed a certain way in their analysis. Thus, their rationale for proposing the improved approach of separate thresholds for pathogenic and benign variants was unclear. Attempting to understand whether there is a correlation between the type of data the tool uses, and its performance could explain the tools' prediction power and how to improve it. For instance, some of the tools are metapredictors that take as input scores from various other tools also tested in this study. Thus, there will be some redundancy in the final classification.

Response: We thank the reviewer for the suggestion. We have now addressed this point at the revised manuscript (pages: 18 – 19, lines: 397-408 and 417-426) by adding two paragraphs discussing the low concordance rate between predictors, aligned with previous studies. We also discuss the main reasons for the superior performance observed for meta predictors.

Comment 6

• Expanding on the previous point, the reason for discordance in HBA genes but concordance in HBB was unclear. It might be a result of the bigger HBB dataset compared to HBA although the authors did not explore or mention whether the size of the dataset correlates with concordance. They also did not test for concordance or discordance after the separate thresholds were applied so it is not clear whether their proposed approach improves concordance for the HBA variant predictions of the top tools.

Response: In the later improved approach, we have assessed the concordance of the top performing tools as shown in Figure 3B and 3C, but without grouping by gene. We have now added a heatmap of concordance in Supplementary Figure 4 which still shows higher concordance for pathogenic variants on HBB (also see pg , lines 360-364).

The lower concordance that the tools exhibit for HBA1 and HBA2 can be explained by the fact that the pathogenicity of HBA1 and HBA2 variants almost always cannot be determined by the phenotype at the heterozygous state simply, as is the case for HBB, due to gene numbers (4 alpha alleles VS 2 beta alleles).

This exacerbates the frequent confusion between the categorization of pathogenic at the gene level (reduced expression) versus the phenotypic level! (See MacArthur’s seminal paper MacArthur DG, et al. Guidelines for investigating causality of sequence variants in human disease. Nature. 2014 Apr 24;508(7497):469-76. doi: 10.1038/nature13127. PMID: 24759409; PMCID: PMC4180223 – although you must be familiar with it). We have discussed this point in pg 18-19 (lines 409-416).

Author Response

Reviewer 1

In this manuscript the authors set out to characterise the process of differentiation of inner cell mass cells within the mouse blastocyst into either epiblast or primitive endoderm, which is a binary fate choice, using various models. To this end, they made use of well-established reporter cell lines previously generated in their lab as well as a widely used fluorescent system (FUCCI) that allows stages in the cell cycle to be visualised and sorted. The experimental output was compared with computational models and published data generated from mouse embryos during the process of primitive endoderm and epiblast segregation. Their data uncovered interesting mechanistic insight into the dynamics of the cell cycle and how these correlate with lineage choice and amplification. The methods have been carefully considered and validated in previous work by the group and the analysis is thorough. The single cell profiling is particularly well presented, and backed up by immunofluorescence data using well-characterised lineage reporters with appropriate statistical analysis. Probably the most interesting finding, which the authors identify as unexpected, is the considerable lengthening of the G1 part of the cell cycle in cells differentiating into PrE, but coinciding with a reduction in overall cell cycle length. Also, cell cycle length from mother to daughter cells in all conditions appears not to be inherited, yet sister cells, and to a lesser extent, cousins, appear to retain similar cell cycle dynamics. This feature is attributed to differential levels of FGF, suggested by the use of PD03 or PD17 as downstream inhibitors. Not surprisingly, levels of the PrE-associated factor Hex could predict the likelihood of differentiation to PrE, but also higher levels of Hex correlated with a shorter cell cycle. Also, blocking MEK/ERK signalling increased cell cycle duration as well as reducing differentiation to PrE in the culture conditions designed to promote differentiation to epiblast. The aims of the paper appear to be achieved and the results adequately support the authors' conclusions. A similar system to the one established here could be envisaged for downstream developmental processes, such as those involving binary decisions for specific tissue formation in organogenesis, but would require the generation and validation of different reporter cell lines.

We thank this reviewer for their support of our manuscript.

Reviewer 2

In this paper, the authors show that the maintenance of pluripotent mouse stem cell cultures and their conversion towards primitive endoderm relies on selective effects of specific culture media that act on the survival and cell cycle properties of different primed subpopulations. They further demonstrate that FGF/ERK signaling underlies correlations between cell cycle length in daughter cells, and identify characteristic, lineage-specific differences in relative G1 length as cells differentiate along the endodermal lineage that is recapitulated in vivo. The study is based on a technically challenging combination of long-term time-lapse imaging with reporters for cell cycle and lineage priming and delivers new insight into the old question of whether extracellular signals regulate differentiation in cell populations by selection or by induction.

A central conclusion of the study, that media conditions control differentiation through cell cycle regulation, is based on the analysis of time-lapse imaging of cells in PrE differentiation and pluripotency conditions. Even though the authors acknowledge that cell death contributes to population composition, the manuscript mainly talks about changes to the cell cycle. This focus on the cell cycle does not do the data justice, especially in the context of PrE differentiation: The time-lapse movie shows that there is massive cell death from 24 h onwards, to a degree that there is no net growth of the population but rather a decline in cell numbers over the course of the experiment. This impression is supported by the lineage trees, where the NEDiff cells appear to selectively die, rather than being outcompeted by PrE cells. Thus, while cell cycle regulation clearly contributes to differentiation at the population level, it remains an open question how important this effect is in the chosen differentiation paradigm, compared to selective effects that act through cell survival.

• We acknowledge that there is a large amount of cell death in the beginning of differentiation and believe this could be a response to changes in media and cytokines. This is also observed in other differentiation and reprogramming protocols (Ying and Smith 2003; Hayashi et al. 2011; Yasunaga et al. 2005; Argelaguet et al. 2019; Rugg-Gunn 2022).

• While our original analyses were focused on cell cycle, we did not mean to imply that survival is irrelevant to selecting the correct populations at the end of differentiation. Although there is clearly an increase in NEDiff cell death, these rates fluctuate during differentiation (Table S2) and it is difficult to make any hard conclusions about the timing of selection. In addition, we find no signature for apoptosis in all scRNA-seq clusters associated to early NEDiff. However, we thank the reviewers for raising this issue and we address the issue of survival more extensively in the revised manuscript (lines140-142, and 342-347, in addition to a new modelling section described below).

• To further explore when relative survival is most important for effective differentiation, we have reformulated our model. Our new modelling results show that changes in the survival rates have stronger impact shifting the cell proportions at later stages of differentiation. Phase diagrams in Figure 3- Supplement 1 show that at day 5 reaching an appropriate proportion of PrE requires less change in the survival rates than in doubling times, suggesting that survival can have greater impact on the ratio than cell division. However, at day 3, the modelling suggests the opposite, consistent with a first wave of a cell cycle regulation and PrE fastest division time (Fig. 2D). We have discussed this in the Results section, lines 162-168.

• We have added survival alongside proliferation to the abstract.

Reviewer 3

The manuscript of Birckman and colleagues tackles the link between lineage priming, lineage specification, and cell cycle in the ESCs culture. This is an interesting piece of work, with several noteworthy findings, that elegantly explain how lineage priming can be efficiently achieved during the changing cultural conditions. There are several interesting points raised by the authors, relating to lineage priming, cell specification, and cell cycle, that can be presented to the scientific community. Namely:

• Differential regulation of the cell cycle can tip the balance between populations of cells primed to different cell fate choices (here PrE and Epi).

• Different culture conditions favour acceleration/stimulation of the cell cycle of different cell populations.

• Only a small population of cells from the original culture enters a differentiation process which is followed by selected expansion and/or survival of their progeny.

• In the case of endodermal type specification (towards PrE), a shortening of the cell cycle is accompanied by the proportional relative increase of G1 phase length.

• FGF activity is responsible for cell cycle synchronisation, required for the inheritance of similar cell cycles between sisters and cousins

Unfortunately, in the current version of the manuscript, the authors try to create the impression that the relationship between cell cycle, heterogeneity and cell fate found in ESCs can be directly translated to the in vivo system. It is not clear, however, how easily and reliably the information about the cell cycle in ESCs can be translated to an in vivo setting. The timeline of PrE vs Epi specification in vivo and in vitro are completely different. In embryos, PrE is specified within 24h, whereas with in vitro it takes 6 days. I cannot see how these two timelines - and also different cell cycle lengths - can be reliably compared.

• We were aware of the difficulties inherent in this comparison and apologize if our statements were not sufficiently conditional. We have now added caveats to the results section (line 328) and a revised discussion that explicitly discusses the difference in time lines (lines 404-409).

• On line 111, we added a clarification that our in vitro model is a tool for deconstructing “transcriptional signatures” as this is precisely what we measure both in vivo and in vitro.

• On line 322 we clarified that even though the time frames are different, we found a similar G1 signature trend in our in vitro dataset than the one found in the in vivo published dataset.

• On line 337 we amended the sentence to clarify that some aspects of cell cycle regulation found in vitro could be also exploited in vivo.

• On line 414 we have added a caveat line explaining that the use of G1 to drive increasing levels of commitment is a facet of cell fate choice both in vivo and in vitro, even though the time scales are different.

Author Response

Reviewer 1

In this article Farrell et al. leverage existing datasets which measure frailty longitudinally in mice and humans to model 'robustness' (the ability to resist damage) and 'resilience' (the ability to recover from damage), their dynamics across age, and their relative contributions to overall frailty and mortality. The concept of separating damage/robustness from recovery/resilience is valid and has many important applications including better assessment and prediction of effective intervention strategies. I also appreciate the authors' sophisticated attempts to effectively model longitudinal data, which is a challenge in the field. The use of human and mouse data is another strength of the study, and it is quite interesting to see overlapping trends between the two species.

While I find the rationale sound and appreciate the approach taken at a high level, there are a few key considerations of the specific data used which are lacking. The authors conceptualize resilience based on studies which primarily use short time scales and dynamic objective measures (ex. complete blood cell counts in Pyrkov et al.) often in conjunction with an acute stress stimulus. For example, they heavily cite Ukraintseva et al. who define resilience as "the ability to quickly and completely recover after deviation from normal physiological state or damage caused by a stressor or an adverse health event."

Resilience and robustness are typically studied at short time-scales, with small numbers of continuous health attributes. We study transitions of binary health attributes, which we call damage and repair, and which we suggest should be thought of as resilience and robustness. Our approach is well suited for studying large numbers of binary health attributes over long time-scales without acute external stimuli. How resilience and robustness in these limits (binary, large numbers, long times, intrinsic dynamics) compare with resilience and robustness as has been typically measured (continuous, short times, acute stimuli) is an interesting and important question that arises from our work.

Given these definitions, the human data used seem to fit within this framework, but we should carefully consider the mouse data. The mouse frailty index is a very useful tool for efficiently measuring the organismal state in large cohorts. A tradeoff for quickly measuring a broad range of health domains is that the individual measurements are low resolution (categorical) and involve inherent subjectivity (which may be considered part of the measurement error). Some transitions in individual components are due to random measurement error and I believe this is especially likely with decreases (or 'resilience' transitions).

The reason I think the resilience transitions are subject to high measurement error is that I am skeptical as to whether many of the deficits in the mouse index are reversible under normal physiologic conditions. For example, it is exceptionally unlikely for a palpable/visible tumor to resolve in an aged mouse over the time scales studied here, thus any reversal that was observed is very likely due to random measurement error. Other components which I have doubts about reversibility are alopecia, loss of fur color, loss of whiskers, tumors, kyphosis, hearing loss, cataracts, corneal capacity, vision loss, rectal prolapse, genital prolapse.

In summary, I applaud the authors' efforts in generating complex models to better understand longitudinal aging data. This is an important area that needs further development. I appreciate their conceptualization of resilience and robustness and think this framework has an important place in aging research. I also appreciate their cross-species approach. However, the authors may have over-conceptualized and made some assumptions about the mouse data which may not be valid. It will be important to assess the results with careful consideration of the time scales of the underlying biology and the resolution and measurement error inherent to these tools.

For each of our mouse attributes, there are published studies demonstrating reversibility (see our new Supplementary Table 1). Nevertheless, we cannot distinguish what causes the observed discrete transitions (measurement error, stochastic fluctuations in underlying organismal features, or logisticlike continuous transitions in underlying continuous variables). We analyze the discrete data as given.

The question of time-scale is interesting. From survival curves of individual binarized attributes, we obtain reasonable fits to exponential models (i.e. a single timescale) see Fig 5 supplement 1 and 2. For the human data there are a broad range of timescales for both robustness and resilience. For the mouse data there appears to be a similarly broad range (note the logarithmic scale) though with considerable uncertainty. We work with the data we have, so we are unable to probe shorter timescales than the measurement interval (months for mice, and years for humans). We have reinforced this caveat in the discussion.

Reviewer 2

This study uses repeated measurements of the frailty index (FI), composed of multiple binary parameters. It is posited that newly detected changes in the number of these parameters represent damage and that the parameters that have previously been detected but are not detected currently represent damage repair. Statistical treatment then follows, deriving resilience and robustness and their changes over time. This is an interesting idea. Strengths of the study include analyses across species (mice and humans), including multiple datasets in mice.

To be clear, our data analysis is on the binary health attributes that are used in the FI. By considering the damage/repair (binary transitions) of individual attributes, we can obtain the aggregate damage/repair rates.

What are the elements of FI that increase at each period of life, and what are those that decrease? For example, humped phenotype or alopecia are more likely to appear in old mice and are essentially irreversible, whereas weight loss due to infection may be more common in young mice and is reversible. Therefore, the choice of health deficits would affect the model and, for example, may artificially lead to a decreased value of what the authors call damage repair.

More generally, information on the frailty index lacks sufficient details. I doubt that this method has sufficient accuracy to draw conclusions from as little as 32 female mice (21 + 11 animals in datasets 1 and 2) and 63 males (13 + 6 + 44 animals in datasets 1, 2 and 3). Also, only 25 enalapril-treated mice of each sec were analyzed, and only 17 exercised mice (11 females and 6 males). The number of human participants is large, but the total follow-up period is not shown, and the subjects were assessed based on 23 parameters only.

We have not examined other choices of health attributes. While we picked standard sets from available data, we do not know whether other attributes would behave differently. It would be difficult to do our detailed modelling on single attributes in the mouse data, since the data is so sparse. Our approach was developed specifically to be able to draw conclusions from limited mouse data. Where possible we aggregate the individual mice, sex, health attributes, studies, and measurement times. The analysis of human data shows that the approach generalizes.

While we have mostly not studied individual attributes (we have considered survival times, but without age or time effects), we would expect that some of them may have behavior that qualitatively differs from our aggregate results. If attribute selection was biased towards (or away from) qualitatively distinct behaviors that would, of course, be reflected in aggregate results. We suspect that this would be unlikely, but that any such distinctive behavior would be interesting and important to identify and understand. We have added some discussion on this point, since we cannot exclude this possibility.

A key assumption in this work is that increased FI is equivalent to the rise in damage. However, the relationship between changes in FI and damage is unknown. One can imagine a situation when damage increases, but protection also increases. In this case, fitness may increase, decrease or remain unchanged. What is the basis for calling an increased number of health deficits damage? Is there a more reliable method to measure damage that could support the authors' claims?

See also discussion point #1 in essential revisions. We call binary states 0 “healthy” and 1 “damaged”, but we could instead say “more healthy for most individuals” and “less healthy for most individuals” – where “healthy” means associated with desirable (low FI and low mortality) health outcomes. We have not explored other measures of organismal damage. We have not explored how interactions between variables could affect resilience or robustness for individuals. We do not think that alternative approaches would be easy to study without much more data (for mice) that is more finely resolved in time (for mice and humans). We are quite happy to have found an approach to use with binarized data, but would welcome viable alternative approaches to compare with.

Reviewer 3

In this work, the authors aimed at investigating two related components of aging-related processes of health deficits accumulation in mice and humans: the processes of damage (representing the robustness of an organism) and repair (corresponding to resilience), and at determining how different interventions (the angiotensin-converting enzyme inhibitor enalapril and voluntary exercise) in mice and a representative measure of socio-economic status (household wealth) in humans affect the rates of damage and repair. Two key elements in this study allowed the authors to achieve their goals: 1) the use of relevant data containing repeated measurements of health deficits from which they were able to compute the cumulative indices of health deficits in mice and humans and which are also necessary to evaluate the processes of damage and repair; 2) the methodological approach that allowed them to formulate the concepts of damage and repair, model them and estimate from the available data. This methodological framework coupled with the data resulted in important findings about the contribution of the age-related decline in robustness and resilience in health deficits accumulation with age and the differential impact of interventions on the processes of damage and repair. This provides important insights into these key components of the process of aging and this research should be of interest to both lab researchers who plan experimental studies with laboratory animals to study potential mechanisms and interventions affecting health deficits accumulation as well as researchers working with human longitudinal studies who can apply this approach to further investigate the impact of different factors on robustness and resilience and their contribution to the overall health deterioration, onset of diseases and, eventually, death.

The key strength of this work is a rigorous analytic approach that includes joint modeling of longitudinal measurements of health deficits and mortality (in mice). This approach avoids biased inference which would be observed if longitudinal data were analyzed alone, ignoring attrition due to mortality. Another strength is a comprehensive analysis of both laboratory animal data that allows exploring the impact of different interventions on the processes of damage and repair and human data that allows investigating disparities in these processes in individuals with different socioeconomic backgrounds (represented by household wealth).

One weakness (which is commonplace for human studies) is self-reported data on health deficits in humans which makes it difficult to compare with lab data where deficits are assessed objectively by lab researchers. The subjective nature of health deficits measurements complicates the interpretation of findings, especially about repairs of deficits. In addition, it is not clear whether the availability/absence of caregivers at different exams/interviews factors into the answers on difficulty/not difficulty with specific activities constituting health deficits and, respectively, into their change over time reflected in damage/repair estimates.

Variability of the evaluator is expected in any longitudinal study, and amounts to a variety of measurement error. The question of whether there are age-effects in the measurement error, such as bias or age-dependent variability is interesting. For the mouse data, evaluator training is designed to minimize such errors and inter-evaluator differences are not large (Feridooni et al, 2015; Kane et al, 2017). For the human self-report data any such age-effects are unavoidable.

Author Response

Reviewer 1

Sadeh and Clopath analyze two mouse datasets from the Allen Brain Atlas and show that sensory representations can have apparent representational drift that is entirely due to behavioral modulation. The analysis serves as a caution against over-interpreting shifts in the neural code. The analysis of data is coupled with careful modeling work that shows that the behavioral state reliably shifts sensory representations independently of stimulus modulation (rather than acting as a gain factor), and further show that it is reproducibly shifted when the behavioral state is adequately controlled for. The methods presented point towards a more careful consideration and measurement of behavioral states during sensory recordings, and a re-analysis of previous findings. The findings held up for both standard drifting grating stimuli as well as natural movies.

The fact that neurons may have different tuning depending on the behavioral state of the animal raises obvious questions about readout. The authors show that neurons with strong behavioral shifts should simply be ignored and that this can be achieved if the downstream decoder weights inputs with more stimulus information. While questions remain about why behavior shifts representations and how that could be more effectively utilized by downstream circuits, the results presented clearly show that sensory representations might not always be simply drifting over time, and will spark some careful analysis of past and future experimental results.

Many thanks for a clear summary of the work and emphasizing the significance of the results.

Reviewer 2

Studies from recent years have shown that neuronal responses to the same stimuli or behavior can gradually change with time - a phenomenon known as representational drift. Other recent studies have shown that changes in behavior can also modulate neuronal responses to a given sensory stimulus. In this manuscript, Sadeh and Clopath analyzed publicly available data from the Allen Institute to examine the relationship between animal behavioral variability and changes in neuronal representations. The paper is timely and certainly has the potential to be of interest to neuroscientists working in different fields. However, there are currently several important issues with the analysis of the data and their interpretations that the authors should address. We believe that after these concerns are addressed, this study will be an important contribution to the field.

We really appreciate the time and the effort the reviewer(s) have taken to evaluate our results and analysis in detail. Their comments are very relevant and critical to the improvement of the manuscript. We explain below how we addressed their various comments and concerns

1. The manuscript raises a potential problem: while previous work suggested that the passage of time leads to gradual changes in neuronal responses, the causality structure is different: i.e., the passage of time leads to gradual changes in behavior, which in turn lead to gradual changes in neuronal responses. The authors conclude that "variable behavioral signal might be misinterpreted as representational drift". While this may be true, in its current form, the paper lacks critical analyses that would support such a claim. It is possible that both factors - time and behavior - have a unique contribution to changes in neuronal responses, or that only time elicits changes in neuronal responses (and behavior is just correlated with time). Thus, the authors should demonstrate that these changes cannot be explained solely by the passage of time and elucidate the unique contributions of behavior (and elapsed time) to changes in representations.

This is a very important point and we addressed it with new analyses, by dedicating a new figure (Figure 1–figure supplement 5) and a new part of the Results section to it. The results of our new analyses show that strong representational drift mainly exists in those animals/sessions with large behavioral changes between the two blocks, and that in animals/sessions with small behavioral changes, such drift is minimal, despite the passage of time (see our responses below to Major comments for further details).

1. There are also several issues with the analysis of the data and the presentation of the results. The most concerning of which is that the data shows a non-linear (and non-monotonic) relationship between behavioral changes and representational similarity. In many of the presented cases, the data points fall into two or more discrete clusters. This can lead to the false impression that there is a monotonic relationship between the two variables, even though there is no (or even opposite) relationship within each cluster. This is a crucial point since the clusters of data points most likely represent different blocks that were separated in time (or separation between within-block and acrossblock comparisons).

This is an important concern. To address this, we analyzed the source of the non-monotonic relationship / opposite trend in the data and demonstrated the results in a new figure (Figure 4–figure supplement 2). Our results show that the non-monotonic relationship does not compromise the result of our previous analysis. Furthermore, it suggests that the non-monotonic / opposite trend is emerging as a result of more complex interactions between different aspects of behavior. We have also shown, in separate analyses, that the passage of time is not the main contributing factor to representational drift, rather large behavioral changes are correlated with strong drifts between the two blocks of presentation (Figure 1—figure supplement 5, and Figure 3—figure supplement 2).

More generally, we did not intend to claim that the relationship with behavioral changes is linear or/and monotonic. We used linear analysis just to show the main trend of decrease in representational similarity with large behavioral changes. Any other analysis should assume some form of nonlinearity, but because the nonlinear relationships between behavior and activity were complex, it was not easy to assume such nonlinearity.

We in fact tried to use two other ways of analysis, nonlinear correlations and generalized linear models (GLM), but there were issues hindering a proper use of each analysis. Nonlinear correlations assume a specific type of nonlinearity, but the nature of nonlinearity underlying the data is not clear (in fact, it looks to be different in different example non-monotonic trends in the data). We could not, therefore, assume a nonlinearity that best fitted all the data; we believe the nature of this nonlinearity, or how behavior modulates neuronal activity in a nonlinear manner, is in itself an interesting and open question for future investigation, but beyond the scope of this study. GLM did not provide useful results either, as the relationship between behavioral changes and neural activity/representational similarity was state-dependent and transitioning between nonlinear states, therefore hindering the usage of linear methods.

We therefore opted for the simplest analysis which can show and quantify this dependence - emphasizing that further analyses are in fact needed to get to the bottom of the exact nonlinear relationship (for further details, see the responses below to Major comments).

1. The authors also suggest that using measures of coding stability such as 'population-vector correlations' may be problematic for quantifying representational drift because it could be influenced by changes in the neuronal activity rates, which may be unrelated to the stimulus. We agree that it is important to carefully dissociate between the effects of behavior on changes in neuronal activity that are stimulus-dependent or independent, but we feel that the criticism raised by the authors ignores the findings of multiple previous papers, which (1) did not purely attribute the observed changes to the sensory component, and (2) did dissociate between stimulus-dependent changes (in the cells' tuning) and off-context/stimulus-independent changes (in the cells' activity rates).

That’s a very valid point. As population vector correlations are used quite often in (experimental and theoretical) works on representational drift, we wanted to highlight the pitfalls of such a metric in dissociating between sensory-evoked and sensory-independent components. However, as the reviewers have mentioned, these two aspects have been separated and addressed independently in some of the past literature in the field. For instance, as we discussed in the Discussion, Deitch et al. (Current Biology, 2021) have calculated this for different metrics, including tuning curve correlations, which can potentially alleviate this problem:

“A recent analysis of similar datasets from the Allen Brain Observatory reported similar levels of representational drift within a day and over several days5. The study showed that tuning curve correlations between different repeats of the natural movies were much lower than population vector and ensemble rate correlations5; it would be interesting to see if, and to which extent, similarity of population vectors due to behavioural signal that we observed here may contribute to this difference.”

We tried to highlight these contributions better in the revised manuscript (see further on this below in our responses to Major comments).

1. Another important issue relates to the interchangeable use of the terms 'representational drift' and 'representational similarity'. Representational similarity is a measure to identify changes in representations, and drift is one such change. This may confuse the reader and lead to the misconception that all changes in neuronal responses are representational drift.

We thank the reviewer(s) for raising this point. We have clarified our use of the terms representational similarity and representational drift in the revised manuscript. Specifically, we have quantified representational drift index between the two blocks according to a previously used metric (RDI; Marks & Goard, 2021) in our new analysis (Figure 1–figure supplement 5).

For the main part of the paper, however, we have decided to base our analysis on representational similarity (RS), and to evaluate the drop of RS with changes in behavior. Our reasoning for this is twofold. First, any measure of representational drift should ultimately be a function of the representational similarity. The measure we used above, for instance, is calculated as RD = (RS_ws - RS_bs)/(RS_ws + RS_bs) (Marks and Goddard, 2021), with RS_ws and RS_bs referring to the average representational similarity within a session or between different sessions. However, RS contains more information, especially with regard to fine-tuned changes - the above metric, for instance, averages all the changes within each block of presentation. By focusing on the basic function of representational similarity, we could capture both the gross changes between the blocks as well as more nuanced changes that can arise within them, especially with regard to behavioral changes. Another aspect that would have been lost by only using the usual metric of representational drift is the direction of change. In our analysis, we in fact found that the average RS increased within the second block of presentation, which might be contrary to the usual direction of drift. We found this unconventional change of RS interesting and informative too. We could highlight that, presenting the raw RS provided a better analysis strategy. Based on these reasons, we think representational similarity would be a better metric to base our analyses upon, although we have now calculated a conventional representational drift index for comparison too.

Reviewer 3

Although it is increasingly realized that cortical neural representations are inherently unstable, the meaning of such "drift" can be difficult or impossible to interpret without knowing how the representations are being read out and used by the nervous system (i.e. how it contributes to what the experimental animal is actually doing now or in the future). Previous studies of representational drift have either ignored or explicitly rejected the contribution of what the animal is doing, mostly due to a lack of high-dimensional behavioural data. Here the authors use perhaps the most extensive opensource and rigorous neural data available to take a more detailed look at how behaviour affects cortical neural representations as they change over repeated presentations of the same visual stimuli.

The authors apply a variety of analyses to the same two datasets, all of which convincingly point to behavioural measures having a large impact on changing neural representations. They also pit models against each other to address how behavioural and stimulus signals combine to influence representations, whether independently or through behaviour influencing the gain of stimuli. One analysis uses subsets of neurons to decode the stimulus, and the independent model correctly predicts the subset to use for better decoding. However, one caveat may be that the nervous system does not need to decode the stimulus from the cortex independently of behaviour; if necessary, this could be done elsewhere in the nervous system with a parallel stream of visual information.

Overall the authors' claims are well-supported and this study should lead to a re-assessment of the concept of "representational drift". Nonetheless, a weakness of all analyses presented here is that they are all based on data in head-fixed mice that were passively viewing visual stimuli, such that it is unclear what relevance the behaviour has. Furthermore, the behavioural measurements available in the opensource dataset (pupil movements and running speed) are still a very low dimensional representation of what the mice were actually doing (e.g. detailed kinematics of all body movements and autonomic outputs). Thus, although the authors here as well as other large-scale neural recording studies in the past decade or so make it clear that relatively basic measures of behaviour can dramatically affect cortical representations of the outside world, the extent to which any cortical coding might be considered purely sensory remains an important question. Moreover, it is possible that lowerdimensional signals are overly represented in visual areas, and that in other areas of the cortex (e.g. somatosensory for proprioception), the line between behaviour parameters and sensory processing is blurred.

Many thanks for the clear and insightful summary of the results, significance and caveats of our analysis. We totally agree with this critical evaluation - and suggestions for future work.

Author Response

Reviewer 2

In the manuscript, the cellular deformation that is due to the shear stress generated in a classical microfluidic channel is used to deform detached cells that are moving in the flow. A very elegant point of the paper is that the same cells are used in the provided software to determine the fluid flow, which is a key parameter of the method. This is particularly important, as an independent way to crosscheck the fluid flow with the expected values is important for the reliability of the method. Instead of complicated shape analysis that are required in other microfluidic methods, here the authors simply use the elongation of the cell and the orientation angle with respect to the fluid flow direction. The nice thing here is that a well-known theory from R. Roscoe can be successfully used to relate these quantities to the viscoelastic shear modulus. Thanks to the knowledge of the fluid flow profile, the mechanical properties can be related to the tank treading frequency of the cells, which in turn depends on the position in the channel, and the flow speed. Hence, after knowing the flow profile, which can be determined with a sufficiently fast camera, and the actual static cell shape, it is possible to obtain frequency dependent information. Assuming then that cells do have a statistically accessible mean viscoelastic property, the massive and quick data acquisition can be used to get the shear modulus over a large span of frequencies.

The very impressive strength of the paper is that it opens the door for basically any, non-specialized cell biology lab to perform measurements of the viscoelastic properties of typically used cell types in solution. This allows to include global mechanical properties in any future analysis and I am convinced that this method can become a main tool for a rapid viscoelastic characterization of cell types and cell treatment.

Although it is both elegant and versatile, there remain a couple of important questions open to be further studied before the method is as reliable as it is suggested by the authors. A main problem is that the model and the data simply don't really work together. This is most prominent in Figure 3a. This is explained by the authors as a result of non-linear stress stiffening. Surely this is a possible explanation, but the fact that the question is not fully answered in the paper makes the whole method seems not sufficiently backed. I agree that the test with the elastic beads are beautiful, but also here the results obtained with the microfluidic method and the AFM seem not to match sufficiently to simply use the proposed model in conjecture with a single power law approach to fully translate the single frequency data into a frequency dependent plot. There are more and more hints that two power law models are more reasonable to describe cell mechanics. If true this would abolish the approach to exploit only a single image to get the mechanical power law exponent and the prefactor in a single image. Despite all the excitement about the method, I have the feeling that the used models are stretched to their extreme, and the fact that the only real crosscheck (figure 3a) does not work for the power law exponent undermines this impression.

We had assumed that the probing frequency equals the tank treading frequency. This is incorrect. As the cell undergoes a full rotation, any given volume element inside the cell is compressed twice and elongated twice. Hence, the frequency with which the cell is probed is twice the tank-treading frequency. This correction shifts the G’ and G” versus frequency curves to the right (by a factor of two), and in addition, the G” data points are shifted (increased) by a factor of two (Eq. 17). This also increases the fluidity alpha (and hence the slope of the power-law relationship) roughly by a factor of two (Eq. 22), and since the actual slope of the G’ and G” versus frequency data “cloud” is unchanged by the correction, the single power-law description now describes the data much better (see new Fig. 3a).

Regarding the critique that models are stretched to their extreme: The Roscoe model assumes that cells behave as the visco-elastic continuum-mechanics equivalent of a Kelvin-Voigt body consisting of an elastic spring in parallel with a resistive (or viscous) dash-pot element . This then gives rise to a complex shear modulus with storage modulus G’ and loss modulus G”, measured at twice the tank treading frequency 𝜔. Roscoe makes no assumptions whatsoever about how G’ and G” might change as a function of frequency. Hence, our “raw” G’ and G” data, e.g. in Fig. 3a, are obtained without any power law assumption.

One could leave it at that, as the reviewer suggests below, and only present the raw G’ and G” vs. frequency plots. However, this would also make it nearly impossible to compare our measurements to those obtained with other techniques that operate at different, non-overlapping time- or frequency-scales. For such a comparison to work, one needs a model to predict how G’ and G” scale with frequency.

A commonly used and very simple model to predict how G’ and G” scale with frequency, which is also the model used by Fregin et al. and many others, is that of a Kelvin-Voigt body consisting of an elastic spring in parallel with a resistive element (dash-pot), both with a frequency-independent stiffness and resistance (viscosity), respectively. However, our data show that G’ and G” of different cells, all measured at different tank-treading frequencies, exhibit a behavior that is very unlike that of a simple Kelvin-Voigt body with a constant, frequency-independent stiffness and resistance. In this case, G’ would be flat (power law exponent zero), and G” would increase proportional with frequency (power law exponent of unity). This is clearly not what our data show.

Rather, we find that G’ and G” increase with increasing frequency according to a power law, with the same exponent 𝛼 for G’ and G”. At high frequencies (beyond the range of our microfluidic method, but in the range of our AFM measurements), G” increases more strongly with frequency, akin to a Newtonian viscosity (power law exponent of unity), which we take into account in the case of the AFM measurements. A large number of publications have shown that many types of cells, including cells in suspension, follow power law rheology, regardless of the measurement method. Also the AFM measurements that we include in this study support the validity of power-law rheology.

Power law rheology predicts a peculiar behavior: The ratio of G”/G’ in the low-frequency regime (where the high-frequency viscous term is not yet dominating) must be equal to tan(𝛼𝜋/2), for mathematical reasons (Eq. 22). With our correction (that the probing frequency is twice the tank-treading frequency), we find that Eq. 22 correctly predicts the power-law exponent of the G’ and G” vs. frequency data.

Note that we actually do not fit a power law model (Eq. 1) to the population data of G’ and G” vs. frequency in Fig. 3a. The G’ and G” data are obtained by applying Roscoe-theory, without any further assumptions such as power-law rheology. Only the lines shown in Fig. 3a that go nicely through the data are a prediction of how a typical cell (selected from the mode of the joint probability density of alpha and k, see Fig. 3b) would behave if we had measured it at different frequencies, under the assumption that this cell follows power law rheology, based on Eq. 22. With this assumption, we can directly convert the measured G’ and G” of any cell into a stiffness k and power law exponent 𝛼 using Eqs. 21 and 22 - no fit is needed here.

Since we only measure two parameters for any given cell at twice its tank-treading frequency, namely strain and alignment angle, we can only extract two parameters for each cell (i.e., G’ and G”, or k and alpha) but not a third parameter. In essence, the reviewer expresses concerns that the G' and G" behavior of a typical cell, when extrapolated to higher or lower frequencies, may not necessarily match the frequency behavior of the entire cell population (Fig. 3a). However, our data show that a single (typical) cell that was measured at a single mid-range frequency comes remarkably close to describing the G’ and G” versus frequency behavior of all other cells.

The reviewer suggests that a power law model with two exponents may be able to even more accurately describe the mechanics of the cell population. This is certainly correct, and in particular when cell mechanics is measured over a larger range of frequencies or strain rates, as we have done here using AFM, we find that at higher frequencies, G” deviates from a weak power law and merges into a different power law with a larger slope (i.e., power law exponent) that approaches unity or a value close to unity, akin to a Newtonian viscous term. Therefore, the single power law expression (Eq. 1) is not sufficient for the AFM data, and we use Eq. 2 instead. However, in the case of our shear stress cytometry measurements, the tank-treading frequency remains below the range where this second power law behavior becomes prominent. Therefore, the Newtonian viscosity term of Eq. 2 cannot be fitted with reasonable fidelity to the data from a single measurement.

In the case of polyacrylamide beads, we start to see a hint of an upward trend in G” versus frequency at tank-treading frequencies of around 10 Hz, and therefore have performed a global fit with Eq. 2 to the shear flow data where we keep the Newtonian viscous term constant for all conditions (different shear stresses and bead stiffnesses).

The reviewer furthermore cautioned that mechanical non-linearities such as strain stiffening may distort or otherwise bias the results. As the reviewer brings up this issue in more detail below, we have addressed it there.

Regarding the concern that “results obtained with the microfluidic method and the AFM seem not to match sufficiently to simply use the proposed model in conjecture with a single power law approach to fully translate the single frequency data into a frequency dependent plot.”:

First, we tend to agree more with the opinion of Reviewer #1 who found it remarkable that results obtained with the microfluidic method and the AFM method are actually fairly similar. Now that we have introduced the correction that the probing frequency is twice the tank-treading frequency, the cells in suspension turn out to be softer and more fluid-like compared to the cells measured with AFM. But there are many more commonalities between the AFM data and the shear flow data, which we list above in our reply to reviewer #1, the most relevant here is that cells show power-law behavior both when measured with AFM and with our new method.

Second, we did not use a single power law to fit the AFM data. Rather, we used Eq. 2, which contains two power law relationships (the second power law exponent of unity for the Newtonian viscosity therm is usually not explicitly written). However, the origin of the Newtonian viscosity therm arises mainly from the hydrodynamic drag of the cantilever with the surrounding liquid, and less so from the cells. This hydrodynamic drag is absent in our shear flow deformation cytometry method, and moreover the tank treading frequency of most cells remains far below 10 Hz where an additional Newtonian viscosity therm does not yet come into play.

Third, we disagree that Fig. 3a is “the only real crosscheck for the power law exponent”. The inverse relation that we see between the power law exponent and the stiffness of individual cells (Fig. 3b) has been previously reported for different cell types and methods. Moreover, we find a power law exponent close to zero for PAA beads at small strain values, which is to be expected for a predominantly elastic material such as PAA. We think that this last result is a particularly convincing experimental cross-check.

Author Response

Reviewer 2

In this manuscript, Gao et al claim that they have constructed a gene regulatory network underlying alveologenesis and its significance to bronchopulmonary dysplasia (BPD). Using RTPCR and in situ hybridization, the authors claim that Igf1 and Igf1r are expressed in secondary crest myofibroblasts (SCMFs) and their loss of function using Gli1-creER results in alveolar simplification, a tissue level disorganization of alveoli that phenocopies BPD. Further, the authors investigate transcriptomic changes in mesenchymal and epithelial populations from control and Igf1r mutant lungs. For this, the authors developed a 47-gene panel that they claim to represent signaling modules within SCMFs and used this panel for RT-PCR analysis. These data are used to generate an interaction network to evaluate signaling partners, co-effectors mediated by IGF1 signaling in SCMFs, other fibroblasts and alveolar epithelial cells. Using this GRN, the authors concluded that Wnt5a is a key signaling molecule downstream of IGF1 signaling that regulates alveologenesis.

While the authors' claims are salient, some of the conclusions were previously shown by others. For example, a role for Wnt5a driven Ror/Vangl2 has already been shown to be a key mediator of alveologenesis, by virtue of the same signaling effectors identified in this study (Zhang 2020 eLife).

Response: For the network construction, we not only used our own data, but also considered perturbation analyses and gene regulation data contributed from the work reported by others in the lung research community. The goal was to decipher the genetic regulations among these genes, connect them together, and build the GRN so the lung research community can employ it as a tool to study lung development and its disease in a network-type context.

We are aware of the excellent study by Zhang et al. 2020 and appreciate their findings related to WNT5a/Ror/Vangl2 functions in lung development. With due respect, we would like to point out that Zhang and colleagues inactivated WNT5a by Tbx4Cre which is highly expressed during the embryonic stage (i.e. Cebra-Thomas et al., 2003). This approach cannot exclude the indirect effects of the mutation that originate during the embryonic phase, on alveologenesis, which is an entirely postnatal process. In contrast, our study used a conditional CreER model to inactivate WNT5a specifically during alveologenesis (i.e. PN2). More importantly, our work identified the upstream and downstream regulatory connections of this signaling pathway and further elucidated its role and function from the network ground.

Additionally, the genetic loss of function studies performed here are not specific to SCMFs and instead they target broader alveolar and airway fibroblasts.

Response: Please see our Response to General Comment #3 above for the specificity of Gli1 to SCMFs.

The construction of a gene regulatory network is a potentially exciting tool, but this requires additional perturbations to distinct nodes identified in this work. It would be of particular interest to determine whether there is any redundancy among these nodes and what are the downstream effectors that are specific to each node. While I recognize that this is outside the scope of this work, the authors need to demonstrate the significance of at least one such node.

Response: We agree with the general validity of the reviewer’s comment that much more can be done that is not in this first report of the alveologenesis GRN. There is always much more.

The reviewer has raised some critically important and interesting points. We appreciate the reviewer’s acknowledgement that these very key studies are not within the scope of what is presented in this initial report on GRN construction. Each of such studies will likely require a separate report. The content of the present manuscript was chosen with the goal of disseminating a highly cogent and focused set of data that introduces the utility of GRN in alveologenesis. As noted above by the Editors, this is a novel approach in “translating publicly available data into meaningful biological insights”. We hope this clarifies the main purpose of our study and this manuscript.

Author Response:

Reviewer #2 (Public Review):

The topic is interesting, the study addresses an important question, and the manuscript is fairly well written. However, in my opinion, there are a number of serious problems that need to be addressed - because there are many similar laboratory studies on this subject. In my opinion, the novelty of the main message (a neutrophil - B-cell axis governs disease tolerance during sepsis via Cxcr4) is limited. My explanation is as follows.

Firstly, human sepsis is defined (according to Sepsis 3 criteria) as life-threatening organ dysfunction caused by a dysregulated host response to infection (Singer et al. 2016) and in agreement with the Authors, despite considerable research efforts the pathophysiology is still unknown. Besides, the mechanisms underlying the signaling and trafficking of PMN leukocytes within the affected tissues, and the roles of adhesion molecules, including chemokine receptors are still not fully understood. Indeed, diverse therapies directed against these targets have shown dramatic effects in animal models; however, in humans, their clinical impact has been modest. There are many reasons for the discordance between biological promise and bedside reality, and one of them might be the use of animal models. Extrapolation from animal models always requires an awareness of species-related and other dependent variations and I would like to stress that this study employed mice, the Author has investigated the mechanisms involved in the PMN reactions in a mouse model of intraabdominal (O18:K1 E. Coli) bacterial infection, but this fact is not mentioned in the title or abstract (only in keywords) or introduction.

We thank the reviewer for this comment. We fully agree that the translational potential of many mouse studies is limited, but truly believe that there are conserved mechanisms between mouse and human which are worth being explored and reported. We certainly did not intend to hide that our study was performed in mice and have now clarified this by adapting the abstract as follows: “Here, we established a mouse model of long-lasting disease tolerance during severe sepsis, manifested by diminished immunothrombosis and organ damage in spite of a high pathogen burden.“ page 2, line 11

Secondly, according to the Authors they "established and investigated a model of disease tolerance during sepsis, which enabled them to reveal the importance of B cells and neutrophils in mediating tissue tolerance in the context of severe infections". Here it should be noted that 1. LPS administration to rodents does not mimic human sepsis, and 2. the mechanism of endotoxin tolerance (or preconditioning) has been studied for decades. It is characterized by a hyporesponsive state following low-dose stimulation with a TLR4 ligand (i.e. lipopolysaccharide). Besides, endotoxin tolerance provokes cross-tolerance against other forms of injuries as well such as liver ischemia-reperfusion (J Surg Res 57, 1994).

Ad 1. We thank the reviewer for this critical comment. While we fully agree on the fact that LPS administration does not mimic human sepsis, we are slightly puzzled by this criticism as we at no point say so in our manuscript. What we instead say is that E. coli peritonitis is a sepsis model, a claim that is widely accepted in the field.

We are explaining this in the intro: “In this study, we investigated mechanisms of disease tolerance and tissue damage control, by comparing tolerant and sensitive hosts during a severe bacterial infection. While sensitive animals developed severe coagulopathy and tissue damage during sepsis, tolerant animals were able to maintain tissue integrity in spite of a high bacterial load. Disease tolerance was induced by the prior exposure of animals to a single, low-dose of LPS and could be uncoupled from LPS-induced suppression of cytokine responses.” page 3, line 32-34, page 4, line 1-3

…as well as in the result section: “We thus challenged mice intravenously (i.v.) with a subclinical dose of LPS 1 day, 2 weeks, 5 weeks or 8 weeks, respectively, prior to the induction of Gram-negative sepsis by intraperitoneal (i.p.) injection of the virulent E. coli strain O18:K1.” page 5, line 7-9

… and in our methods section, which we have adapted to make this point even more clear to the reader: Tolerance was induced by i.v. injection of 30μg E. coli LPS (Sigma-Aldrich) at indicated times before induction of bacterial sepsis by intraperitoneal (i.p.) infection with 1-2x104 E. coli O18:K1. E. coli peritonitis was induced as described previously (Knapp, de Vos et al. 2003, Knapp, Matt et al. 2007, Gawish, Martins et al. 2015). page 24, line 13-15

Ad 2. We agree that LPS- or endotoxin tolerance is an old topic which has been studied for a long time. However, as we explain in detail in our response to the editor, the contribution of “LPS tolerance” to “disease tolerance” is still under investigation. As explained extensively above (please refer to our response to the editor), we observe signs of LPS tolerance in our experimental setup, as LPS pre-exposed mice produce lower levels of inflammatory cytokines shortly after infection. However, our data collectively suggest, that reduced early cytokine production (most likely a sign of LPS tolerance) is not the reason for improved tissue damage control in LPS-pre-treated mice. As such, we argue that the protective phenotype we observed is independent of early cytokine suppression and independent of monocytes and macrophages, hence not a result of LPS tolerance.

Thirdly, according to the Authors they considered the possibility that B cells regulate infection-induced neutrophil functionalities because “we discovered that LPS-induced protection was still observed in splenectomized animals”. Nevertheless, the role of spleen in endotoxin effects (or more correctly, that the absence of spleen) in the development of tolerance to endotoxin was demonstrated decades ago (and studied repeatedly by the group of Agarwal (Br J Exp Pathol 53 1972).

It seems that there has been a misunderstanding as we do not make this claim in our manuscript. To be precise the correct wording that we used in our manuscript is: “Since we discovered that LPS-induced protection was still observed in splenectomized animals, we considered the possibility that B cells regulate infection-induced neutrophil functionalities via effects exerted by sharing the same bone marrow niche. In fact, B cells, neutrophils and their precursors build up the majority of the constitutive CD45+ bone marrow cell pool, where they mature while sharing the same niche (Yang, Busche et al. 2013).“ page 19, line 17-21

This obviously has a different meaning. As we saw that LPS-induced tissue tolerance was abrogated in (full body) B cell deficient mice, our intention was not to study the effect of splenectomy on LPS-tolerance but to make use of splenectomy to narrow down the B cell compartment which is driving the protective effect. Of course, the role of the spleen during endotoxemia and during peritonitis has been studied before, but the point we wanted to make with our finding was that splenectomy, in contrast to a full B cell deficiency (in Rag2-/- or JHT-/- animals), did not abrogate LPS-induced tissue protection.

To address and clarify this point, we slightly modified our explanation in the results section and included some of these “old” splenectomy studies: “We then tested if splenectomy would replicate the protective effects of full B cell deficiency during sepsis and interestingly found that splenectomy was associated with reduced liver damage in naïve, sensitive mice, which is in line with other studies (Agarwal, Parant et al. 1972, Karanfilian, Spillert et al. 1983), but, in contrast to complete lymphocyte deficiency, not sufficient to abrogate LPS-induced tissue protection in tolerant animals (Figure 2G and S2F). This suggested that mature splenic B cells contributed to tissue damage during severe infections, while other, not spleen derived, B cell compartments were instrumental in driving disease tolerance.“ page 8, line 1-7

Next, according to the Authors, "it is tempting to speculate that B cells act as important regulators of granulopoiesis and neutrophil trafficking at steady state and under inflammatory conditions". Nevertheless, previous studies have established that neutrophil trafficking is regulated mainly via CXCR4 in steady state, and the attenuation of CXCR4 signaling leads to the entry of PMNs into the circulation from the bone marrow (JCI 120(7) 2010).

We believe that there is another misunderstanding. This comment suggests that an involvement of B cells in neutrophil regulation would be against already published knowledge about CXCR4 as a master regulator of neutrophil trafficking. This is not at all what we are claiming in our manuscript.

A potential involvement of B cells in neutrophil regulation is not in conflict with what is already known about the important role of CXCR4. As CXCR4 signaling is critical for both B cells AND neutrophils, competition for the CXCR4 ligand Cxcl12 (SDF1) and differences in the sensitivity to altered ligand availability might serve as an explanation.

We are actually discussing the role of CXCR4 in neutrophil trafficking extensively in the results section and in the discussion of our manuscript and have now slightly modified our wording and extended our discussion part to clarify this point:

“…neutrophil aging, a process that is counteracted by Cxcr4 signaling, the master regulator of neutrophil trafficking between the bone marrow and the periphery (Martin, Burdon et al. 2003, Eash, Greenbaum et al. 2010, Adrover, Del Fresno et al. 2019).” page 13, line 7-9

“Considering the reported importance of Cxcr4 signaling in neutrophil retention in the bone marrow and their release to the periphery (Martin, Burdon et al. 2003, Eash, Greenbaum et al. 2010, Adrover, Del Fresno et al. 2019),…“ page 15, line 1-2

“Cxcr4 interaction with its ligand Cxcl12 (stromal cell-derived factor 1, SDF1) has been shown to be critical for the retention of neutrophils in the bone marrow under steady state, their release to the periphery as well as their homing back to the bone marrow when they become senescent (Martin, Burdon et al. 2003, Eash, Greenbaum et al. 2010). Importantly, Cxcr4 signaling is essential, as Cxcr4 knockout mice die perinatally due to severe developmental defects ranging from virtually absent myelopoiesis and impaired B lymphopoiesis to abnormal brain development (Ma, Jones et al. 1998). A different sensitivity to changes in SDF1 concentrations as a potential mechanism of the reciprocal regulation of lymphopoiesis and granulopoiesis has been suggested earlier (Ueda, Kondo et al. 2005).“ page 19, line 33-34, page 20, line 1-7

Furthermore, selective inhibition of CXCR4 by AMD3100 is protective in many injury models, including mice with fecal peritonitis (Front. Immunol 2020 | https://doi.org/10.3389/fimmu.2020.00407).

We thank the reviewer for pointing this out. In the above cited paper injection of AMD3100 blocks neutrophil migration into the peritoneal cavity as well as into the tissue during zymosan- or fecal slurry-induced peritonitis. Interestingly, we do not see any benefit of Cxcr4 inhibition (using AMD3100) in our model, but in contrast observed tissue protection by administration of the Cxcr4 agonist ATI2341 (Figure 5F). This can be explained by a different timing (and maybe also route) of administration. In the aforementioned study, AMD3100 is injected intraperitoneally, 1h BEFORE induction of peritonitis. AMD3100 injection is known to cause an immediate release of neutrophils from the bone marrow to the blood (Liu, Li et al. 2015), which means that in this experimental setup, neutrophils are already in the circulation prior the injection of zymosan or fecal slurry. Our experimental setup in contrast uses a therapeutic approach, as we inject AMD3100 or ATI2341 just 6h post induction of E. coli peritonitis. At 6h post infection, E. coli infection has already caused a massive increase in blood neutrophils and infiltration of neutrophils into the peritoneum and various organs. We thus believe that these experimental setups are not truly comparable, but agree with the reviewer that this needs to be addressed in our manuscript.

We have now added the following paragraph to the discussion to address this study:

“Given its clinical importance, Cxcr4 inhibition (using AMD3100) has been studied in different injury models, but interestingly only little is known about the therapeutic impact of Cxcr4 activation. Strikingly, activating, but not antagonizing, Cxcr4 during sepsis promoted tissue damage control in our model, which is in conflict with a study showing that Cxcr4 blockade with AMD3100 prior induction of peritonitis prevents neutrophil infiltration and tissue inflammation (Ngamsri, Jans et al. 2020). While we only see a tissue protective effect of ATI2341, but not AMD3100, we believe that this is due to differences in the timing and maybe also the route of drug administration. As we use a therapeutic approach and target Cxcr4 as late as 6h post E. coli injection, a time when there is already substantial neutrophilia in blood and organs, our data support an impact of Cxcr4 signaling on neutrophils’ tissue damaging properties and suggest that B cell driven regulation of Cxcr4 is a potential mechanism of disease tolerance and thus might be an interesting therapeutic target during severe sepsis.“ page 20, line 12-23

Lastly, it has been previously recorded that Rag1 animals had a higher death rate to CLP than wild type animals and that this could be ameliorated by adaptive transfer of syngeneic T cells induced to overexpress the anti-apoptotic molecule Bcl-2 by gene transfer techniques (Hotchkiss, Crit Care Med 1997)

We thank the reviewer for this comment. We are aware of the fact that the role of lymphocytes in different experimental models of peritonitis-induced sepsis has been studied before. However, the contribution of different lymphocyte populations remains controversial, likely due to different experimental setups and methodologies used in different studies. While we do not really see the connection of lymphocyte apoptosis to our study, we want to point out that the study, which is mentioned by the reviewer does not report a higher death rate of Rag1-/- animals, but shows that there is substantial lymphocyte apoptosis during sepsis (Hotchkiss, Swanson et al. 1997). We believe that the study which the reviewer refers to is from 1999 and has been published in the Journal of Immunology (Hotchkiss, Swanson et al. 1999).

However, as lymphocyte apoptosis is not connected to the topic of our study, we chose to discuss our data in the context of more B cell specific literature and have cited another important CLP study which showed that IFN-activated B cells are critical for survival by promoting early inflammation and neutrophil effector functions during CLP which in turn improves bacterial clearance (Kelly-Scumpia, Scumpia et al. 2011). In this setup, the increased mortality of Rag1-/- animals during CLP is likely a result of an increased pathogen load and therefore not in conflict with our data. While we appreciate that CLP is the more physiologic model, the strength of our E. coli sepsis model is that bacterial outgrowth already occurs at a maximum speed and is not further enhanced by the absence of certain immune cell types which is why we can uncouple immunopathologic effects from the pathogen load.

We mention this study in our result section: “Given that B cells were shown to promote early production of proinflammatory cytokines such as IL-6 during sepsis in a type I IFN dependent manner …“ page 8, line 8-9

We have further added a paragraph to our discussion to better explain the differences between CLP and the model we have used for this study: “It was demonstrated earlier that mature, splenic B2 cells promote neutrophil activation by boosting type-I IFN dependent early inflammation, which in turn improves bacterial clearance and survival during CLP (Kelly-Scumpia, Scumpia et al. 2011). While enhanced inflammation can mediate pathogen clearance during CLP, it at the same time contributes to tissue damage which is of particular importance in our model. In support of proinflammatory, tissue-damaging properties of mature B2 cell subsets, we found splenectomy similarly protective as B cell deficiency during primary sepsis and reconstitution of Rag2-/- mice with B cells to increase tissue damage. Interestingly, we did not identify an important role for the proposed IFNAR-driven inflammatory function of B cells (Kelly-Scumpia, Scumpia et al. 2011) in sepsis, and inflammation did not differ between wild type and lymphocyte deficient mice. “ page 18, line 29-34, page 19, line 1-5

Therefore, until this point, I consider the work largely repetitive and suggest to downgrade the wording a bit due to the lack of novelty. The paper confirms these previous observations in a partially new context, which is the demonstration of a crosstalk between PMNs and B cells in the bone marrow, in which B cells influence PMN trafficking likely by modulating Cxcr4 related pathways. We have highlighted the novelties of our study in this response letter and our revised manuscript, and hope the reviewer agrees with us that this improved the clarity and better explains the novelties.

Author Response:

Reviewer #3 (Public Review):

The main goals of this study by Guan, Aflalo and colleagues were to examine the encoding scheme of populations of neurons in the posterior parietal cortex (PPC) of a person with paralysis while she attempted individual finger movements as part of a brain-computer interface task (BCI). They used these data to answer several questions: 1) Could they decode attempted finger movements from these data (building on this group's prior work decoding a variety of movements, including arm movements, from PPC)? 2) Is there evidence that the encoding scheme for these movements is similar to that of able-bodied individuals, which would argue that even after paralysis, this area is not reorganized and that the motor representations remain more or less stable after the injury? 3) Related to #2: is there beneficial remapping, such that neural correlates of attempted movements change to improve BCI performance over time? 4) Can looking at the interrelationship between different fingers' population firing rate patterns (one aspect of the encoding scheme) indicate whether the representation structure is similar to the statistics of natural finger use, a somatotopic organization (how close the fingers are to each other), or be uniformly different from one another (which would be advantageous for the BCI and connects to question #3)? Furthermore, does the best fit amongst these choices to the data change over the course of a movement, indicating a time-varying neural encoding structure or multiple overlapping processes? The study is well-conducted and uses sound analysis methods, and is able to contribute some new knowledge related to all of the above questions. These are rare and precious data, given the relatively few people implanted with multielectrode arrays like the Utah arrays used in this study. Even more so when considering that to this reviewer's knowledge, no other group is recording from PPC, and this manuscript thus is the first look at the attempted finger moving encoding scheme in this part of human cortex .

An important caveat is that the representational similarity analysis (RDA) method and resulting representational dissimilarity matrix (RDM) that is the workhorse analysis/metric throughout the study is capturing a fairly specific question: which pairs of finger movements' neural correlates are more/less similar, and how does that pattern across the pairings compare to other datasets. There are other questions that one could ask with these data (and perhaps this group will in subsequent studies), which will provide additional information about the encoding; for example, how well does the population activity correlate with the kinematics, kinetics, and predicted sensory feedback that would accompany such movements in an able-bodied person?

What this study shows is that the RDMs from these PPC Utah array data are most similar to motor cortical RDMs based on a prior fMRI study. It's innovative to compare effectors' representational similarity across different recording modalities, but this apparent similarity should be interpreted in light of several limitations: 1) the vastly different spatial scales (voxels spanning cm that average activity of millions of neurons each versus a few mm of cortex with sparse sampling of individual neurons, 2) the vastly different temporal scales (firing rates versus blood flow), 3) that dramatically different encoding schemes and dynamics could still result in the same RDMs. As currently written, the study does not adequately caveat the relatively superficial and narrow similarity being made between these data and the prior Ejaz et al (2015) sensorimotor cortex fMRI results before except for (some) exposition in the Discussion.

We agree that vastly different spatiotemporal scales (comments 1 and 2) limit the chances of finding correspondence between fMRI and single-neuron recordings. We have added motivation for our comparisons to the Results and Discussion sections.

Revised text in the Results: “We note that our able-bodied model was recorded from human PC-IP using fMRI, which measures fundamentally different features (millimeter-scale blood oxygenation) than microelectrode arrays (sparse sampling of single neurons).”

Revised text in the Discussion: “This match was surprising because single-neuron and fMRI recordings differ fundamentally; single-neuron recordings sparsely sample 102 neurons in a small region, while fMRI samples 104 – 106 neurons/voxel (Guest and Love, 2017; Kriegeskorte and Diedrichsen, 2016). The correspondence suggested that RSA might identify modality-invariant neural organizations (Kriegeskorte et al., 2008b), so here we used fMRI recordings of human PC-IP as an able-bodied model.” “This result does obscure a straightforward interpretation of the RSA results – why does our recording area match MC better than the corresponding implant location? Several factors might contribute, including differing neurovascular sensitivity to the early and late dynamic phases of the neural response (Figure 4e), heterogeneous neural organizations across the single-neuron and voxel spatial scales (Arbuckle et al., 2020; Guest and Love, 2017; Kriegeskorte and Diedrichsen, 2016), or mismatches in functional anatomy between participant NS and standard atlases (Eickhoff et al., 2018).”

…3) that dramatically different encoding schemes and dynamics could still result in the same RDMs…

Regarding point 3, we agree that RSA provides a second-order correspondence (Kriegeskorte et al., 2008a) rather than direct neuron-to-neuron comparisons. To supplement RSA, we also provide more detail on single-neuron responses for the reader in Figure 1–figure supplement 5. However, we believe that population metrics helpfully summarize the computational strategies of recorded brain regions (Cunningham and Yu, 2014; Saxena and Cunningham, 2019), so we focus on population comparisons here.

Relatedly, the study would benefit from additional explanation for why the comparison is being made to able-bodied fMRI data, rather than similar intracortical neural recordings made in homologous areas of non-human primates (NHPs), which have been traditionally used as an animal model for vision-guided forelimb reaching. This group has an illustrious history of such macaque studies, which makes this omission more surprising.

We agree that similar intracortical recordings from homologous areas of NHPs would be useful to construct an able-bodied model. While our lab has historically studied NHP reaching and grasping, we unfortunately did not perform any analogous experiments involving individuated finger movements. We have updated the Discussion to clarify this.

Revised text in the Discussion: “We asked whether participant NS’s BCI finger representations resembled that of able-bodied individuals or whether her finger representations had reorganized after paralysis. Single-neuron recordings of PC-IP during individuated finger movements are not available in either able-bodied human participants or non-human primates. However, many fMRI studies have characterized finger representations (Ejaz et al., 2015; Kikkert et al., 2021, 2016; Yousry et al., 1997), and representational similarity analysis (RSA) has previously shown RDM correspondence between fMRI and single-neuron recordings of another cortical region (inferior temporal cortex) (Kriegeskorte et al., 2008b).”

A second area in which the manuscript in its current form could better set the context for its reader is in how it introduces their motivating question of "do paralyzed BCI users need to learn a fundamentally new skillset, or can they leverage their pre-injury motor repertoire". Until the Discussion, there is almost no mention of the many previous human BCI studies where high performance movement decoding was possible based on asking participants to attempt to make arm or hand movements (to just list a small number of the many such studies: Hochberg et al 2006 and 2012, Collinger et al 2013, Gilja et al 2015, Bouton et al 2016, Ajiboye, Willett et al 2017; Brandman et al 2018; Willett et al 2020; Flesher et al 2021). This is important; while most of these past studies examined motor (and somatosensory) cortex and not PPC (though this group's prior Aflalo, Kellis et al 2015 study did!), they all did show that motor representations remain at least distinct enough between movements to allow for decoding; were qualitatively similar to the able-bodied animal studies upon which that body of work was build; and could be readily engaged by the user just by attempting/imagining a movement. Thus, there was a very strong expectation going into this present study that the result would be that there would be a resemblance to able-bodied motor representational similarity. While explicitly making this connection is a meaningful contribution to the literature by the present study (and so is comparing it to different areas' representational similarity), care should be taken not to overstate the novelty of retained motor encoding schemes in people with paralysis, given the extensive prior work.

We agree that multiple previous BCI studies instruct participants to attempt arm/hand movements and that these studies are important to discuss. We have updated the Introduction/Discussion to include these references.

Our work does fill in two important gaps in the existing literature. First, prior BCI studies had shown general resemblance between able-bodied and BCI movement, but previous human BCI studies had not shown whether the details of pre-injury representations are preserved. We have also updated the manuscript to describe a second motivation: that outside of the BCI community, neuroscientists do not agree on whether BCI studies of tetraplegic humans generalize to able-bodied movement, given the potential for reorganization after severe injury. In the Discussion sections of several recent BCI studies (Armenta Salas et al., 2018; Fifer et al., 2021; Flesher et al., 2016; Stavisky et al., 2019; Willett et al., 2020), the authors addressed whether the newly discovered phenomena were simply artifacts of reorganization (we believe not).

Revised text in the Introduction: Understanding plasticity is necessary to develop brain-computer interfaces (BCIs) that can restore sensorimotor function to paralyzed individuals(Orsborn et al., 2014). First, paralysis disrupts movement and blocks somatosensory inputs to motor areas, which could cause neural reorganization (Jain et al., 2008; Kambi et al., 2014; Pons et al., 1991). Second, BCIs bypass supporting cortical, subcortical, and spinal circuits, fundamentally altering how the cortex affects movement. Do these changes require paralyzed BCI users to learn fundamentally new motor skills (Sadtler et al., 2014), or do paralyzed participants use a preserved, pre-injury motor repertoire (Hwang et al., 2013)? Several paralyzed participants have been able to control BCI cursors by attempting arm or hand movements (Ajiboye et al., 2017; Bouton et al., 2016; Brandman et al., 2018; Collinger et al., 2013; Gilja et al., 2015; Hochberg et al., 2012, 2006), hinting that motor representations could remain stable after paralysis. However, the nervous system’s capacity for reorganization (Jain et al., 2008; Kambi et al., 2014; Kikkert et al., 2021; Pons et al., 1991) still leaves many BCI studies speculating whether their findings in tetraplegic individuals also generalize to able-bodied individuals (Armenta Salas et al., 2018; Fifer et al., 2021; Flesher et al., 2016; Stavisky et al., 2019; Willett et al., 2020). A direct comparison, between BCI control and able-bodied neural control of movement, would help address questions about generalization.

In the revised Discussion, we further contextualize our study in the prior work. In particular, as BCI studies have made fundamental neuroscience discoveries, they have had to address whether their results generalize to able-bodied individuals. Direct comparisons between able-bodied movement and tetraplegic BCI movement, like our study, help to bridge this gap.

Revised text in the Discussion: Early human BCI studies (Collinger et al., 2013; Hochberg et al., 2006) recorded from the motor cortex and found that single-neuron directional tuning is qualitatively similar to that of able-bodied non-human primates (NHPs) (Georgopoulos et al., 1982; Hochberg et al., 2006). Many subsequent human BCI studies have also successfully replicated results from other classical NHP neurophysiology studies (Aflalo et al., 2015; Ajiboye et al., 2017; Bouton et al., 2016; Brandman et al., 2018; Collinger et al., 2013; Gilja et al., 2015; Hochberg et al., 2012), leading to the general heuristic that the sensorimotor cortex retains its major properties after spinal cord injury (Andersen and Aflalo, 2022). This heuristic further suggests that BCI studies of tetraplegic individuals should generalize to able-bodied individuals. However, this generalization hypothesis has so far lacked direct, quantitative comparisons between tetraplegic and able-bodied individuals. Thus, as human BCI studies expand beyond replicating results and begin to challenge conventional wisdom, neuroscientists have questioned whether cortical reorganization could influence these novel phenomena (see Discussions of (Andersen and Aflalo, 2022; Armenta Salas et al., 2018; Chivukula et al., 2021; Fifer et al., 2021; Flesher et al., 2016; Stavisky et al., 2019; Willett et al., 2020)). As an example of a novel discovery, a recent BCI study found that the hand knob of tetraplegic individuals is directionally tuned to movements of the entire body (Willett et al., 2020), challenging the traditional notion that primary somatosensory and motor subregions respond selectively to individual body parts (Penfield and Boldrey, 1937). Given the brain’s capacity for reorganization (Jain et al., 2008; Kambi et al., 2014), could these BCI results be specific to cortical remapping? Detailed comparisons with able-bodied individuals, as shown here, may help shed light on this question.

The final analyses in the manuscript are particularly interesting: they examine the representational structure as a function of a short sliding analysis window, which indicates that there is a more motoric representational structure at the start of the movement, followed by a more somatotopic structure. These analyses are a welcome expansion of the study scope to include the population dynamics, and provides clues as to the role of this activity / the computations this area is involved in throughout movement (e.g., the authors speculate the initial activity is an efference copy from motor cortex, and the later activity is a sensory-consequence model).

An interesting result in this study is that the participant did not improve performance at the task (and that the neural representations of each finger did not change to become more separable by the decoder). This was despite ample room for improvement (the performance was below 90% accuracy across 5 possible choices), at least not over 4,016 trials. The authors provide several possible explanations for this in the Discussion. Another possibility is that the nature of the task impeded learning because feedback was delayed until the end of the 1.5 second attempted movement period (at which time the participant was presented with text reporting which finger's movement was decoded). This is a very different discrete-and-delayed paradigm from the continuous control used in prior NHP BCI studies that showed motor learning (e.g., Sadtler et al 2014 and follow-ups; Vyas et al 2018 and follow-up; Ganguly & Carmena 2009 and follow-ups). It is possible that having continuous visual feedback about the BCI effector is more similar to the natural motor system (where there is consistent visual, as well as proprioceptive and somatosensory feedback about movements), and thus better engages motor adaptation/learning mechanisms.

We agree that different BCI paradigms could better engage motor adaptation and learning, although it is interesting that participant NSS did not improve her performance simply by attempting “natural” finger movements. To better caveat our findings, we have revised our manuscript as suggested.

Revised text in the Discussion: “The stability of finger representations here suggests that BCIs can benefit from the pre-existing, natural repertoire (Hwang et al., 2013), although learning can play an important role under different experimental constraints. In our study, the participant received only a delayed, discrete feedback signal after classification (Figure 1a). Because we were interested in understanding participant NS’s natural finger representation, we did not artificially perturb the BCI mapping. When given continuous feedback, however, participants in previous BCI studies could learn to adapt to within-manifold perturbations to the BCI mapping (Ganguly and Carmena, 2009; Sadtler et al., 2014; Sakellaridi et al., 2019; Vyas et al., 2018). BCI users can even slowly learn to generate off-manifold neural activity patterns when the BCI decoder perturbations were incremental (Oby et al., 2019). Notably, learning was inconsistent when perturbations were sudden, indicating that learning is sensitive to specific training procedures. So far, most BCI learning studies have focused on two-dimensional cursor control. To further understand how much finger representations can be actively modified, future studies could benefit from perturbations (Kieliba et al., 2021; Oby et al., 2019), continuous neurofeedback (Ganguly and Carmena, 2009; Oby et al., 2019; Vyas et al., 2018), and additional participants.”

Overall the study contributes to the state of knowledge about human PPC cortex and its neurophysiology even years after injury when a person attempts movements. The methods are sound, but are unlikely (in this reviewer's view) to be widely adopted by the community. Two specific contributions of this study are 1) that it provides an additional data point that motor representations are stable after injury, lowering the risk of BCI strategies based on PPC recording; and 2) that it starts the conversation about how to make deeper comparisons between able-bodied neural dynamics and those of people unable to make overt movements.

Author Response

Reviewer #1 (Public Review):

Okawa et al show that topical oral application of an agent used in SPECT imaging, hydroxymethylene diphosphonate (HMDP-DNV), displaces pre-existing nitrogen-containing bisphosphonate (N-BP) from the jawbone of mice and prevents the development of bisphosphonate-related osteonecrosis of the jaw (BRONJ), a devastating complication that rarely occurs after invasive dental procedures in N-BP treated patients. They further demonstrate pro-inflammatory genomic signaling in gingival cells of N-BP treated mice, which reverses with HMDP-DNV. The methods are well-described overall and the results are potentially important. However, limitations include the short study period and the lack of multiple time points. Additional data to address these limitations would help to strengthen the authors' conclusions. If these results are added, this work could have a high impact in the field and the data could set the stage for further testing. The significance lies in the unmet need for therapeutic options to prevent this complication, which is widely dreaded and impedes the use of often needed bisphosphonate therapy.

We agree with this comment and performed an additional experiment to investigate a long-term healing of HMDP-DNV treatment. We performed an additional experiment, in which the outcome of HMDP-DNV topical treatment to the tooth extraction wound of ZOL-injected mice was obtained after 4 weeks of the tooth extraction. In addition to the reported effect of HMDP-DNV at 2 weeks after tooth extraction, this additional experiment addressed: (1) the longer study period and (2) more than one time point for treatment assessment.

Author Response

Reviewer #1 (Public Review):

In this paper, Chaudhary et al assessed 143 children with AML, and out of 20 mitochondria-related DEGs that were chosen for validation, 16 were found to be significantly dysregulated. They show that upregulation of SDHC and CLIC1 and downregulation of SLC25A29 are independently predictive of lower survival, which was included in developing a prognostic risk score. They also show that this risk score model is independently predictive of survival better than ELN risk categorization, and high-risk patients had significantly inferior OS and event-free survival. The authors demonstrated that high-risk patients are associated with poor-risk cytogenetics, ELN intermediate/poor risk group, absence of RUNX1-RUNX1T1, and not attaining remission (p=0.016). The risk score also predicted survival in the TCGA dataset. They concluded that they have "identified and validated mitochondria-related DEGs with prognostic impact in pediatric AML and also developed a novel 3-gene based externally validated gene signature predictive of survival."

Although this paper is interesting, it lacks novelty and does not advance the field significantly. The authors have used a similar approach in their recent paper in Mitochondrion where they showed that PGC1A driven increased mitochondrial DNA copy number predicts outcome in pediatric AML patients. Additionally, the authors have a small number of patients and chose only 20 genes for their analysis.

We appreciate that the reviewer found our paper interesting and read our recently published article in Mitochondrion.

In our previous work, the key finding was the predictive impact of mitochondrial DNA copy number on patients’ survival outcome in pediatric AML. Hence in the current paper, we deciphered it further to explore the heterogeneity associated with altered mitochondrial DNA copy number by identifying dysregulated genes in patients stratified by mitochondrial DNA copy number. We have identified several dysregulated mitochondria-related genes in pediatric AML for the first time hence we believe there is novelty in the work. Furthermore, developed novel mitochondria related gene signature that can predict survival of the pediatric patients with AML by analysing the prognostic impact of the dysregulated genes. These genes were identified to be dysregulated in pediatric AML for the first time and the gene signature model had predictive ability over and above ELN. Hence, we believe there is a novelty in the current work.

The initial transcriptomic analysis was done in limited number of patients which remains a limitation of the study and mentioned in discussion line 313-315. However, the validation of selected genes by RT-PCR was carried out in a consecutively recruited cohort of pediatric AML patients over more than 3 years (total 143 patients between July 2016 to December 2019), with a median follow up of 36 months.

As the main aim of the study was to decipher and validate mitochondria-related DEGs, the 20 genes were chosen based their mitochondrial localization as per mitochondrial compartment score. We have further validated these 20 genes in the external cohort from TCGA dataset (n=179), and the external validation adds to the strength of the study.

Reviewer #2 (Public Review):

The design of the study is good. One of the strengths/novelties of the paper is that the authors stratified patients into 3 groups based on mitochondrial DNA (mtDNA) copy number and performed RNA-seq, where previous studies have no/little information about mtDNA copy number. Out of 143 patients, they sequenced only 3, 4, and 5 patients from 3 groups, along with 3 controls. High heterogeneity among cancer patients is unlikely to be accounted for by 3-5 samples per group, thus having limited statistical power. The authors should discuss the limitations of the small sample size and possible outcomes. The authors validated their differentially expressed genes with TCGA LAML which are mostly adult patients. A correct comparison will be with pediatric AML from other larger studies that had not stratified patients based on mtDNA.

We appreciate that reviewer liked our study design. We agree that the initial transcriptomic sequencing was done in only few patients out of 143 patients recruited for this study.

Small sample size in the sequencing cohort is a limitation of the study considering the heterogeneity of AML (mentioned in the revised manuscript discussion line 313-315).

However, the validation of selected genes by RT-PCR was carried out in a consecutively recruited cohort of pediatric AML patients over more than 3 years (total 143 patients between July 2016 to December 2019), with a median follow up of 36 months. Only validated genes were used for further analysis and developing risk score.

We have validated the differentially expressed genes in the publicly available TCGA adult AML dataset and we agree that the better comparison would be with the larger cohort of pediatric AML patients. However, we could not find publicly available pediatric AML patients DEGs database, which additionally reports clinical outcomes for analysing prognostic impact. Hence the TCGA dataset was chosen.

External validation of our gene signature risk score further adds to the strength of the study as the gene signature appears valid for both pediatric as well as adult AML patients (this is mentioned in revised manuscript result line 205-207).

Author Response

Reviewer #1 (Public Review):

My primary criticism of this paper is that it misses the opportunity to give some key details about the statistics of neural activity during 'ripples' rather than studying identified replay events. A secondary criticism is that they limit their analyses to neurons that have place fields in both environments. I think the activity of the other 3 categories of neurons (active in Track 1 only, active in Track 2 only, and not active in either track) are also of critical interest.

We agree with the reviewer that it is important to demonstrate that the main observations are not due to a small subset of neurons or replay events. We have described above the inclusion of Figure 1- figure supplement 6, where the threshold for replay detection is made less stringent and the ratio of significant replay events/candidate replay events are now reported in the manuscript. To address the concern that the analysis is limited to neurons only with place fields on both tracks, we have added four more subpanels to Figure 1-figure supplement 6, where we perform our regression analysis on all spatially tuned (pyramidal) neurons (Figure 1-figure supplement 6E), neurons with only place fields on one track (track 1 and track 2 neurons will be in the upper right and lower left quadrant of plot respectively, Figure 1-figure supplement 6F), neurons with peak amplitude <1Hz on each tracks (Figure 1-figure supplement 6G) and finally, interneurons (Figure 1-figure supplement 6H). Consistent with our previous findings, we observe significant regressions for POST replay events for all spatially tuned neurons and neurons with place fields only one track. Conversely, neurons that were not active on either track and interneurons are not rate modulated by experience during replay.

It is important to note that replay detection uses all spatially tuned cells, but the regression analysis is limited to cells active on both tracks in the main analysis. The reason for this is now explained in more detail in the revised manuscript (page 5):

“It is important to note that a significant regression would be expected when analyzing neurons with a place field only on one track, as they are expected to participate in replay events of this track, while being silent during the replay of the other track. As such, our regression analysis only analyzed place cells active on both tracks and stable across the whole run (Figure 1-figure supplement 1B and see Methods).”

Reviewer #2 (Public Review):

This study by Tirole et al. addresses to what extent differences in firing rate that occurs during the awake experience of two different tracks are replayed during SWRs.

In principle, this is a topic broadly relevant to our understanding of the circuit-level mechanisms and neural coding of memory, because it can provide insight into the ways in which experience is transformed into memory traces, and in particular, whether an entire coding modality (firing rate patterns) is available for replay. However, I didn't have an easy time situating this study in the context of the existing literature. When I first read the title, I expected this work was going to address the question of if there is replay of rate-remapped experiences, which is still an understudied topic (but see Takahashi, 2015) and would be important to examine. But once I realized that the two experiences here are actually more like global remapping, it was less clear to me what is novel here.

My best guess about what's novel is that even though on the one hand, many studies have shown a distinguishable replay of two (or more) distinct experiences, e.g. different mazes like in Karlsson et al. 2009, different arms of a T-maze in Gupta et al. 2010, the overlapping central stem element of different trajectories in various mazes (Takahashi, 2015 and work from the Jadhav lab). On the other hand, there have been extremely detailed examinations of the contributions of firing rate changes (as distinct from temporal order or synchrony) as in Farooq et al. 2019. But perhaps the authors think that the intersection of those two kinds of work has not been studied, that is, how much do firing rate changes specifically contribute to the replay of two distinct experiences? In any case, regardless of whether I understood that correctly or not, the authors need to be more explicit in the introduction and discussion in contextualizing their work. I also suspect that the current findings are a direct logical consequence of putting together these well-established previous results; this would not mean the current work isn't a useful advance, but it would moderate the novelty and general interest.

Beyond this overall question of how the work relates to the extant literature, I have a suggested modification to the data analysis. I think that the quality of the data and the care taken in the analyses were very high in general, so I do not have any major concerns, and the conclusions are very thoroughly supported. However, I wonder if there is a way to simplify some of the analyses and make them a bit more straightforward to interpret. As the authors have realized, there is potential for a circularity in the analysis, in the sense that to compare firing rate differences for two tracks between Track and Replay, Replay events first need to be assigned to one or the other (decoded) Track. But then any firing rate differences may be contributing to the output of the decoder, rendering the analysis circular. I understand the authors use various methods like the firing-rate-insensitive method in Figure 2 to deal with this crucial issue. But wouldn't a simpler way be to leave out the cell whose firing rates are being analyzed out of the decoding step so that the labeling of Replay events is independent of that cell? This seems an intuitive and rigorous way to address the central question the authors have. Is there some reason why that isn't done?

We thank the reviewer for this feedback, and agree it is important to emphasize the novel contributions of the manuscript (as we see it), and clarify this further if needed. The reviewer is correct that there are several studies that have looked at rate remapping during reactivation. We have cited some of these, but have now updated our citations in the intro and discussion based on the comments here. While we have avoided directly criticizing a particular study in our earlier draft of the manuscript, these previous studies are affected generally by several issues: 1) replay detection methods were sensitive to rate modulation, creating a circular argument for the existence of rate modulation in replay. [Our study thoroughly addresses this with several controls]. 2) the analysis of reactivations rather than replay, which lacks the statistical rigor of sequence detection [we have focused on replay using a strict threshold for significance] 3) Replay/reactivations are analyzed for a single environment, making it difficult to distinguish between rate modulation and changes in the overall excitability levels of neurons maintained over behavior and sleep. [our studies uses two tracks to avoid this potential issue]. 4) When multiple contexts were decoded, neurons that only fired in one context were not removed from the analysis, artificially “inflating” any observed rate modulation. [we have circumvented this issue by only analyzing neurons with place fields in both environments]

The suggestion to repeat the analysis and leave one neuron out for replay detection is excellent, however this was avoided due to the required processing time- to run our complete analysis takes more than a week, and repeating this for each possible “leave-one-out” combination would take significantly longer (this has to be done independently for each neuron). We used multiple controls (track rate shuffle, replay rate shuffle, rank order correlation- figure 2, figure 2—figure supplement 2) to eliminate any possibility that a neuron’s firing rate could influence replay detection. Specifically, for rank-order correlation based replay detection, each burst of spikes is only treated as a single event (median of spike times in the burst), which directly circumvents the problem of firing rate biasing replay event selection.

Author Response

Reviewer 1

In general, I consider that the manuscript reflects a huge effort in terms work done and data collection, the manuscript is very well written, and it brings new knowledge in terms of cooperative breeding and its connection with groups size in ostrich. My major concerns are about the title and introduction that are in my opinion too broad and not enough detailed.

In the introduction the scientific background that led to this research is lacking, and the manuscript would benefit from a more supported introduction, which makes it difficult to understand how far this study went comparatively to previous studies. The research work was well conducted, and adjusted to the study aims. However, it would benefit from including more details on the observational data collected by the authors.

I think the research topic is interesting, and the study was well performed, but the manuscript would benefit from a more clear approach to the working hypothesis, expected results and background theories/hypotheses.

We are very grateful for the positive and constructive feedback. The title and introduction have been revised according to the reviewer’s suggestions. We provide a more extensive introduction to the hypotheses being tested, which are now explicitly stated. The observational data we collected have been described in more detail and we integrate our observational and experimental data more thoroughly.

In the evaluation summary, the reviewer highlights that we did not address some aspects of groups, such as relatedness and parentage. We have now added additional analyses to show these do not change the conclusions of our study (for details please see responses to reviewer 2 who raises similar concerns more extensively). These were not originally included in the manuscript as the aim of our study was to examine how group size and composition influence the average reproductive success for any given individual, irrespective of variation in relatedness and parentage within groups.

Reviewer 2

This work sets out to investigate experimentally the effect of differences in group size and group composition on reproductive behavior and success in ostrich groups. Direct field observations of the relationship between group composition/group size and reproductive success, do not allow for causal inference, as there may be several reasons why patterns may arise. For example, observing individuals having a higher reproductive success in larger groups than in smaller groups may not be a direct result of a larger group size per se, but it may be that higher quality individuals manage to establish themselves more often in larger groups. Hence, experimental manipulation of group size and group condition in natural contexts is important. 96 experimental groups of ostriches were established in fenced off areas in the Karoo in South Africa, varying the number of males (1 / 3) and the number of females (1 / 3 / 4 / 6) across groups. Groups were followed for almost a year, studying a period without parental care (eggs were removed and incubated in an incubator to measure reproductive success) and a period with parental care (eggs were left in the enclosures).

In the latter case, behavioral observations were done to study nest incubation, and sexual conflict (interruptions of incubation). The study was done for seven years, and having such data on experimental manipulations in semi-wild conditions is very valuable. The combination of behavioral analysis, with careful tracking of the fate of eggs (by daily nest checks), the experimental nature, and measuring reproductive success make for a very complete analysis of the breeding ecology of this system and can serve as a blueprint for more of such work in the fields of cooperation, group living and breeding ecology.

Some aspects, however, deserve more attention. First, at present, the origin and familiarity and possible relatedness among the group members of the experimentally composed groups is not discussed, and it may be that these factors play a role in shaping the results. Second, the reproductive measure used was the average number of chicks per sex, but it was not calculated at the individual level. There were no genetic analysis done to establish which individuals were actually successful in terms of reproduction. Since individual level selection is likely very important in this system, the results of average reproductive success need to be interpreted with great care. Third, the study was done under semi-natural conditions, meaning that the effects of other factors possibly shaping the success of group size and group composition in the wild (e.g., possible nest predation) were weakened. Finally, a closer connection between the experimental results on optimal group size, and whether this can actually be found in the dataset on natural variation in group size and group composition can be explored.

We are very grateful for the careful review of our work and positive feedback. The suggestions and comments have been extremely helpful in revising the manuscript, which have led to the following changes:

1) We have added details about the origin and familiarity of group members, together with extra analyses verifying that our results are not confounded by variation in within-group relatedness. The study population has a nine-generation pedigree allowing us to accurately estimate relatedness between individuals. In the design phase of the experiment, relatedness amongst individuals was kept low in accordance with data from natural populations, but there were related individuals of the same sex in some groups. We tested if the average relatedness within groups influenced the average number of chicks individuals produced and found no significant relationship (Supplementary file 1 – Tables S16 and S17).

2) We have included genotyping analyses of 3227 offspring to verify that our non-genetic estimates of average reproductive success per sex (total chicks produced by groups / number of same sex individuals) accurately reflect measures obtained using genetic estimates of individual reproductive success. Genetic and non-genetic measures were highly correlated (R >0.95). We have added these verification analyses to the manuscript. The text has also been edited to further clarify that our aim is to estimate the average reproductive benefits for any given individual of being in group of a particular size, rather than examining differences in reproductive success between individuals within groups, for which genetic methods are required.

3) We have clarified the advantages and limitations of experimental studies. As reviewer 2 highlights, observational studies alone do not provide causal insight into the factors influencing group size, but as reviewer 1 indicates, experimental studies can lack ecological context. Consequently, both have their merits. Experimental manipulations of entire social groups are currently lacking on large vertebrate cooperative breeders, but can be used to estimate the costs and benefits of living in different group sizes that arise independently of ecological conditions. The results of such experimental studies can be used as a benchmark against which other data can be compared, such as observational data on wild groups subject to ecological pressures, including nest predation. The discrepancies between experimental and observational data can then be used to infer the relative importance of social versus ecological factors in shaping social groups.

4) We have added a figure (Figure 1 - figure supplement 1) and extended the discussion to better connect our experimental data with our observations of natural variation in group size.

Author Response

Reviewer 1

This manuscript attempts to explain the well-known difference in DNA mutation rates between father vs. mother (paternal mutation is 4 times higher than maternal mutation in humans). Although the mutation rate difference was believed to arrive from the number of cell divisions (male germ cells undergo many more divisions compared to female germ cells), recent studies suggested that most mutations arise from DNA damage (which will be proportional to the absolute time) rather than DNA replication-induced mutations (which will be proportional to the number of cell divisions). The authors thus revisited the question as to why the paternal mutation rate is higher (if absolute time is more important than the number of cell divisions in causing mutations). They used 'taxonomic approaches' comparing paternal/maternal mutation rates of mammals, birds, and reptiles, correlating them to specifics of reproductive mode in these species. To measure paternal vs. maternal mutation rate, they compared the mutation rates of neutrally evolving DNA sequences between the X chromosome vs. autosomes, as well as the Z chromosome (utilizing the fact that the X chromosome will spend twice more generations in females than males, while autosomes spend equal time. Likewise, the Z chromosome will spend twice more time in males than in females, while autosomes spend equal time).

They first confirm the paternal bias across a broad range of species (amniotes), eliminating many species-specific parameters (longevity, sex chromosome karyotype (XY vs. ZW), etc) as a contributor to the paternal bias. This implies that something common in males in these broad species causes paternal bias. They show that in mammals, the paternal bias correlates with a generation time. They propose that the total mutation is determined by the combination of the mutation rate during early embryogenesis (when both male and female have the same mutation rate) and the later mutation rate when two sexes exhibit different mutation rates. This model seems to explain why generation time correlates well with the extent of paternal bias in mammals. However, this does not explain at all why birds do not exhibit any correlation with a generation time. The speculation on this feels rather weak (although there is nothing they can do about this. Fact is fact).

The logic behind their analysis is well laid out and seems mostly sound. Their finding is of broad interest in the field.

• I am confused by this statement (the last sentence in the result section): 'If indeed the developmental window when both sexes have a similar mutation rate is short in birds then, under our model, generation times are expected to have little to no influence on α." Based on their model, if the early period is gone, when the mutation rates are similar between sexes are similar, intuitively it feels that generation time influences α even more. Am I missing something? (if the period with the same mutation rate is gone, then females and males are mutating at different rates the whole time).

We apologize for the lack of clarity, as we should have made clear that here we are assuming a fixed ratio of paternal to maternal generation times. Under that assumption, if female and male germ cells are accumulating mutations as a fixed rate over time, then for each sex, the number of mutations accumulated with time is a line that goes through the origin, and the ratio of the paternal-to-maternal slopes (α) will be constant regardless of the age of reproduction. In other words, if Me=0 in equation 1, then α would be constant for any fixed ratio Gm/Gf. We have revised this sentence to be clearer; lines 334-338 now read:

“If indeed the mutation rate in the two bird sexes differs from very early on in development (i.e., if term Me ≈ 0 in equation 1), then assuming a fixed ratio of paternal-to-maternal generation times, our model predicts the sex-averaged age of reproduction will have little to no influence on α.”

• The authors state that this paper provides a simple explanation as to why paternal biases arise without relying on the number of cell divisions. However, it seems to me that the entire paper relies on the recent findings that mutation arises based on absolute time (instead of cell division number), and the novelty in this paper is the idea of 'two-phase mutation rates' to explain the observed numbers of paternal bias in various species. Yet it fails to explain the mutation rate difference in birds. There is not enough speculation or explanation as to what determines different mutation rates in males of various species. Although the modeling seems to be sound and there is nothing that can be done experimentally, I felt somewhat unsatisfied at the end of the manuscript.

We agree with the reviewer that our paper does not address why the ratio of paternal-tomaternal mutation rates is lower in birds than mammals, and had stated so explicitly (lines 358360): “Another question raised by our findings is why, after sexual differentiation of the germline, mutation appears to be more paternally-biased in mammals (∼4:1) than in birds and snakes (∼2:1).”

To try to gain more insight into this question, we are now analyzing mutations in a set of three generation pedigrees from birds and reptiles, which should allow us to obtain a direct estimate of α and characterize sex differences in the mutation spectra, which we can then compare to what is seen in mammals. While this analysis is beyond the scope of this manuscript, we now note how this question might be pursued (lines 360-362):

“In that regard, it will be of interest to collect pedigree data from these taxa, with which to compare mutation signatures to those typically seen in mammals.”

Reviewer 2 The primary goal of this paper is to re-assess the cause for the excess of male over female germline mutations seen in many animals. By re-analyzing X (Z) and autosomal substitution rates across 42 species of mammals, birds, and snakes, and fitting a model that allows for a constant and equal-sex embryonic mutation rate, along with a mutation rate that increases with age, the authors show that there is no need to invoke the model that assumes mutation rate depends strictly on numbers of cell divisions.

Strengths 1. The paper challenges a dogma in evolutionary genomics, which states that males have a higher germline mutation rate than females. It establishes convincingly that the count of premeiotic mitotic divisions is NOT the primary driver of the excess male mutations, but instead, it is the intrinsic mutation rate in males (balance of DNA damage vs DNA repair) that accumulates over time.

1. The authors establish a simple model where the number of mutations that accumulate each generation depends on the embryonic mutation rate (which is shown empirically to not differ between the sexes) and a post-maturity mutation rate, which has elevated male mutation (driven presumably by a shift in the balance between DNA damage and DNA repair). The model is very clear and intuitive described.

2. The paper is extremely carefully thought-out, planned, and executed. Criteria for inclusion and exclusion of species in the phylogenetic work are clearly laid out. Similarly, decisions about filtering genomic regions (avoiding repeats, etc.) are well done and exhaustively documented. The standard of scholarship is very high - for example, the analysis of de novo mutation rates in mammals pulled in data from no fewer than 15 published studies.

Weaknesses 1. The method of estimating alpha relies on the assumption that the mutation process (and rates) are the same in autosomes and sex chromosomes. There is an attempt to control for GC content and replication timing, but it is easy to imagine other factors at play, including the inactivation of one X in females, the extensive differences in chromatin modifications, especially of the X, that differ in males vs. females. The case of the cat X chromosome, with its 50 Mb of recombination cold spot and corresponding oddly slow substitution rate, might be just one example of features in other species that cause other perturbations in the substitution rate of the X. This does not seriously erode confidence in the results, but there is more potential for intrinsic mutation rates of sex chromosomes and autosomes to differ than is suggested by the authors.

We agree with the reviewer that despite our attempts, we do not control for all factors that distinguish X and autosomes beyond exposure to sex. We had written that “while our pipeline may not account for all the differences between autosomes and X (Z) chromosomes unrelated to sex differences in mutation, the qualitative patterns are reliable.” and have now included a sentence to make this limitation clearer (lines 165-167):

“Nonetheless, it is unlikely that our regression model perfectly accounts for all the genomic features that differ between sex chromosomes and autosomes other than exposure to sex.”

In turn, the assumption that mutation rates in X (Z) and autosomes differ only with regard to their exposure to sex (after accounting for base composition and other genomic features) is unproven; we now state this assumption explicitly in the Methods (lines 678-681). Nonetheless, it seems warranted by the high concordance of evolutionary- and pedigree-based estimates of alpha in humans, mice and cattle. With regard to the specific factors mentioned by the reviewer, excluding CpG sites has little effect on our qualitative conclusions for mammals (see Fig S1E), suggesting that DNA methylation differences between X and autosomes are not having a major influence on our findings. Moreover, X-inactivation in the germline of mammals (as distinct from the soma) is likely quite short-lived, given that it lasts around three days in early development of mice (Chuva de Sousa Lopes et al. 2008) and at most four weeks in humans (Guo et al. 2015). Thus, it is unlikely to be an important mutation rate modifier. We have now reworked three paragraphs in the main text to make the limitations above clearer (lines 127-175).

1. The authors point out that the human mutations in spermatogonia are due to mutation signatures SBS5/40 ( which are known not to be correlated with cell division rates). The work on the nonhuman species could be greatly extended with this mutation spectrum approach. For each species, one could ask: Are the mutation spectra of the embryonic mutations consistent between males and females? What about the mutation spectra for the post-puberty individuals? Is alpha consistent across mutation signatures? Does the GC bias correction impact these inferences?

Unfortunately, there is not enough de novo data to address this question outside of humans. In turn, the analysis of substitution data is unreliable, because of the differential impact of repeated substitutions at a site and the effects of GC-biased gene conversion.

1. While the data do not suggest reasons WHY males display a higher mutation rate, it is fair to ask whether the evolutionary drive for a higher mutation rate might shape the mechanism whereby it happens. There is a certain amount of speculation in the paper as it is, and it is done in a way that is often well supported by data after the fact. Speculation about why males have an elevated mutation rate would not erode the overall quality of the paper, and I would expect that many readers would be eager to see what the authors have to say on the subject.

As we envisage it, along the lines of Lynch’s models for the evolution of germline mutation (Lynch 2010), there is likely selection to keep the mutation rate as low as possible, subject to the constraints of the need to replicate DNA, repair damage, etc. efficiently. Why the attainable lower limit would be higher in males than in females is unclear to us, both mechanistically and in terms of evolutionary selection pressures. As we now note lines 353-355, a potential proximal cause is a greater effect of reactive oxygen species, a major source of DNA damage, in male germ cells than in oocytes (Smith et al. 2013; Rodríguez-Nuevo et al. 2022). Potential evolutionary causes are even less clear to us, but could be related to the greater competition among sperm vs. oocytes (added in lines 354-357).

Another way to think about these results is as shifting the question somewhat, broadening it from the long-standing puzzle of the selection pressures shaping sex differences to asking what determines the relative mutation rates of different cell types, including oocytes and spermatagonia but also somatic cell types/tissues. We had previously written that “our results recast long standing questions about the source of sex bias in germline mutations as part of a larger puzzle about why certain cell types (here, spermatogonia versus oocytes) accrue more mutations than others.” We have revised the final paragraph of the Discussion to try to emphasize this point.

Overall the paper achieves its intended goal of toppling the dogma that the excess male mutation rate is driven by number of rounds of cell division in spermatogenesis (compared to oogenesis).

Author Response

Reviewer #2 (Public Review):

While several studies have now been performed using time-varying exposures, i.e. PMIDs 35532785, 33749377, 35484151, 35679339, MR studies with time-varying outcomes have been lagging behind. Richardson et al. leveraged time-varying effects of both adiposity and vitamin D levels to investigate the dependency of childhood and adulthood body size on vitamin D levels during childhood and adulthood. Hence, in this way, MR analyses are conducted to the same outcome, measured at different timepoints in the life course.

Strengths:

Usage of both time-varying exposures and outcomes: Through exploiting individual-level data on vitamin D status, the authors demonstrate that childhood body size, but not adult body size, has an effect on childhood vitamin D.

In addition, both childhood and adulthood body size do affect vitamin D levels during adulthood, however the effect of childhood body size on vitamin D seems to be indirect, as its effect is attenuated when taking adulthood body size into account.

Hence, these effects are time-specific and illustrate the feasibility of using time-dependent genetic effects in MR to separate effects from early and later life on an outcome measured at different timepoints in the life course.

Limitations:

While multivariable MR is an elegant tool to assess direct and indirect effects of an exposure on outcome, a recent preprint highlights poor performance of multivariable MR to study time-varying causal effects (https://www.medrxiv.org/content/10.1101/2022.03.16.22272492v1). A description of strengths and limitations of MR, and especially of the multivariable MR design is lacking in the Discussion section.

Many thanks for this suggestion. The preprint mentioned by the reviewer (which has yet to be peer reviewed at the time of this response) in fact mentions the approach applied in our work where the authors claim that ‘multivariable Mendelian randomization is a legitimate tool for obtaining meaningful inferences in this case.’ That said, we agree that adding some further discussion regarding the strengths and weaknesses of our approach is warranted (page 7):

‘Findings from these endeavours should facilitate studies conducting techniques such as lifecourse MR, which can provide insight into the direct and indirect effects of modifiable early life exposures on disease outcomes by harnessing genetic estimates obtained from unprecedented sample sizes when conducted in a two-sample setting. That said, lifecourse MR requires careful examination of genetic instruments to ensure that they are capable of robustly separating the effects of an exposure at different timepoints over the lifecourse (Sanderson et al (2022, in press)).’

Abstract: background and conclusions focus on the influence of vitamin D deficiency on disease risk, hence using vitamin D as an exposure variable. The current study investigates the effects of childhood and adulthood body size on childhood and adulthood vitamin D levels, hence using vitamin D as an outcome variable. I agree that differential time points at which exposures and outcomes are measured may impact conclusions drawn from MR studies, and that childhood/adulthood adiposity may have differential effects on vitamin D levels, during childhood or adulthood. However, as vitamin D is used as an outcome variable in this study, it is less clear how the findings impact the causal influence of vitamin D deficiency on disease risk.

We agree with the reviewer that future work is necessary to investigate how the findings of this work may impact disease risk, although this is a substantial undertaking which is outside the scope of this short report. We have therefore added the following to page 6 of our Discussion to make the point that future work is necessary to investigate this:

‘Future studies are therefore warranted to disentangle the causal factors which influence disease risk from non-causal confounding factors through the triangulation of multiple lines of evidence including those identified by robustly conducted MR studies.’

Following up on the previous remark, the authors state in the Discussion that adiposity may have acted as a confounding factor on the observed association between vitamin D and T1D (Hypponen et al. 2001). I agree that obesity/adiposity may act as a confounder in observational study designs assessing the effect of vitamin D on disease risk. This is supported by the causal effect of body size on vitamin D levels. However, as also other factors beyond adiposity might influence the observed association between vitamin D and T1D, and hence might explain the discrepancy between observational and MR studies, I would like to suggest rephrasing it more cautionary before jumping to the clinical implications.

We have updated this section of the Discussion on page 6 to tone down the clinical implications of our findings by replacing the previous sentence with:

‘Evidence from this study therefore highlights the importance of developing a deeper understanding into the role that confounding factors, such as adiposity, may potentially have in distorting observational associations between vitamin D levels and disease risk’

Author Response

Reviewer #1 (Public Review):

This paper describes a new software tool: smartScope, for automated screening of cryo-EM grids. SmartScope can also perform automated data collection on suitable grids, including using beam-image shifts and tilted stage geometries. SmartScope uses deep-learning approaches for the selection of squares and holes of interest. The description of the software given in the paper is very promising, and as the code has not yet been made available, I cannot comment on its modularity, ease of installation, or general usability.

The convolutional neural networks for square and hole detection were trained on relatively few examples, and supposedly all from the same microscope. How easy would it be for users to re-train these detectors for their own purposes? Could a description of that be added to the paper/documentation?

Training was done on a mix of images coming from Ceta and K2 detectors. We added more details about the nature of the training data in the Materials and Methods section. Users will be able to re-train the model using the code provided.

The introduction makes the same point over multiple pages, and could probably be easily cut in half length-wise. This will force the authors to formulate more succinctly, and thereby more clearly. Hopefully, this would then eliminate wooly or incorrect statements like: "the beginning of each new project is fraught with uncertainty", "[The number of combinations] grows exponentially with the inclusion of each parameter" (it doesn't!), "would be an invaluable tool".

We carefully drafted the introduction to appeal to the broad audience of eLife while emphasizing the significance of our work. We have edited the text to make it more concise without missing the important points while reducing its length by over one third.

Also, the first half of the Abstract needs some rewriting. It focuses first on grid optimisation, which is not what smartScope is about. SmartScope is about grid screening. Just say that and save some lines in the Abstract too.

While SmartScope is not a tool for grid optimization, it provides direct feedback on grid quality which is a critical component of cryoEM specimen optimization. To clarify this point, we edited the abstract to highlight the screening aspect of SmartScope and we shortened it from 197 to 151 words.

Lines 257-261 describe some setup in serialEM. Perhaps because I am not familiar with that software myself, but I had no clue what those lines meant. Perhaps some example setup files could be provided as supplementary information?

Since setup files are tailored to specific hardware combinations, a settings file itself would not be beneficial. However, we added a new supplementary table with examples of 2 tested microscope configurations. As with any software, we expect SmartScope to evolve as new users report bugs and request new features. We also hope that a community of open-source developers will help us move it forward. For that reason, users are encouraged to refer to the “live” table on the documentation website of SmartScope where additional hardware combinations will be posted as the software is tested on new systems.

For the DNA polymerase data set: mention in the Results section how long the entire data collection (or 4.3k images) took. Also, the sharpened map in the validation file has a very weird distribution of greyscale values. Its inclusion of volume with varying greyscale is basically a step function, indicating that this is more or less a binary density map. I suspect that this is a result of the DeepEMhancer procedure. But given that the scattering potential of proteins is not binary, I wonder how such a map can be justified. Also, the FSC curve shown in the paper does not mention any masks, but the reported resolution of 3.4A is higher than the unmasked resolution calculated by the PDB: 3.7A. Why is the DeepEMhancer software used here? Is it hiding a slightly suboptimal map? As map quality is not what this paper is about, perhaps it would suffice to show the original map alone?

Thank you for pointing out the need of more clarity regarding this point. DeepEMhancer seems to apply a more conservative “sharpening” in the lower resolution areas of the map leading to more pleasing images. Hence, we used the corrected map for display purposes only. The raw map and half-maps are provided via EMDB. The FSC curve and overall resolution values reported in the paper were obtained using a shape mask produced using standard procedures implemented in CryoSparc. FSC curves and local-resolution map (Resmap) were calculated using the half-maps produced during refinement prior to sharpening We have now added the requested details to the figure legend. We also added the unmasked resolution in table 1 together with information about data collection throughput.

Author Response

Reviewer 1

In Drosophila germline, most piRNA loci use a non-canonical mechanism to transcribe piRNA precursors at the presence of H3K9me3, which depends on an HP1a paralog called Rhino/HP1d that specifically binds piRNA loci. How does Rhino find the right loci to bind? The current model in the field posits that maternally deposited piRNAs provide a specificity cue for Rhino. Now, Baumgartner et al. from Brennecke Group described a novel factor, the ZAD zinc-finger protein CG2678/Kipferl, that appears to provide another key specificity input to a subset of Rhino's chromatin binding, specifically in differentiated female germline (but not in males or stem/progenitor cell types in the female germline). Using genetics, genomics, genome editing, microscopy and biochemical approaches, Baumgartner et al. propose that Kipferl binds a G-rich DNA motif and, at the presence of local H3K9me3, recruits and/or stabilizes the binding of Rhino to these loci and then convert them from transcriptionally inert heterochromatin to piRNA-producing loci. Overall, the text is well written, the figure is clear, and the data is of high quality. With some additional experiments and text edits, this work represents a significant contribution to the field and should attract readers working on piRNA, transposon, satellite DNA, zinc-finger proteins, HP1 and heterochromatin.

Specific concerns

1. The genetic hierarchy between Kipferl and Rhino requires further clarification. Authors seem to propose a simple model where Kipferl acts genetically upstream of Rhino. This simple hierarchy is at odds with several observations. First, the center of Kipferl binding generally has less Kipferl binding without Rhino (Fig 5D). In some cases, Kipferl binding is completely gone without Rhino (Fig 7E middle, bottom). The text describes the loss of Kipferl spreading without Rhino but should also mention this reduction/loss in Kipferl binding. The effect of rhino-/- on Kipferl's chromatin binding should be shown along with wildtype level of Kipferl enrichment in Fig 5C for proper comparison. How should readers understand the effect of Rhino on Kipferl? What is the prominent Kipferl domain in rhino-/- in Fig 5B? Second, the broad binding of Kipferl is gone in rhino-/-, does it mean Kipferl requires Rhino to spread? Or, could Rhino (that is recruited by maternally deposited Piwi/piRNA) recruit Kipferl to neighboring sites, which look like a spreading phenomenon? Most importantly, the argument of Kipferl recruiting Rhino should be directly demonstrated by a sufficiency test in addition to the presented evidence of necessity. Could authors tether Kipferl in H3K9me3decorated regions to see if Rhino is recruited and vice versa? Observations like 42AB in Fig 5E make one wonder if Rhino also recruits Kipferl, so their relationship is not simply Kipferl recruiting or acting upstream of Rhino, as described throughout this manuscript. Clarifying the relationship between Kipferl and Rhino is essential as it is a central claim made.

The relationship between Kipferl and Rhino is indeed complex and we agree that the linear hierarchy as stated in the first submission is too simplistic. We therefore added a clear statement that loss of Rhino impairs spreading as well as stability/strength of the Kipferlchromatin interaction (text relating to Figure 5, second paragraph, Figure 5C,D) . We furthermore edited relevant passages in the text to clarify the points raised by this reviewer. We added an analysis of Rhino/Kipferl domains and the binding of Rhino or Kipferl in kipferl mutants and rhino mutants, respectively (panel 5C). This strengthens the conclusion that Rhino and Kipferl are co-dependent at many sites. Together with the previous analysis that focuses on Kipferl peaks in rhino mutants (now panel 5E), we conclude that Kipferl does bind many Rhino domains by itself, albeit at considerably lower levels and in less broad peaks. We do not know what the prominent Kipferl accumulation observed in immuno fluorescence in rhino mutants corresponds to. The suggested tethering experiment is an interesting suggestion that we consider part of a follow-up study that also aims at understanding the exact molecular and structural basis of the Rhino-Kipferl interaction, ideally in complex with DNA.

1. DNA binding of Kipferl remains putative. Since the 4th zinc-finger is shown to impact Kipferl localization via interaction with Rhino, it remains formally possible that the first three zinc-fingers control Kipferl localization via protein-protein interaction rather than direct DNA binding. Unless direct biochemical evidence of Kipferl binding DNA is available, the DNA binding of Kipferl should be toned down and described as putative and requires further investigation in text.

We agree that definitive statements addressing this question require biochemical or structural insight into Kipferl-DNA interactions. We therefore made text changes to reflect this throughout the text relating to Figures 5 and 6.

1. The relative contribution of maternally deposited piRNAs versus Kipferl in recruiting Rhino is unaddressed. Prior work from multiple groups including Mohn et al. 2014 Cell from the same group of this manuscript suggested a role of maternally deposited piRNAs in determining a subset of H3K9me3 domains as Rhino binding sites. Is Kipferl or maternally deposited piRNA a better predictor of Rhino binding? This manuscript proposes that Kipferl binds a simple G-rich motif and at the presence of H3K9me3 recruits Rhino binding. The readers are left wondering where maternally deposited piRNAs fit in the model of Rhino recruitment, which should be tested or discussed in text, as maternally deposited piRNA is seen as the key determinant of Rhino binding before this work.

At this point, we cannot firmly separate the role of maternal piRNAs (which would act early in embryogenesis) from a guiding function of Kipferl, whose function during early embryogenesis is unclear (e.g. we see strongly reduced levels of Kipferl in germline stem cells). The current data in the field, together with the new Kipferl findings, indicate that Rhino requires H3K9me2/3 and an additional specificity factor/determinant for stable chromatin binding in the differentiating female germline. While maternal piRNAs might be essential to provide locus-specific H3K9-methylation, Kipferl has the capacity to alter the Rhino profile considerably at sites where H3K9me2/3 co-occurs with Kipferl recruitment sites to chromatin (presumably DNA motifs). Together the two pathways might act in parallel to explain why certain transposon insertions are bound by Rhino, while others are not. We aimed to clarify our view on this important topic in the revised Discussion section (second paragraph).

Reviewer 3

In this manuscript, Baumgartner et al investigated how cells control Rhino specific deposition on only a subset of the H3K9me3 chromatin domains to specify piRNA source loci. They identified a previously unknown protein, Kipferl, which by interacting with the chromodomain of Rhino guides and stabilizes its specific recruitment to selected piRNA source loci. Kipferl would be preferentially recruited to Guanine-rich DNA motifs. They show that in Kipferl mutant flies, Rhino nuclear subcellular localization and Rhino's chromatin occupancy changes dramatically. Then, they dissect all the domains of the Kipferl protein and show that the Rhino- and DNA-binding activities can be separated and that the 4th ZnF of Kipferl is required to interact with Rhino.

It is a very elegant genetic work (CRISPR-edited, rescue, KD, overexpression fly lines). In addition, the authors used a combination of yeast two hybrid screen, ChIP, small-RNA-seq and imaging to dissect the function of this new protein. The data in this paper are compelling. Some conclusions might be more moderate. Even if the effect of Kipfler on 80F (Rhino binding, piRNA production) is very obvious, this study also clearly demonstrates that other protagonists are required for the specific binding of Rhino to other piRNA source loci (including 42AB and 38C).

• Is Kipferl expressed early during oogenesis development? If Kipferl starts to be expressed only after the GSCs and cystoblast stage, Kipferl is probably not required to determine the specification of piRNA source loci identity but probably more for the maintenance of the specification. Could the authors discuss or comment on that?

According to our image in Fig. 2D, Kipferl is very weakly expressed in GSCs and early cystoblasts. This is also supported by our unpublished observations on a cultured germline stem cell line (see above), where Kipferl is not detectable on chromatin by ChIP-seq. In these cells, Rhino has a remarkably different chromatin occupancy. Also in testes where Kipferl is not expressed, a different Rhino pattern was observed (Aravin laboratory) despite males inheriting the same complement of maternally deposited piRNAs. Together these data are consistent with a model where Kipferl acts as a specificity factor at its binding sites. We agree, however, that several Rhino domains exist where Kipferl does not show pronounced binding without Rhino. At these sites, Kipferl might act as a stabilizer or maintenance factor for Rhino, as it is nevertheless required for stable Rhino binding. In agreement with findings from testes (Aravin lab), we argue that Rhino’s chromatin occupancy in ovaries is not stable across developmental stages. And that it is respecified upon cystoblast differentiation, at least in part, by Kipferl. We also addressed this central point above (general comment #4 and 5).

• To perform most of their ChIP-seq analysis, the authors have divided the genome into pericentromeric heterochromatin and euchromatin based on H3K9me3 ChIP-seq data performed on ovaries. With this classification the 42AB (2R:6,256,844-6,499,214) and the 38C (2L:20148259-20227581) piRNA clusters known to be heterochromatic fall in the euchromatic part of the genome. Was there a problem with the annotation?

As stated in the text, clusters 42AB, 38C, and 80F were analyzed separately (as reference loci) and therefore were not included in either euchromatin or heterochromatin. The reviewer is correct that in the heatmaps, these clusters fall into the euchromatic compartment, as the classification into heterochromatin was not performed based on the presence or absence of the H3K9me3 chromatin mark at any given locus, but defined as inclusion in the continuous body of pericentromeric heterochromatin, which ends 400 kb upstream of 42AB and 2,000 kb downstream of 38C. We added a respective comment to the methods section (lines 945946).

• Some regions exist in euchromatin that are strongly enriched in Rhino, in Kipferl and in H3K9me3 but are not producing piRNA. Does this type of region exist in heterochromatin?

In euchromatin, roughly 80% of all Rhino-bound 1kb-tiles produce less than 10 piRNAs per kb per 1 million sequenced miRNAs. In heterochromatin, this is the case for only 10% of Rhino-bound tiles. This difference is likely caused by the high density of transposon fragments within heterochromatin, which allow the initiation of piRNA production from Rhino/Moonshiner-dependent transcripts through triggering.

• Kipferl has been identified to interact with Rhino by a yeast two-hybrid screen (Figure 2). A co-IP which is the classical method for confirming the occurrence of this intracellular RhinoKipferl interaction should be provided.

See our response to main comment #1.

• Rhino is known to homodimerize and it has been reported that this homodimerization is important for its binding to H3K9me3 (Yu et al, Cell Res 2015). It is surprising not to find Rhino among the interactors that were picked up from the screen. Do the authors have any explanations or at least comments on these results?

We can only speculate as to why Rhino was not identified in the Y2H screen. We are able to detect the homodimerization of Rhino in dedicated yeast two hybrid experiments in the lab, although the interaction was weak. One potential explanation is that dimerization of bait and prey is in competition with dimerization of bait and bait or prey and prey, reducing the efficiency of bait recruitment. For our yeast two hybrid experiments in the lab we use the Gal-4 system, while the screen was based on the more stringent LexA system, for which the homodimerization of Rhino might be too weak to be detected.

• In Kip mutants, the delocalization of Rhino to a very large structure at the nuclear periphery is a very clear phenotype (Figure 3). All the very elegant genetic controls are provided. This particular localization of Rhino is correlated with an increase in 1.688 Satellite expression and a colocalization of Rhino and the 1.688 RNAs in the nucleus. The authors propose that this increase is consistent with an elevated Rhino occupancy at 1.688 satellites. The authors should moderate their statements in the light of the results of ChIP experiments. Rhino is maintained on these loci in Kip mutants but an increase is not very clearly observed. Couldn't it be the RNA and not the DNA of this 1.688 region traps Rhino? The same in situ experiment should be performed after an RNAse treatment. The delocalization of Rhino is lost in the Kipferl, nxf3 double mutant flies. What is the chromosomal Rhino distribution in this context? Is the increase in nascent transcripts of 1.688 satellites lost?

The suggestion that RNA might trap Rhino at Satellite loci is a very interesting point. We performed the suggested RNAse treatment experiment in ovaries. This did lead to the disappearance of Rhino foci, however this is the case for both wildtype and kipferl depleted ovaries. While this indeed might point towards a role of RNA in stabilizing Rhino at chromatin, more in-depth experiments are required to clarify this.

Regarding the Nxf3 point: we clarified this in the revised text (lines 293-296): In nxf3/kipf double mutants we still observe strongly increased RNA FISH signal for the Satellite transcripts of 1.688 and Rsp families, which colocalize with GFP-Rhino (Fig. S3H). We therefore assume that Rhino is still associated with the same chromosomal regions as it is in the Kipf mutant. Just the localization at the nuclear envelope is lost.

• The level of some Rhino dependent germline TE piRNAs is affected in Kipferl GLKD. Is there a direct correlation between TEs which lost piRNAs and those for which the level of transcripts increases (Diver, 3S18, Chimpo, HMS Beagle, flea, hobo) ?

We added a dedicated statement to this in the revised text: piRNAs antisense to the TEs that are upregulated at the RNA level are strongly reduced, but they are not the only TEs where piRNAs are decreased (lines 340-343).

• Figure 5E, it seems that Kipferl binding is also dependent on Rhino. All the presented loci have much less binding of Kip in Rhino -/- (The scale for the 42AB locus should be the same between the Rhino -/- and the control MTD w-sh). In addition, the distribution of Rhino in the Kipferl-sh on the 42AB is maintained but seems to be different. Could the authors discuss these points?

This point has been addressed above (main revision requests).

• It is not clear why the authors focus only on Kipferl binding sites in a Rhino mutant in the Figure 5D? Even if the authors mention in the text that "Kipferl binding sites in Rhino mutants ... often coincided with regions bound by Kipferl and Rhino in wildtype ovaries" it should be added the same analysis presented in figure 5D centered on Kipferl peaks detected in ChIP experiments in WT condition in the different genotypes.

We addressed this in the new revised Figure 5 and the corresponding text.

• There is a discrepancy between the results found Figure 3A and Supp figure 3B. In the Rhino mutant the level of Kipferl protein does not seem to be affected whereas in the Rhino GLKD, there is a strong decrease of Kipferl protein. The authors completely elude this point.

See our comment to reviewer 1 above.

• Comparing the figure 5E and the figure 6G presenting both the 80F piRNA cluster, depending of the scale and the control line that was chosen to illustrate the results we can draw different conclusions. In the figure 5E we can conclude that le level of Kipferl decreases on the 80F locus in Rhino (-/-) compared to the control MTD w-sh, whereas in the figure 6G we can conclude that the level of Kipferl is similar in the Rhino (-/-) compared to the control w1118.

We made a mistake with the axis label for the Kipferl ChIP in w1118 in Fig. 6F (former panel G), which goes up to 800 like for the Rhino ChIP. This has been fixed.

• gypsy8 or RT1b are enriched in GRGG motifs and are also the ones that among Rhinoindependent Kipferl enrichment are the most Rhino enriched. Are these 2 elements present in the 80F cluster? Are these two elements derepressed upon Kipferl GLKD ? Where are these two elements in the figure presenting the change in TE transcript level upon Kipferl GLKD?

Both TEs are indeed present in cluster 80F. However, Kipferl loss does not result in their derepression despite piRNA loss. Rt1b/a are also not significantly upregulated in the rhino KD, suggesting that only evolutionarily old copies exist that are not able to reactivate. Gypsy8 is slightly upregulated in a rhino KD, but not in kipf KD. This discrepancy might be due to the difference in developmental timing when the effect of Rhino or Kipferl depletion sets in. Neither element is known to react strongly to any perturbation of the piRNA pathway and they are mostly considered old and inactive.

Author Response

Reviewer 1

This manuscript reports the cryo-EM structure of HOPS, a heterohexameric tether that participates in the fusion of late endosomes, autophagosomes, and AP-3 vesicles with lysosomes. HOPS has been characterized extensively through biochemical studies, which indicate that HOPS cooperates with SNAREs to facilitate membrane fusion. The authors conclude that HOPS is not a highly flexible structure as has been proposed, but instead has a stiff backbone to which the SNARE-binding Vps33 subunit is tightly anchored. Because the ends of HOPS bind to opposing membranes, the implication is that HOPS acts as a lever and membrane stressor, thereby amplifying the effects of SNARE assembly and catalyzing fusion.

The structural biology analysis was based on an improved purification protocol and appears to be well done. An atomic-level structure is always valuable, and this contribution will undoubtedly guide further research involving HOPS. Initial steps in this direction are presented in the form of functional studies of structure-guided mutants.

Structures are most useful when they help to define mechanisms, and the authors argue that the HOPS structure explains how HOPS catalyzes membrane fusion. The key conclusion is that the antiparallel association of the Vps11 and Vps18 subunits create a rigid core for the complex, leaving flexible ends that bind the Ypt7 GTPase to anchor the two membranes. This model is inconsistent with earlier suggestions that HOPS bends to bring the two membranes together. Instead, the inferred rigidity of the HOPS core, combined with the central location of the SNARE-binding module, suggests that HOPS acts as a lever that exerts a force on the membranes to promote SNARE-driven membrane fusion.

This interpretation is interesting and potentially exciting, but I question why the authors are certain that the Vps11-Vps18 core is truly rigid. Proteins can undergo all sorts of rearrangements. Is there evidence that Vps11 and Vps18 interact strongly and in a unique configuration? Portions of a protein that have a consistent structure in vitro might nevertheless rearrange during functional interactions in vivo. If there is any flexibility of the Vps11-Vps18 core, this property combined with the evident flexibility of the Ypt7binding portions and the low affinity of Vps41 for Ypt7 would make HOPS anything but a rigid membrane stressor. If the authors wish to make a strong point about the functional implications of the HOPS structure, these points need to be addressed.

Based on our data we conclude that the Vps11-Vps18 core represents a rigid structure. Our extensive 2D and 3D classifications, as well as the 3D variability analysis of cryo-EM data indicate no flexibility in this region of the complex (in contrast to the Vps41- and Vps39-termini of the particle), as illustrated in Figure 1 and Figure 2 - Supplemental Figure 3. Additionally, the highest resolution achieved in this region within the whole structure suggests the least flexibility of this region in comparison to other parts of the complex.

To get a better idea, we mapped the interface between Vps11 and Vps18. The interface area between Vps11 and Vps18 is 1972 A2 according to the PDBePISA tool, which is large enough to form a strong interaction and is comparable with protein interfaces in other complexes with similar structural elements as in HOPS (e.g. Yang et al. Nat. Comm. 2021, Kschonsak et al. Nature 2022). To demonstrate this, we added an additional Supplement Figure to Fig. 2 (Fig. 2-S4) addressing the interaction area between Vps11 and Vps18 and revised the manuscript text in line 111 with words “…large interface area of 1972 Å2 which provides a…”.

Reviewer 3

This is an exciting new cryoEM structure of the HOPS tethering complex, which is necessary for membrane fusion at the vacuole/lysosome in eukaryotic cells. Finally, we can visualize, at moderate resolution, the positioning of HOPS subunits with respect to each other, and predict how HOPS and its various binding partners, such as Rab GTPases and SNAREs, can interact and control fusion. A conceptual advance put forward by this structure seems to be a rigid central core of HOPS that may contribute to helping drive the efficiency of the SNARE-mediated fusion mechanism.

As exciting as this new structure is, however, the study seems to fall a bit short of its promise to explain "why tethering complexes are an essential part of the membrane fusion machinery, or how HOPS "catalyzes fusion." As such, the title is also misleading with regard to HOPS being the "lysosomal membrane fusion machinery."

Overall, the manuscript could benefit greatly, especially for a non-HOPS specialist reader, in providing more introduction and context to the complex and tethering/fusion mechanisms in general. Additionally, the examination of the structure, in light of decades of biochemistry and cell biology studies of HOPS (and homologous proteins that regulate fusion), seems superficial and suggests that deeper analyses may reveal additional insights and lead to a more detailed and impactful model for HOPS function. Moreover, are the insights gained here applicable to other tethering complexes, why or why not?

We thank the Reviewer for her/his kind and helpful comments and have addressed the concerns below and in the revised manuscript.

Author Response

Reviewer 1

The authors used a combination of biochemical assays and cryoEM to investigate the role of PME-1 in regulating PP2A, which revealed that PME-1 uses its unstructured loops to associate with the B-domain of the PP2A holoenzyme to regulate the function of the C-domain. This is a high quality work. This reviewer finds the later work involving p53 to be a helpful step in explaining the role the PME-1:PP2A interaction can have on important phosphorylation pathways, but I consider this aspect of the work to be very preliminary, especially given its rather minor effects. That said, the authors do not make claims that extend beyond the scope of the evidence they provide and thus I find the connection and discussion of PME-1, PP2A and p53 to be suitable on the whole.

Response: We greatly appreciate the positive comments and the recognition of our work.

Reviewer 2

The manuscript by Li et al is well-written and contributes an elegant cryo-EM structure of the PP2A-B56 holoenzyme, providing key structural rationale for holoenzyme demethylation and the inhibition of PP2A holoenzyme activity. A strength of the manuscript is the complementation of the structural data with a comprehensive biochemical/functional characterization demonstrating a mechanism for an oncogenic function of PME-1 in the regulation (inhibition) of p53 phosphorylation via PP2A-B56 holoenzymes under basal and DDR conditions.

Response: We greatly appreciate the recognition and positive comments of our work.

Reviewer 3

PME-1 catalyzes the removal of carboxyl methylation of the PP2A catalytic subunit and negatively regulates PP2A activity. Like the PP2A methyltransferase LCMT-1, PME-1 was previously thought to act only on the PP2A core enzyme. However, in this study, the authors show that PME-1 can interact and demethylate different families of PP2A holoenzymes in vitro. They also report the cryo-EM structure of the PP2A-B56 holoenzyme in complex with PME-1. Their structure reveals that the substrate-mimicking motif of PME-1 binds to the substratebinding pocket of B56 subunit, which tethers PME-1 to PP2A, blocks substrate-binding to PP2A, and promotes PME-1 activation and demethylation of PP2A holoenzyme. Their further mutagenesis and functional analyses indicate that cellular PME-1 function in p53 signaling is mediated by PME-1 activity towards PP2A-B56 holoenzyme. In summary, this study has provided significant insights into our understanding of PP2A regulation by PME-1, demonstrating that PME-1 not only demethylates the PP2A core enzyme, but also the holoenzyme to control cellular PP2A homeostasis.

Response: We greatly appreciate the recognition and the positive comments on our work.

Author Response

Reviewer 3

The number of identified anti-phage defense systems is increasing. However, the general understanding of how phages can overcome such bacterial defense mechanisms is a black box. Srikant et al. apply an experimental evolution approach to identify mechanisms of how phages can overcome anti-phage defense systems. As a model system, the bacteriophage T4 and its host Escherichia coli are applied to understand genome dynamics resulting in the deactivation of phage-defensive toxin-antitoxin systems.

Strengths: The application of a coevolutionary experimental design resulted in the discovery of a geneoperon: dmd-tifA. Using immunoprecipitation experiments, the interaction of TifA with ToxN was demonstrated. This interaction results in the inactivation of ToxN, which enables the phage to overcome the anti-phage defense system ToxIN. The characterization of the genomes of T4 phages that overcome the phage-defensive ToxIN revealed that the T4 genome can undergo large genomic changes. As a driving force to manipulate the T4 phage genome, the authors identified recombination events between short homologous sequences that flank the dmd-tifA operon. The discovery of TifA is well supported by data. The authors prepared several mutant strains to start the functional characterization of TifA and can show that TifA is present in several T4-like phages.

In addition, they describe T4 head protein IPIII as another antagonist of a so far unknown defense system.

In summary, the application of a coevolutionary approach to discover anti-phage defense systems is a promising technique that might be helpful to study a variety of virus-host interactions and to predict phage evolution techniques.

Weaknesses: The authors apply Illumina sequencing to characterize genome dynamics. This NGS method has the advantage of identifying point mutations in the genome. However, the identification of repetitive elements, especially their absolute quantification in the T4 genome, cannot be achieved using this method. Thus, the authors should combine Illumina Sequencing with a longread sequencing technology to characterize the genome of T4 in more detail.

We think the combination of Illumina-based sequencing and PCR analyses presented are more than sufficient to arrive at the conclusions drawn about the repeats that emerge in our evolved T4 clones.

To characterize the influence of TifA during infection, T4 phage mutants are generated using a CRISPR-Cas-based technique. The preparation of these phages is unclearly described in the methods section. The authors should describe in detail whether a b-gt deficient strain was applied to prepare the mutants. Information about the used primers and cloning schemes of the Cas9 plasmid would allow the community to repeat such experiments successfully.

We have added details to the Methods section to clarify and expand on our mutagenesis approach.

The discovery of TifA would benefit from additional data, e.g. structure-based predictions, that describe the protein-protein interaction TifA/ToxN in more detail.

We were unable to predict the ToxN-TifA interaction interface using AlphaFold, and we are currently conducting follow-up work to characterize how TifA neutralizes ToxN.

Several publications have described that antitoxins can arise rapidly during a phage attack. The authors should address that this concept has been described before as well by citing appropriate publications.

We believe that we have already addressed this point sufficiently in the Introduction of the manuscript, in which we discuss (1) the emergence of phage-encoded pseudo-toxI repeats to overcome P. atrosepticum toxIN and (2) the presence of the naturally-occurring antitoxins Dmd and AdfA in T4 and T-even phages, respectively. We also discuss the similarities between TifA, Dmd, and AdfA in the discussion of the manuscript. To our knowledge, these are the only known examples of antitoxins arising during phage attack outside of TifA, but we are happy to include additional citations of which the reviewers are aware.

The authors propose that accessory genomes of viruses reflect the integrated evolutionary history of the hosts they infected. However, the experimental data do not support such a claim.

We disagree with the reviewer’s comment, as our evolution experiment demonstrates the plasticity of the T4 genome during adaptation to different hosts, as well as showing that the T4 accessory genome includes genes necessary for infection of some, but not all hosts. The proposal also comes as the last sentence of the Abstract and is framed not as a conclusion, but as a proposal based on the work done here, with the clear intention of providing a sense of how future work may build off our work.

Author Response

Reviewer 2

Hansen et al. investigates the catalytic behavior of phosphatidylinositol phosphate kinases (PIPKs), a family of enzymes that generate the regulatory lipid, phosphatidylinositol 4,5bisphosphate (PIP2) of eukaryotic cells. In their previous studies the Authors showed the positive feed-back regulation of these enzymes by their reaction product, PIP2 using a clever methodology, namely the real-life fluorescent monitoring of the enzymatic activity in supported lipid bilayers. This time the Authors noted a substantial difference between the strength of dimerization of the type II (PIP5P 4-kinases) and the type I (PI4P 5-kinases) enzymes, the latter exhibiting very weak dimerization in solution in contrast to the stable dimer formation of the former. Using supported membrane bilayers, the Authors showed that at low protein density the type I enzyme (they used PIP5KB) followed the behavior described previously, namely membrane interaction determined by the presence of PIP2 in the bilayer and this behavior was the same for a mutant protein, unable to dimerize. However, at increased protein concentration, the PIP5KB enzyme started to form dimers, which increased its time of membrane residence, still dependent on PIP2. Furthermore, the Authors showed that dimerization had a major impact on catalytic activity, multiplying the positive feed-back effect described for the monomeric form. Lastly, they demonstrated the impact of the enhanced feed-back regulation under competitive reaction conditions (in the simultaneous presence of a PIP2 5-phosphatase) showing that the previously described bistable reaction product pattern is highly dependent on dimerization, which also increases the stochastic nature of product bistability in a competitive reaction setting. The Authors discuss the potential impact of these findings on the regulation of the enzyme in the real cellular setting.

Strengths:

This is an important study revealing a new layer of complexity in the interfacial kinetic behavior of an enzyme family that is central to the regulation of multiple cellular functions. The simplified in vitro set up allowed the Authors to examine in very exact terms the impact of protein dimerization on reaction kinetics and complex behavior under competitive reaction conditions. The in vitro methods are creative, the experiments are well done with appropriate controls and together with the data analysis convincingly support the Authors' conclusions.

Weaknesses:

1. The Discussion misses opportunities to relate the present findings to specific published observations: For example, it has been reported that type II PIP4KC knockout cells display increased PIP5K activity, presumably because of the heterodimerization of the proteins with the PIP5Ks, thereby reducing their activity (PMID: 31091439). An additional recent study described the regulation of the PIP5K by phosphatidylserine and cholesterol-rich domains (PMID: 31402097). Both of these studies raise questions that can be easily addressed by the reagents and methods described in the present study. Even if these studies are saved for the future, discussion of those published studies would emphasize the importance of the current findings in the context of the questions raised by them.

We thank the reviewer for mentioning these important articles. We extended our discussion to connect the finding of these articles to the PIP5K regulatory mechanism described in our manuscript. The following statements have been added to the discussion section:

“Although new molecular mechanisms concerning PIP5K activation have been revealed through single molecule characterization of PIP5K in vitro, it remains challenging to interpret how dimerization, PI(4,5)P2 binding, and interactions with peripheral membrane proteins regulate membrane localization of PIP5K in vivo. Complicating our interpretation of cellular localization, PIP5K can also reportedly interact with phosphatidylserine and sterol lipids, which modulate lipid kinase activity (Nishimura et al. 2019).”

“Left unregulated, the PIP5K positive feedback loop has the potential to generate excessively high concentrations of PI(4,5)P2 in cells, which would be detrimental to numerous signaling pathways that rely on cellular PIP lipid homeostasis. New evidence suggests that, in vivo and in vitro, PIP4K can attenuate PIP5K activity through the formation of a membrane bound heterokinase complex (Wang et al. 2019; Wills et al. 2022). Deciphering the molecular basis of PIP4KPIP5K complex formation using single molecule in vitro measurements will be critical for determining both the mechanism of kinase inhibition and for generating separation of functions mutants that perturb this regulatory mechanism.”

1. As written, the paper is not always easily accessible to readers who are not experts in biophysical methodology and terminology. Some explanation may help general readers to follow the manuscript.

In our revised manuscript, we include additional description in the results and discussion sections to more clearly explain how our experiments were executed and the rationale for our interpretations.

Author Response

Reviewer 1

They adopted a comprehensive experimental and analytic approach to understand molecular and cellular mechanisms underlying tissue-specific responses against 3-CePs. They used two cell lines - BxPC-3 and HCT-15 - as example models for responsive and non-responsive cell lines, respectively. Although mutation rates didn’t differ by the drug treatment, they observed changes in cell cycle and expression of genes involved in DNA damage, repair and so on. Furthermore, they combined RNA-seq and ATAC-seq data and applied two approaches, pairwise and crosswise, to identify a number of gene groups that are altered in each cell line upon the drug treatment. Finally, they calculated enrichment of up/down genes in different cell lines, tumor types and samples to estimate potential responsitivity against the drug. This study is unique in in-depth analysis of RNA-seq and ATAC-seq data in identifying genetic signature underlying drug treatment. This study has the potential to be applied to different drugs and cell lines.

We thank the reviewer for the precise and kind summary of our work.

However, several major concerns need to be resolved. First of all, the biological and clinical performance of 3-CePs is not clearly described. They referenced several papers but they seem to have focused on the chemical properties of the drug. Without proven activity of 3-CePs against cancers in vitro and in vivo, the rationale of the study would be compromised.

We apologize for not being clear enough when introducing previous findings on the differential sensitivity of HCT-15 and BxPC-3 cancer cell lines to 3-CePs. In the revised manuscript, we now cite references on the preferential activity of these agents against the pancreatic cancer cell line in 2D and 3D in vitro cancer models (see lines 71-74, 128-129). These compounds have been selected to exemplify the use of the pipeline in drug discovery and early-stage of drug development: indeed, only cellular data are available for these molecules, which have not yet been characterized in vivo. The pipeline itself offered a final perspective on directions to take for their further development, i.e. most sensitive tumor types to target (PAAD, KIRC).

Their RNA-seq analysis was focused on discovering differentially expressed genes between cell lines, time points, etc. Interestingly, they found that DNA damage and repair signal was specifically increased in HCT-15. But is this approach capable of finding signals that are constitutively expressed in different cell lines? In other words, what if the differential responsiveness to 3-CePs was already there even before the drug was introduced?

We thank the reviewer for pointing out such key concept. The premise for the developed approach is that factors determining the overall cellular sensitivity to a treatment must be determined by intrinsic characteristics of the cell line. For this reason, we built the sensitivity signature on basal transcriptome profiles, where we prioritized a subset of genes based on perturbational evidence (perturbation-informed basal signature).

Beyond signature genes, we show in figure R1 (see above) the results of a GSEA analysis on the whole overlap (300 genes) between DE genes from the baseline comparison (BxPC-3 ctrl vs HCT-15 ctrl) and those from the 6 h M treatment comparison, in the sensitive cell line (BxPC-3 M 6 h vs BxPC-3 ctrl). Pathways like ribosome biogenesis, ROS metabolism, UPR also arise, attesting that genes activated in response to the treatment also have a constitutively different expression in unperturbed cells.

Are there any overlapping signals between pairwise vs crosswise approaches?

We thank the reviewer for this question. To make it easier for the reader to compare the output from the two types of integration and to intuitively grasp their functional overlap, we changed the visualization of the results from the pairwise approach (Figure 4 D).<br /> Indeed, some functional pathways both new or already emerging from previous analysis, arise from both integrations. This overlap has now been directly discussed from the functional point of view in the main text (from line 348 and in the following crosswise integration paragraph).

Genes used as input in both types of integration are DE or DAR-associated, so this means that many of the hits that we find having the same double regulation (pairwise) also appear in CoCena modules. Among them, only few hits show both 1) the same double regulation in a specified comparison (as suggested by crosswise) and also 2) end up having the similar pattern of regulation across all conditions (contributing to the same CoCena module, one of the strengths of the crosswise integration). Indeed, while the pairwise integration checks one single comparison per time, CoCena checks the pattern throughout conditions providing a more holistic view of the gene regulation (e.g one gene can have a different pattern across conditions at the transcriptional and chromatin level). This is due to the biological fact that RNA and chromatin regulation is not 1:1 (also, for instance, from a timing perspective).

The major added value of the two approaches consists in their intrinsically different output information. Within a specific comparison, the pairwise integration detects genes consistently activated at the transcriptome and chromatin level. At this information level gene set enrichment can simplify the coherent functional role of this set of genes; we now report this extra information in figure 4 to provide a more granular description of the pairwise integration. Instead, CoCena analyzes the pattern throughout conditions, and clusters together genes and peaks that behave similarly. Functional annotation of genes behaving similarly can put together promoters and/or transcripts that together may orchestrate a specific process (as highlighted by GSEA on each module).

Probably a similar question with the above: is this methodology applicable to other drugs in addition to 3-CePs?

To address this extremely important point, that we agree with the reviewer would be key to prove the versatility of our approach, we further applied the pipeline to the prediction of cancer cell lines’ sensitivity to cisplatin, a thoroughly reported broad-acting chemotherapeutic also acting as a DNA damaging agent. Results strongly supported the broad applicability of our approach, which was able to predict sensitivity to this reference drug with extremely high accuracy.

Reviewer 2

Carraro et al. describe a framework to understand MoA and susceptibility of drug candidates by integrating RNA-seq and ATAC-seq information. More specifically, by collecting drug responses from high-sensitive and low-sensitive cell lines, the authors identified a key set of pathways with co-expression analysis, and further predicted sensitivity of different cancer cell lines.

The authors provided a new bioinformatics pipeline to integrate multi-omics data (RNA-seq and ATAC-seq) in a drug response study. This approach increased detection power and identified additional key pathways that are associated with drug 3-CePs. This framework has the potential to be applied to the general drug discovery process.

We thank the reviewer for the precise summary of our study.

However, the current manuscript failed to describe the integration methodology in a clear and concise way. Without a full understanding of the methodology, it’s tough to evaluate the downstream results in an unbiased manner.

We apologize for not having included sufficient details in describing the difference between CoCena and the other two horizontal and vertical approaches. As already discussed in the response to Reviewer 1, we now included a more detailed description not only in the Methods section (from line 894) but also in the main text (lines 393-400).

In addition, the authors didn’t mention how much additional value this multi-omics approach provided compared to the single-omic data set, as multi-omics approaches are more expensive and labor-intensive.

We thank the reviewer for this valuable point. To better support the claim for multi-omics approaches, we have extended the Introduction (lines 96-98), as successful integration of information derived from multiple omic layers usually strengthens the determination of the major observed cellular responses. Here, this information helps dissecting and predicting how perturbations (here by drugs) can affect the overall cellular dynamics and mechanisms underlying a certain niveau of sensitivity. We agree with the reviewer that current costs are still prohibitive for large scale use of multi-layer omics in many settings, mainly when it comes to clinical use or drug development. However, significantly less expensive technologies (90% cost-reductions, lines 53-55) have recently been announced, which assures us that approaches as outlined here, will be applicable to many more clinical questions in the near future. Further, we show evidence that some cellular responses to the drug-induced perturbation was only revealed by applying multilayer analysis, but not by a single omics layer, e.g. TGF beta and EMT signaling (see lines 456-459).

Reviewer 3

Carraro et al utilize systems biology approaches to decode the mechanism of action of 3chloropiperidines (a novel class of cancer therapeutics) in cancer cell lines and build a drugsensitivity model from the data that they evaluate using samples from The Cancer Genome Atlas and cancer cell lines. The approach provides a framework for integrating transcriptomic and open-chromatin data to better understand the mechanism of action of drugs on cancer cell types. The author’s approach is of sound design, is clearly explained, and is bolstered by validation via holdout sets and analysis in new cell lines which lends the findings and approach credibility.

The major strength of this approach is the depth of information provided by performing RNA-seq and ATAC-seq on cells treated with 3-CePs at various time points, and the author’s utilization of this data to perform pairwise and crosswise analyses. Their approach identified gene modules that were indicative of why one cell type was more sensitive to a particular drug compared to another. The data was then used to build a sensitivity model which could be applied to samples from The Cancer Genome Atlas, and the authors evaluated their sensitivity predictions on a set of cancer cell lines which validated the predictions.

We thank the reviewer for the accurate recapitulation of our work.

The major drawback to this type of approach is that it relies on next-generation sequencing (somewhat costly) and requires intricate bioinformatics analyses. While I agree with the author’s perspective that this approach can be applied to additional classes of drugs and cancer samples, I disagree with their view that it is efficient and versatile. However, for research teams with the means to perform both transcriptomic and open-chromatin studies, I think this integrated approach has promise for evaluating novel classes of drugs, particularly in cancer cell lines that are easy to manipulate in vitro.

We thank the reviewer for this insightful comment. As with almost every technology, the early years are more difficult and at times adventurous. However, we have seen enormous improvements in robustness of the technology and significant cost reduction with more to come. Only recently sequencing technologies have been introduced into the market with a further 90% cost reduction (as stated in line 53-55). We are convinced that due to their increasing affordability and robustness, RNA-seq and ATAC-seq will be implemented routinely into clinical contexts. As a group working at the cross-section between drug discovery and bioinformatics, we hope that our current work, accompanied by a fair and detailed sharing of our scripts, will become a head start to run this type of analysis also by others in the field who are not (yet) so close to bioinformatics and computational biology.

While there are examples of similar frameworks being applied to drug development, this work will add to the body of literature utilizing an integrated systems biology approach for pairing drugs with specific tumor or cancer types and understanding their mechanism of action on an epigenetic level.

We thank the reviewer for this very positive statement and the support for our approach and her/his interest in the described pipeline.

Author Response

Reviewer 1

The manuscript provides a dataset of single-cell transcriptomics of several adult mice ovaries and performs computational analysis to determine the molecular signatures of the cells isolated.

Strengths: - Provide data from different estrous stages and lactating. - Many markers are validated. - Several estrous cycle-specific biomarkers are revealed.

We thank the reviewer for the positive assessment of our efforts to comprehensively validate cell and estrous-cycle specific biomarkers.

Weaknesses: - It does not stratify or provided trajectories of the data according to the different estrous stages and lactation periods.

We have now added stratification of data sources in figures 1B, 5A, and 5B.

• Only single markers are validated, making it difficult to see the population.

While we show representative RNAish of single markers for the identification of the cellular populations, we provide heatmaps with complete signatures in Figures 1C, 2B, 3B, 4B, Dotplots in figures 4D, 5D, 6A, Figure 2 – supplement 1D,E, feature plots in Figure 3-supplement 1A,B, as well as fully referenced tables of validated markers in Supplementary Files 2, 3, and 4.

• The population of peri-ovulatory GC could be better characterized.

We now provide Oxtr as a more specific marker of peri-ovulatory Gc (see figure 3C and figure 3- supplement 1D), in addition to the validated markers presented in Supplementary File 4.

• There is no mention of specific populations or states in the lactation sample.

We now provide cluster composition by sample type in Figure 1B, as well as represent cell state differences in lactating samples in S3E, which are discussed in lines 196-197 and 272-275.

• Monocle analysis could be made more robust.

Since the graphical representation of lineage pseudotime trajectories of granulosa cells was counter intuitive, we have removed this analysis in favor or more concise explanation of differentiation and cell states amongst the mural and cumulus granulosa cells and their response to LH in lines 378-382.

• Specific populations of theca cells (interna and externa) are not named.

Specific populations of theca are now shown in figures 2 and figure 2 – supplement 1 and more extensively described in the results (lines 230-244) and discussion (lines 397-417).

• Differences between stroma 1 and stroma 2 are not found.

After reanalyzing the data, we concluded that these two interstitial stromal cell clusters could not be differentiated by specific dichotomous markers. Nevertheless, we noted that the expression of Ectonucleotide Pyrophosphatase/Phosphoiestrase 2 (Ennp2) was specific and limited to one of the clusters. Given that this same cluster expressed markers such as Col1a1, Lum, Loxl1, shown in the literature to be characteristic of fibroblast, we named them fibroblast-like stroma. The second subcluster, Enpp2 negative, was shown to be enriched in expression of steroidogenic markers such as Cyp11a1, and Cyp17a1 and was named steroidogenic stroma cluster. These results are now presented in figure 2 - supplement 1E,F.

• OSE is only mentioned in the Discussion.

The findings in OSE are now presented in Figure 4 and discussed in the results (lines 287-294) and discussion (lines 418-429).

Reviewer 2

This manuscript by Morris et al., entitled "A single cell atlas of the cycling 1 murine ovary" presented an interesting dataset for understanding cellular and transcriptional dynamics during the estrous cycle in mice. By using single-cell RNA sequencing, the authors reported new marker genes for different cell types and validated some markers using In situ hybridization. However, I believe that the main problem of this paper lies in the interpretation of data.

The major points include: 1. The authors used tSNE for visualization of the generated scRNA seq dataset, which, according to my knowledge, is outdated for scRNA seq data visualization as its reproducibility has become an issue. Which version of the Seurat package does the author use? And also the other software information should be implemented. Therefore, I suggest the authors reanalyze their dataset using an updated Seurat pipeline, and also reanalyze all of their data using UMAP.

The data have been reanalyzed with UMAP instead of tSNE. The R version is 4.1.3, it is now indicated in the Material and Methods section.

1. The authors aimed to explore the unrecognized complexity in the cellular subtypes and their cyclic expression states. For cellular heterogeneity, the authors reported detailed cell percentages of different cell types and validated the new markers using in situ hybridization, however, how do these cells change during the estrous cycle? According to the current manuscript (Figures 3A and 4A), it's hard to interpret such changes. The authors should emphasize this aspect of the description, one possible solution is to add a stack bar chart to show the proportions of different cells at different stages.

We added a plot showing the composition of each cluster by stage of the estrous cycle in figure 1B, 5A, and 4C. The percentage of cells in each cluster has been added to each feature plot.

1. For trajectory analysis, which is the root state? according to line 233 and Fig. S3B, the root state should be state 3 in Fig. S3A, is it right? The authors should clarify them. Also for each branch, adding a piechart for each branch will be more informative for the readers.

Given that the monocle pseudotime trajectories of granulosa cells were difficult to interpret, we have removed this analysis from the manuscript.

1. In lines 235-237, the authors demonstrated that "corpus luteum clusters (CL1-3) and the periovulatory cluster were ordered on another branch suggesting this latter branching fate represents a continuum of differentiation states corresponding to luteinization of granulosa cells.", which doesn't sound convincing enough to me because there is significant overlap for cells in CL1 and CL3, not ordering. To provide a more convincing interpretation of the scRNA dataset, I suggest the authors perform RNA velocity analysis and corporate RNA velocity vectors in the trajectory plots, which will greatly help to understand the scRNA dataset.

Unfortunately, the inDROP pipeline was not compatible with RNAvelocity. Other pseudotime analyses gave similar representation of trajectories. We have therefore elected to remove pseudotime analysis from the manuscript.

1. For Fig. 4A, I suggest the authors add a barplot to show the number of different cells for the different stages as for scRNA dataset, it's sometimes common that some cell types were covered by the other in the tSNE plot.

We thank the reviewer for this suggestion, we have now added the percentage of clusters by sample type in every UMAP dimplot.

1. For Fig. 4D, what is the expression level of these genes according to the scRNA seq dataset? A comparison of such information will increase data reliability.

We thank the reviewer for this suggestion, we have added a dotplot representing the level of expression of each gene in the scRNAseq dataset beside the qPCR graphs (now Fig 5D and S5E).

1. How did the authors identify the secreted markers using their scRNA seq dataset? An explanation should be added.

We screened the significantly differentially expressed genes by estrous stage for proteins predicted to be secreted according to UniProt annotation (Table S5), and prioritized genes with the highest fold change. The text has been modified to include this information (lines 320-324).

Reviewer 3

The authors sought to identify transcriptional changes that occur in the various somatic cell populations of the adult mouse ovary during different reproductive states using single-cell RNA sequencing. The ovaries for the analysis were harvested from mice during the four stages of the normal estrus cycle (proestrus, estrus, metestrus and diestrus), from lactating or non-lactating 10 days postpartum mice, and from randomly cycling mice. They identified the major cell subtypes of the adult ovary but focused their analysis on the mesenchyme (stromal and theca) and granulosa cells. They identified novel markers for stromal, theca and granulosa cell subpopulations and validated these by RNA in situ hybridization. They used trajectory analysis to infer differentiation lineages within the stromal and granulosa cell subtypes. Finally, from their data set they identify four secreted factors that could serve as biomarkers for staging estrus cycle progression.

Strengths - This is the first study to profile ovarian somatic gonad cells at different stages of the reproductive cycle.

We thank the reviewer for the positive assessment of our efforts to profile ovarian gonadal somatic cells comprehensively across the estrous cycle

Weaknesses - Enthusiasm for the current manuscript is lessened because it does not employ stateof-the-art scRNA-seq analysis. For example, once general cell populations have been determined by clustering with all cells, it is best to individually re-cluster these cell populations to identify more refined and accurate subpopulations. The PC used for the initial clustering is very useful for distinguishing different general cell populations (e.g. mesenchyme vs. granulosa vs. endothelial) but may not be as useful for distinguishing biologically relevant subpopulations (e.g. stromal subpopulations). Finally, certain cell subpopulations were excluded from the trajectory analysis without justification - specifically, the mitotic and atretic granulosa cells - calling into question what conclusions can be drawn from this analysis.

We have re-analyzed our dataset using the most up to date version of Seurat and R, including reclustering, and changed our dimensional reduction to UMAP. We have also removed pseudotime analysis from the manuscript, given the difficulties in interpreting and representing trajectories.

Author Response

Reviewer #2 (Public Review):

In the report by Brandao A. et al the authors used a zebrafish adult tail fin regeneration model to elucidate the role of metabolic adaptation in cell fate transition and cell proliferation during regeneration with a focus on bone regeneration. Firstly, the authors used transgenic reporter bglap:GFP to label mature osteoblasts and co-immunostaining with a pre-osteoblast marker runx2 to show that within 6 hours post amputation, osteoblasts show signs of dedifferentiation giving rise to pre-osteoblasts that re-enter the cell cycle between 12 - 24 hpa. The authors then use evidence from gene expression changes, metabolomic analysis, pharmacological perturbation experiments, cell proliferation analysis and histological detection of lineage markers to demonstrate that an immediate metabolic switch from OXPHOS to glycolysis precedes blastema formation in amputated tail fin stump. Importantly, blocking glycolysis with 2-DG suppressed mature osteoblast dedifferentiation and proliferation as well as blastema formation which resulted in failure of tail fin regeneration. In summary, this study has shown that a rapid metabolic switch from OXPHOS to glycolysis immediately after tissue damage is important for subsequent bone regeneration, and more specifically the authors provide evidence to show that glycolysis is required for both dedifferentiation and for cell proliferation, both processes are crucial for appropriate blastema formation.

This study established that metabolic switch is an early response to tissue damage and metabolic adaption is key for cellular responses during bone regeneration. Conclusions of this study are well supported by data provided. There are some details of data mentioned in the text should be clarified.

The authors used Microarray transcriptome analysis to demonstrate dynamic gene expression response in 6hpa OBs compared to 0hpa OBs and stated in page 6 line 154 - 159 that at 6hpa, OBs undergo dramatic gene expression changes with 2200 differentially expressed genes, and a set of genes related to energy metabolism was also dramatically altered. However, in supplement figure 1 there was no mention of which genes related to energy metabolism are altered, there is no real data as to what kind of gene expression changes are happening in 6hpa OBs, because DE gene list is not provided. Do the gene expression changes reflect partial dedifferentiation of OBs? The authors should provide more details of their microarray analysis, or at least provide the DE gene list.

We are thankful for the reviewer positive and constructive comments regarding our experimental work and the feedback for the improvement of the manuscript. We just want to point out to the reviewer that the data on Fig 2B relates to major glycolytic enzymes and OXPHOS components retrieved from the Osteoblast ArrayXS and that, as it was mentioned in the methods section (Lines 714-715), we submitted to NCBI Gene Expression Omnibus archive the transcriptome datasets analysed on this study (accession number GSE194385).

Author Response

Reviewer #1 (Public Review):

This manuscript by Kralt et al. provides insight into the enigmatic process of nuclear pore complex (NPC) biogenesis. By taking advantage of their recent development of an isotope labeling/affinity purification/quantitative mass spectrometry pipeline called KARMA, the authors convincingly demonstrate that Brl1, a double pass transmembrane protein, associates with early NPC assembly intermediates but not mature NPCs. A combination of auxin-inducible degradation of Brl1 coupled with an extensive analysis of nup localization (including the use of RITE technology) and cryo-electron tomography provides compelling evidence of the importance of Brl1 in NPC biogenesis at a step that correlates with inner and outer nuclear membrane fusion. Overall, the strengths of the work are that the experiments are innovative, the data are of the highest quality, and the conclusions are on a solid footing.

A potential weakness is that there is already convincing published data that implicates Brl1 as an NPC biogenesis factor. Although there is no doubt that the current work extends these findings to implicate a lumenal amphipathic helix as a key element of Brl1 function, there remains considerable uncertainty over the ultimate mechanism by which the amphipathic helix contributes to inner and outer nuclear membrane fusion.

We thank the reviewer for the overall positive evaluation.

We agree that several recent papers have pointed towards a role for Brl1 in NPC assembly. However, the literature was not conclusive on whether Brl1 directly acts in this process and did not provide any mechanistic insight into the function of Brl1. For example it was suggested that Brl1 might play a role in nuclear transport [1,2] or affect NPC assembly by regulating lipid homeostasis [3,4]. Especially the effect of Brl1 on lipid homeostasis and whether Brl1 indirectly affects NPC assembly by regulating the lipid composition remained controversial [3-5].

In this respect, we would like to highlight that figures 1-3 provide, to our knowledge, the first direct evidence that Brl1 acts as an NPC assembly factor, and our results clearly go beyond previously published data. First, we identify Brl1 as an NPC-interacting factor in an unbiased analysis of a previously published MS dataset [6]. Second, we show that Brl1 has a preference for binding to young, premature NPCs, which means it binds to NPC assembly intermediates but is not part of the mature complex. This is evident from our metabolic labeling assays and also seen in vivo using the RITE approach. Finally, by in-depth characterization of the associated NPC assembly defects and localization of Brl1 we show that (i) the activity of Brl1 is required for membrane fusion during new NPC assembly and (ii) the lipid binding of its luminal AH is essential for this activity. We agree that we do not have any direct evidence that Brl1 displays fusogenic activity, but such a direct proof would likely require biochemical reconstitutions, which are outside the scope of this study. However, our data provide a solid ground for further work in this direction.

Reviewer #2 (Public Review):

In this study, Kralt et al. investigate the mechanisms of nuclear pore complex (NPC) biogenesis in budding yeast, which only relies on interphase NPC assembly. By combining metabolic labeling and microscopy, they show that Brl1, a nuclear envelope (NE) transmembrane protein previously reported to partake in NPC biogenesis, associates with early NPC assembly intermediates. They further report that Brl1 depletion triggers NPC biogenesis defects, as revealed by (i) the characterization of NPC species lacking a subset of nucleoporins in fluorescence microscopy and metabolic labeling assays, and (ii) the detection of NE abnormalities (i.e. herniations) by cryo-electron tomography. In search of the underlying mechanisms, they identify an essential Brl1 motif predicted to fold as an amphipathic helix (AH), which exhibits liposome-binding activity in vitro and supports NE targeting in vivo. Finally, they demonstrate that overexpression of an AH-deficient Brl1 version blocks NPC assembly at a stage likely preceding the fusion of the inner and outer nuclear membranes. Based on these observations, they suggest that Brl1 AH is required for the membrane fusion step in de novo pore biogenesis.

Overall, the conclusions of the authors are supported by the large panel of high-resolution, quantitative data provided. This study provides an unprecedented characterization of Brl1 recruitment and function during the early steps of NPC maturation, although it was already reported that Brl1 contributes to pore assembly (e.g. Zhang et al., 2018). In this view, the involvement of an AH-containing factor in the fusion step represents the main conceptual advance here. Yet, although the featured results support a role for Brl1 AH in membrane fusion, they do not actually prove that Brl1 acts as a fusogen during nuclear pore formation. Additional characterization of Brl1 AH properties, in particular through in vitro experiments, will be required to understand the underlying mechanisms and their relationships with the other NE proteins proposed to contribute to this process (i.e. Brr6/Apq12).

Of note, this work also validates the utilization of the KARMA workflow (metabolic labeling coupled to affinity purification and mass spectrometry), previously published by the same authors, for the characterization of NPC assembly factors. While this methodological framework could thereby prove useful to assess the biogenesis of multiprotein complexes, beyond NPCs, some potential limitations also emerge, as highlighted here by the necessity to control for post-lysis intermixing.

We appreciate the very positive evaluation of our manuscript. We would like to highlight that the main conceptual advance of this study is not only the identification and characterization of the ahBrl1 but also the direct evidence and characterization of Brl1 as an NPC assembly factor (see also the general response to reviewer #1). Investigating in detail the mechanism of membrane fusion and the role of Brl1, Brr6 and Apq12 in this process will unquestionably be very interesting, but is beyond the scope of this study.

Author Response

Reviewer #1 (Public Review):

In this study, Stephan et al. use experimental data to test whether positive interactions between different crop species strengthen over time (generations) when these species are cultivated in association. Even if this has already been investigated in grassland species, we currently lack experimental data on such questions in crops, which makes the study original and with potentially important agronomic applications. To address the question, the authors designed two types of communities: monocultures and mixtures made from seeds collected on plants that evolved in the same community type in the previous two generations (i.e. mixtures from mixture seeds and monocultures from monoculture seeds), and monocultures and mixtures made from seeds collected on plants that evolved in a different community type in the previous two generations (i.e. mixtures from monoculture seeds and monocultures from mixture seeds). They then used multiple sets of indexes to characterize the magnitude and direction of plant-plant interactions in order to compare communities with different evolutionary histories. Interestingly, the experiment is also replicated across two fertilization treatments. At the individual plant level, the results suggest that facilitation increases and competition decreases for plants grown in the same community type as their progenitors compared to plants grown in a different community type as their progenitors. Community-level analysis, however, shows a different picture: both the total yield of the communities and the relative yield of the mixtures are not affected by the coexistence history of their parents, and the results do not provide evidence for increased complementarity between species that have evolved in mixtures in the previous generations. Finally, the authors show that several aboveground traits have lower variation in communities that evolved in the same community type in the previous generations compared to communities that evolved in a similar community type, which shows phenotypic convergence rather than the expected phenotypic divergence in mixtures. They also report differences in trait means, with for example lower mean leaf dry matter content in communities composed of offspring of plants that were grown in the same community type compared to communities composed of offspring of plants that were grown in a different community type.

The study is based on original and high-quality experimental data. The number of species, communities, and replicates is relevant regarding the research question. It is also very nice to have contrasted environments (fertilized vs unfertilized). All these combinations of factors have been replicated over three consecutive years, which also needs to be acknowledged as an impressive experimental effort.

The statistical analysis is rigorous and successfully accounts for design features when testing the effects of interest. My main criticisms concern, by order of importance, the disconnection between the results and the claims of the paper, some weaknesses in the experimental design, and the clarity of the Materials and Methods.

The main hypothesis of the study, which is that higher facilitation/complementarity should occur in mixtures made from plants that evolved in mixtures compared to mixtures made from plants that evolved in monoculture, is not supported by the results. However, the results are presented in such a way that it seems that this hypothesis is verified. For example, the first index which is used by the author (Relative Intensity Index, RII) shows a significant effect on the treatment of interest (coexistence history). However, this index is not the most relevant to capture facilitation or complementarity effects in multi-species communities, notably because it is computed at the single plant level, and only with three plants per species. The Loreau & Hector partitioning (Net Biodiversity >Effect, NBE, partitioned into a Selection Effect, SE, and a Complementarity Effect, CE), which is used a second time, is the gold standard in the field. This is acknowledged by the authors given that they check the validity of RII by measuring its correlation with CE in Fig. S13). Unfortunately, RII and NBE give very different results: the coexistence history of the species has no effect on NBE, and most notably no effect on the CE component. Yet, the authors claim that the coexistence history has an effect on NBE in the fertilized treatment, but we do not have any information supporting the statistical significance of this result (the p-value used to support this claim l. 103 is > 0.05). More generally, several non-significant results are discussed (e.g. l. 100 to 105, l. 136 to 144). The Figures in the main text are also misleading. They show the means ({plus minus} standard error) in the different treatment but do not report statistical significance. Very often, the related boxplots in the Supplementary Information show much fewer differences between the treatments (e.g. Figure 2 vs Fig. S1, Figure 3 vs Figure S3), and the ANOVA tables confirm that these differences are not statistically significant. Overall, the fact that coexistence history has no effect on the total yield, on NBE, and most notably on the CE component, together with the fact that species' traits converge, notably towards taller plants, do not support reduce competition nor higher facilitation in mixtures with a mixture history compared to mixtures with a monoculture history.

The p-values are indicated in the main text along the figures in the Result section. Significance stars were now added and we hope it will be clearer. Furthermore, the discrepancy between RII results and NE/CE was also discussed more extensively in the discussion and we refer to our responses of the general recommendations (1) and (3) by the review editor above. In summary, with our interpretations we tried to stick to the results provided by the data and now provide explanations to reconcile the different results. This does hopefully help to demonstrate that the different results we obtained are not contradictive.

The amount of phenotypic and genetic variation within each species at the beginning of the experiment has not been controlled and reported in the study. It seems that inbred lines were chosen for some species (e.g., wheat, oat, or lentil) which means that there was no genetic variation for these species, whereas landraces or open-pollinated varieties were chosen for others (e.g., coriander or camelina). It thus means that the evolutionary potential of the different species was not the same. It would have been more rigorous to choose either only fixed genotypes for all species (inbred lines or hybrids), which would then have evolved under the sole effect of epigenetic changes, or only mixtures of genotypes for all species (either varietal mixtures or open-pollinated varieties), which would then have evolved under natural selection and changes in gene frequency.

We recognize that the underlying mechanisms remain unclear, as indeed we did not measure the initial amount of standing variation and we could not find seed or populations with the exact genetic variation. This was not done as investigating the potential genetic mechanism was beyond the scope of the study. Therefore, we can only speculate regarding the potential mechanisms, and we have now added an extensive paragraph discussing the possibilities in the discussion (L305-323).

Several aspects of the Materials and Methods could be clarified. It is not clear how the different plots and community types were re-allocated each year. This is important to interpret the results, as soil legacy effects could also affect the outcomes of plant-plant interaction. For example, were mixture plots with a "pure" mixture history grown in the same plot from one year to the other, or were plots reshuffled each year?

Plots were reshuffled each year precisely to avoid soil legacy effects. This was clarified in the methods.

Also, the sowing pattern of the 4-species mixtures is not explained. Was it also alternate rows, as the 2 species mixtures? Was the pattern the same across the different replicates and treatments for a given 4-species mixture?

Since plots were sown with four lines a 50 cm length, in the case of 4-species mixtures, it was for each crop species 1 line. We did not mix species within sowing lines. The pattern across the different replicates and treatments was randomized and is not necessarily the same for a given 4-species mixture. This was now added to the methods.

We do not have information on the sowing densities in mixtures plots (was it simply their monoculture densities divided by the number of species?).

Yes, indeed. We kept the monoculture sowing densities in the mixture plots (i.e. if we planted 10 lentils per line in the monoculture, we also planted 10 lentils per line in the mixture). This was added in the method description.

An important aspect of index computation is also not explained. For example, monoculture yield is used as a reference to compute Relative Yield (RY), and single plant yield is used as a reference to compute RII. There are several ways to compute these reference values, given that there are multiple replicates of monocultures and single plants for a given species. It can be either the value of the closest replicate in the experiment in the same treatment, the average value of all replicates in the same treatment, or a model-derived prediction which accounts for design effects (BLUE or BLUP). In this experiment, monocultures and single plants are also replicated across different evolutionary histories. So, we need to know which type of monoculture plots or single plant plots were used to compute RII and NBE.

This was specified in the Methods and discussed in the response to the general comments. In short, we always used the average value over the replicates with the same treatment combination, e.g. a single plant with a monoculture history in unfertilised plots as a reference for monoculture history treatments in unfertilised plots.

Reviewer #2 (Public Review):

The paper offers a very novel experimental framework for assessing how coexistence history could influence intercropping success in agricultural systems. The authors do a very nice job combining the science from multiple fields into a coherent and useful framework. Based on this framework we should conclude that growing crops in polyculture fields for multiple generations will increase the benefits of intercropping for growing food.

However, on the ecological side, there are some weaknesses that need to be addressed: 1. The introduction and discussion need more context for how co-occurrence can lead to more facilitation. I see how co-occurrence could lead to trait displacement and less niche overlap, so less competition. But what is the facilitation part of this? The introduction doesn’t introduce any potential mechanisms for this despite many indications that facilitation could also change as a result of coexistence history.

We included a paragraph covering the evolution of facilitation in the introduction (L49-57).

1. The authors should think carefully about their use of net effects, RII_facilitation, and RII_competition. It appears to me as though all three are measuring net effects but in some cases facilitation > competition and in other cases competition > facilitation. Even though that’s true, it doesn’t mean that the indices aren’t still measuring net effects. Given that, the authors should temper that language and consider reinterpreting some of their data.

Indeed, as our RII measures net effects, for more clarity, we decided to skip this distinction between RII facilitation and RII competition – thereby also acknowledging concerns raised by reviewers 1 and 3. Furthermore, we rephrased our statements to make clear that what we measure is the outcome of plant-plant interactions and that we could not always distinguish between increased facilitation and/or reduced competition.

1. The authors should also give careful consideration to the relative balance of inter vs. intraspecific competition. Many (if not all) of these trends could be indicative of stronger intraspecific competition than interspecific competition. This will need to be considered very carefully.

We agree in that increased complementarity with increasing diversity is per se due to stronger intraspecific competition than interspecific competition, and consequently higher benefits of alleviation of the most important source of competition. This is the underlying hypothesis of all BEF studies and actually the reason why we tackled BEF in this study by means of plant-plant interaction metrics. We clarified this in the introduction (L96-99).

1. Have the authors considered separating their data into plots with and without legumes? The strong selection effects with co-occurrence history would also support this. Nitrogen enrichment is one of the most heavily studied facilitation mechanisms and thus this separation might help give insight into the mechanisms operating here.

We tried to separate effects with and without legumes, but since all our 4-species mixtures necessarily included a legume, the plots without legumes were only monocultures and 2-species mixtures, and therefore it did not give a representative picture of the experimental design.

1. Overall, a lack of clarity of underlying mechanisms is the greatest weakness of the paper.

We recognize that the underlying mechanisms remain unclear, as indeed we did not measure the initial amount of standing variation and we could not find seed or populations with the exact same genetic variation. This was not done as investigating the potential genetic mechanism was not the goal of the study. Therefore, we can only speculate regarding the potential mechanisms, and we have now added an extensive paragraph discussing the possibilities in the discussion (L305-323).

Reviewer #3 (Public Review):

This work investigates the effects of growing annual crops for two generations in the same or a different social environment (coexistence history being single plant, monoculture, mixture of species) on measures of competition and yield. This is a very interesting and timely topic; diversification in agriculture is a promising means to help reduce the global decline of biodiversity. The experimental setup appears to be sound and the experiment is carefully executed (though this is not my area of expertise). The authors conclude that growing plants in the same community as their parents did reduces competition.

However, I am not convinced by the interpretation of the results. Particularly the results for competition versus overall yield are in conflict. This discrepancy is not properly discussed and is largely ignored in the conclusions. Hence, I doubt whether the results support the conclusions.

We would like to thank the reviewer for the constructive feedback and the appreciation of our work. Regarding the potentially conflicting findings mentioned by the reviewer here, we would like to refer to our previous statement in response to the review editor, in particular response (1) and (3), where we show that these results are not necessarily conflicting.

My most important comment relates to the discrepancy between results for total yield (Figure 3b) versus those for competition (Figure 2a) and for net biodiversity effect (Figure 3a). Results for all those measures are based on yield records. Figure 2a and 3b (panel fertilizer) show clearly that plants that have the same coexistence history as the tested plants outperform those having a different co-existence history. Figure 3b, however, shows no effect of coexistence history on yield; total yield for Same and Different do not differ. How to reconcile these results? Remarkably, this discrepancy is not discussed at all; the discussion largely ignores the absence of an effect on total yield.

This discrepancy is now discussed in the discussion (L230-245), which was largely rephrased to take into account the comments. The discrepancy between the response of plant-plant interactions and the response of net biodiversity effects to coexistence history can stem from various reasons. First, net biodiversity effects are driven both by complementarity and selection effects (6); therefore, a reduction in competition does not necessarily lead to an increase in net biodiversity effects, as this can be compensated by concurrent changes in selection effects. Changes in RII should however correlate with complementarity effects, which they do in our study (Fig. S11, p-value = 0.033), indicating that reduced competition and/or increased facilitation correlates with higher complementarity effects. As mentioned in the response to the general comments, the reference for RII (single plant) is not the same as for community level measures such as NE (monoculture). This can also explain why coexistence history affects RII but not NE (see how we calculate this extra RII_monoculture in the main response). Finally, our RII calculations and net biodiversity effects also take into account the baseline effect of coexistence history on the reference plant or community (i.e. single plant for RII, monoculture for net effects). This allows to explicitly distinguish the effects of coexistence history on the interactions, independently of the baseline effect on plant performance overall (35), and can explain why the effect of coexistence history on relative metrics (such as RII) does not appear in absolute metrics (such as total yield). We also suggest that the limited timeframe of this study – two generations – might be the reason for the lack of more significant changes in total yield.

Related to the previous comment, the title includes the phrase “reduces competition”. In the manuscript, competition is derived from effects on yield. Still, there is no benefit of the same coexistence history for total yield. This is somewhat misleading.

See response to main comments.

A second important comment relates to the absence of results from the second year. The Methods section explicitly states that the comparisons made in year 3 (as shown in Figure 2) were also made in the second year (2018; L350-358). However, no results are presented. Why are those results excluded?

We collected only partial data after 1 year, as this was considered as an intermediate stage, where adaptation was less likely to give significant results. Notably, we put fewer efforts into collecting data at the individual-level and reduced the number of traits measured, which prevented us from having a full picture of the response of plant-plant interactions as well as of the trait space. Therefore, we decided to not present these partial pieces of data in the study.

A third comment relates to the distinction between competition and facilitation (Equations 3 and 4, and corresponding results), which is artificial and not very meaningful in my opinion. Since RII will never be precisely equal to zero (i.e., the RII=0 category is empty), an increase (decrease) in facilitation must go together with a decrease (increase) in competition, and vice versa. This must be the case since the total of both categories must add up to the number of comparisons made. In other words, if we have a total of N objects, being either apples or pears, then, if we have fewer apples, we must have more pears. (hence, L93-94 is a tautology). I suggest dropping this distinction from the manuscript.

The decomposition between competition and facilitation was dropped (as already mentioned above).

The Discussion seems to ignore some of the results that don’t seem to match the “desired” outcome. For example, L178 speaks about niche differentiation as if this was found, but it was not. Same for L200. Similarly, L181 speaks about “the yield benefit”, which was not there.

We tried to reformulate the discussion and notably to emphasize that we find some clues for niche differentiation (light use, RII) but this did not consistently match other measures (traits, CE).

While the manuscript is well written with respect to the language, it is not always easy to follow and absorb. This is partly because the number of traits is large. A table with the traits could help. Also, the writing could be improved to help the reader get the message. For example, when showing results in Figure 2, it could be mentioned from the start that these are relative to single plants, whereas those in Figure 3a are relative to monoculture. This can be found in the methods but should be clear from the Results as well.

This was clarified and specified in both the main text of the results and in the figure legends.

Author Response

Reviewer 3

This is work by an internationally recognized group with strong expertise in sophisticated single-molecule microscopy assays in cells. They present here a single-molecule fluorescence-based assay for proximity in the nanometer range.

It has long been reported that cyanine dyes such as Cy3, Cy5 and derivatives such as AF555, AF647 can undergo a photoswitching mechanism by which the shorter wavelength dye when being excited can switch the longer wavelength dye which is in a dark state back into the bright state. And it has furthermore been reported that this switching mechanism is not based on FRET, as the distance requirement is more stringent (up to ~ 2 nm). However, this mechanism has not been fully explored for the investigation of molecular interactions yet.

The authors in the present work present a similar mechanism for a different class of rhodamine-based fluorophores, specifically JF549 and JFX650. They describe the discovery of this mechanism in dual-color labeling of a pentameric protein and initial characterization to distinguish it from UV-light-mediated recovery from a pumped dark state as reported for (d)STORM-like measurements. They extend their observation to TMR, JF529 as lower wavelength "senders" and JF646 and JFX646 as longer wavelength "receivers" that can become reactivated into the ground state upon illumination of a nearby "sender". The authors then test activation pulse length and distance dependence and find that longer pulses lead to more recovery and that PAPA of JF549/JFX650 has unlike previously observed for the Cy3/Cy5 pair a smaller distance dependence than FRET of the same fluorophore pair. The authors then move on to use both the UV-light mediated direct reactivation "DR" and proximityassisted photoactivation "PAPA" to activate different molecules that are either double-labeled for PAPA or singly labeled with JFX650 for DR. They succeeded in four different cases to identify clear population shifts to distinguish molecules of different mobility.

Overall, I think the authors made an interesting discovery and characterizing this previously poorly characterised interaction for cellular single-molecule experiments is certainly an important effort. The authors make an honest and quite complete effort to work out the practical details of this interaction and designed experiments that convincingly highlight the basic capabilities this technique offers to the detection of verified interactions and the mobility of interacting molecules in cells.

The weakness is that these capabilities do not seem to be as clear-cut as the reviewer hoped for when starting to read this manuscript. It remains unclear to this reviewer, to what extant PAPA molecules can be separated from DR molecules. In all but the last diffusion experiment(s) in Figure 4, PAPA molecules seem to be significantly perturbed by DR molecules, casting doubt on the usefulness in real experiments. Similarly, in Figure 5, a difference is seen but does not allow for quantification. This certainly is not the case for other methods of sensing as well, but maybe the authors could more specifically compare their efforts and the dynamic range to other sensors for example in Figure 5? This would make it easier for the reader to make up their mind if the assay is worthwhile adopting for their system.

We agree that a problem with PAPA at present is that although PAPA trajectories are significantly enriched for double-labeled complexes, they are still “contaminated” with singlelabeled molecules. As we described in the Discussion (and as pointed out by Reviewer 1), we think that one major contribution to this background arises from chance proximity of sender and receiver molecules independent of direct physical interaction. Additionally, some background is expected from continual spontaneous (a.k.a. “thermal”) reactivation of molecules from the dark state.

In response to the reviewers’ comments, we have tried to quantify more precisely how much PAPA enriches for one population over another by fitting the diffusion spectra of 2-component mixtures to linear combinations of the corresponding individual components (Figure 4–figure supplement 4). We estimate that the fold enrichment of double-labeled molecules ranged from 3.7 to 37-fold between different 2-component mixtures.

We fully agree that it is critical that researchers who use PAPA be aware of its limitations, so that they do not fallaciously assume that all green-reactivated localizations are protein complexes. To avoid committing a bait-and-switch against our readers, we now state explicitly in the Introduction that PAPA in its current form enriches for complexes but does not provide perfect selectivity. In Appendix 2, we now discuss the problem of background reactivation in more detail and outline what we think will be required to correct quantitatively for this background. Though we believe that such corrections will ultimately be possible, at least in some cases, figuring out how to do this rigorously will require substantial additional development of experimental and computational methods, which we hope the editor and reviewers agree is beyond the scope of the current paper.

At the end of Appendix 2, we briefly mention another technical problem that we have noticed with SNAP ligand background staining. While this background was negligible for the experiments described in this paper, which involved highly expressed SNAPf transgenes, it may pose a more significant problem for SNAPf-tagged proteins with lower expression levels. We think it is worth mentioning this problem to make readers aware of it and hopefully to motivate the development of better orthogonal pairs of self-labeling tags.

While there are obviously limitations to PAPA, we think this should not overshadow the fact we have identified a novel photophysical property of commonly used fluorophores and harnessed it to detect molecular interactions in live cells. Our initial proof-of-concept study provides a foot in the door of this new biophysical approach, which we and others will continue to refine. Immediate applications of PAPA could include disambiguation of peak assignments in complex diffusion spectra, confirmation of proposed interactions between proteins (and subsequent investigations into the molecular mechanisms supporting such interactions), or integration into SPT-based high-throughput screening (https://www.eikontx.com/technology) to provide a useful additional readout for each experimental condition.

Author Response:

Reviewer #1 (Public Review):

The authors show that the unmitigated generation interval of the original variant of SARS-CoV-2 is longer than originally thought. They argue that in the absence of interventions that limit transmission late in the course of infection, the fraction of transmission events that occur before symptom onset would be considerably lower, and the fraction of transmission events occurring 10 days or more after infection of the index case would be substantially higher.

These findings improve our ability to accurately estimate the basic reproductive number (R0), to evaluate quarantine and isolation policies, and to model counterfactual intervention-free scenarios. Many applied analyses rely on accurate generation interval estimates. To head off confusion, it would be helpful if the authors could provide more comprehensive guidance about which applied analyses should be informed by the unmitigated generation interval, or the observed generation interval. (E.g. the unmitigated interval is useful for quarantine and isolation policies, but would we ever want to use the unmitigated interval to estimate R?).

The unmitigated generation-interval should be used for estimation of the R0 of the initial epidemic phase, but not for the R(t) of the current epidemics. Estimation of R(t) must account for changes in generation-interval distributions caused by the invasion of new variants and changes in behavior. When analyzing policies of quarantine, isolation or contact tracing, the unmitigated interval should also be adopted to account for late transmissions.

We added few sentences at the end of our introduction to clarify this point:

“The estimated unmitigated generation-interval distribution could be adopted for answering questions about quarantine and isolation policy, as well as for estimating the original R0 at the initial spread in China. However, estimation of instantaneous R(t) should account for changes in generation-interval distributions, reflecting mitigation effects and the current variant.”

The analysis estimates a longer generation interval after accounting for three main sources of bias or error that are common in other analyses: 1. Recently infected individuals are intrinsically overrepresented in data on a growing epidemic. Thus, shorter incubation periods and forward serial intervals are more likely to be observed, even in the absence of interventions. This analysis adjusts for these dynamical biases. 2. Interventions or behavioral changes can prevent transmission late in the course of infection. This can shorten the generation and serial intervals over the course of an epidemic. This analysis focuses specifically on transmission pairs observed very early, before the adoption of interventions. 3. The incubation period and generation interval should be correlated - infectors that progress relatively quickly to symptoms should also become infectious sooner (symptom onset occurs near the peak of viral titers). Most existing analyses assume these intervals are uncorrelated, but this analysis accounts for their correlation.

Overall, the conclusions seem reasonable and well-supported. The observation that the generation interval decreases over the course of an epidemic is also consistent with existing studies that show the serial interval has similarly decreased over time. But given the implications of the findings, I hope the authors can address a few questions about potential additional sources of bias:

1. It is somewhat reassuring that the generation interval decreases relatively smoothly as the cutoff date increases (Fig. S6), but it would be helpful if the authors address the potential impact of ascertainment biases. One of the main reasons that the authors estimate a shorter generation interval is that they define January 17th, early in the outbreak before interventions and behavioral changes had taken place, as the cutoff point for the infector's date of symptom onset. This cutoff eliminates biases from interventions, but it also severely limits the size of the transmission-pair dataset (Fig. S3), and focusing on this very early subset of cases may increase the influence of ascertainment bias. Prior to January 17th, should we expect observed transmission pairs to involve more severe cases on average? And is the unmitigated generation interval correlated with case severity?

We thank the reviewer for identifying a source of possible bias that we overlooked. Following the comment we performed a new sensitivity analysis for the inclusion of the severe cases, summarized in Appendix 1—figure 11.

Severity of the cases was reported only in Ali et al.’s data, for some of the individuals. In these cases, individuals are divided into one of three conditions: mild, severe (non-fatal) and death. As non-mild cases represent a small fraction of the dataset, we combine them into one category, which we denote as severe.

Severe cases (including deaths) were overrepresented in the period prior to January 17, with 8 out of 77 cases, compared to 18 out of 745 in the period of January 18-31. The effect of inclusion of severe cases was analyzed by comparing the means of the estimated generation-interval distribution, separately for the two periods in question, using the inference framework with 30 bootstrapping runs. For the earlier period, the estimated means were compared between the dataset with or without the severe cases. For the later period, we also consider the “enriched” dataset, in which severe cases are oversampled for each bootstrap such that the proportion of severe cases matches that during the earlier period (10%). In both cases we see that the effect on the estimated mean generation interval is small.

1. The analysis assumes the incubation period follows a fixed distribution, whose parameterization comes from a meta-analysis of previously estimated incubation periods. But p.5 discusses the idea that observed incubation periods are affected by the same dynamical biases as forward serial intervals, "For example, when the incidence of infection is increasing exponentially, individuals are more likely to have been infected recently. Therefore, a cohort of infectors that developed symptoms at the same time will have shorter incubation periods than their infectees on average, which will, in turn, affect the shape of the forward serial-interval distribution." Has the incubation period been adjusted for these dynamical biases, or should it be?

In our analysis we use the incubation period distribution from Xin et al. 2021 which already considers the backward bias caused by the expanding epidemic with the corrected growth rate of 0.1/d. Xin et al. showed in their meta-analysis that the mean incubation period reported by the various sources changed according to the dates used by the source. Incubation periods prior to the peak of the epidemic in China were lower than ones from after the peak, in a manner that coincided with the backward correction they performed (using a similar derivation to that suggested by Park et al. 2021). Accordingly, the distribution of incubation period they report is the intrinsic incubation period, after correction for the growth rate of the initial spread in China. We added two sentences in our methods section to clarify this point:

“In their meta-analysis, Xin et al. found an increase of the incubation period following the introduction of interventions in China, matching the theoretical framework shown above. Their inferred incubation period distribution includes a correction for the growth rate of the early spread, accordingly.”

Furthermore, we perform a sensitivity analysis for the shape of the incubation period distribution, and show that it has a minor effect on our conclusions (Appendix 1—figure 10).

1. It appears that correlation parameter estimates co-vary with estimates of the mean generation interval (Fig. S6; S13b). Are the authors confident that the correlation parameter is identifiable? How much would the median generation interval estimate in the main analysis change if the correlation parameter had been fixed to 0 (which isn't realistic) or to 0.5 (which might be plausible)?

As the reviewer pointed out, the correlation parameter estimates co-vary with estimates of the mean generation interval. We further analyzed this relation following the comment. The analysis is summarized in supplemental figures S19-20.

We first examine the relation between the mean generation interval and the correlation parameter based on the uncertainty estimates, consisting of 1000 bootstrap runs. Appendix 1—figure 12 shows a joint bivariate scatter plot of the parameters, together with contours of equal probability. As can be seen there is a connection between the parameters. The estimates centered around the maximum likelihood estimate with correlation parameter of 0.75 and mean generation interval of 9.7 days. The confidence interval for the correlation parameter of 0.45-0.95 corresponds to mean generation intervals in the range of 8-11 days, supporting the conclusion of this study.

Next, we reanalyzed the dataset while fixing the correlation parameter, as suggested by the reviewer. Appendix 1—figure 13 shows the estimated mean generation interval for fixed correlation parameters with values of 0, 0.25, 0.5, 0.75, 0.9. For each fixed correlation parameter 100 bootstrapping runs. As can be seen, the results reflect the same connection that can be seen in Appendix 1—figure 12, with probable values in the range of 8-11 days, for correlation parameters in the range of 0.5-0.9. Assuming no correlation would cause underestimation of the mean generation interval match previous literature (Hart, Maini, and Thompson 2021; Park et al. 2022).

Reviewer #2 (Public Review):

There have been several estimates of the generation time and serial interval published for SARS-CoV-2, but as the authors note, estimates can be subject to biases including shifted event timing depending on the phase of the epidemic, correlation in characteristics between infector and infectee, and impact of control measures on truncating potential infectiousness. This study, therefore, has several strengths. It first collates data on transmission events from the earliest phase of the COVID-19 pandemic, then makes adjustments for these potential biases to estimate the generation time in absence of control measures, and finally discusses implications for transmission.

Given many subsequent aspects of the COVID-19 pandemic have been defined relative to earlier phases (e.g. relative transmissibility of variants, relative duration of infectiousness), understanding the baseline characteristics of the infection is crucial. I thought this paper makes a useful contribution to this understanding, generating adjusted estimates for infectiousness (which is longer than previous estimates) and corresponding values for the reproduction number (which is remarkably similar to earlier estimates, presumably because of the different sources of bias in the growth rate and generation time distribution somehow end up canceling each other out).

However, there are some weaknesses at present. The study correctly flags several potential sources of bias in estimates, but in making adjustments uses estimates from the literature that themselves could suffer from these biases, e.g. the distribution of incubation period from a 2021 meta-analysis. Although the authors conduct some sensitivity analysis it would be worth including some more explicit consideration of whether they would expect any underlying bias to propagate through their calculations. The authors also conduct some sensitivity analysis around the underlying data (e.g. ordering of transmission pairs), but again it would be useful to know whether there could be systematic biases in these early data. Specifically, the paper references Tsang et al (2020), which highlighted variability in early case definitions - is it possible that early generation times are estimated to be longer because intermediate cases in the transmission chain were more likely to go undetected than later in the epidemic?

We recognize the potential biases in the transmission pairs data. We therefore developed an extensive framework of sensitivity analyses for identifying biases that could substantially affect the results. In the results section and figure 5, we show that the main study result, that the unmitigated generation-interval distribution is longer than previously estimated, is robust to reasonable amounts of ascertainment bias. We discuss this point at length and have added several supplemental figures to support this claim.

As reviewer #3 mentioned, we conducted a sensitivity analysis for the inclusion of the longest serial intervals, to investigate possible effects of missing links in the longest transmission pairs. We also discuss why we think it’s not necessary to explicitly model the short intervals that may be unobserved due to missing links.

“Second, we considered the possibility that long serial intervals may be caused by omission of intermediate infections in multiple chains of transmission, which in turn would lead to overestimation of the mean serial and generation intervals. Thus, we refit our model after removing long serial intervals from the data (by varying the maximum serial interval between 14 and 24 days). We also considered “splitting” these intervals into smaller intervals, but decided this was unnecessarily complex, since several choices would need to be made, and the effects would likely be small compared to the effect of the choice of maximum, since the distribution of the resulting split intervals would not differ sharply from that of the remaining observed intervals in most cases.”

We added to the discussion text regarding the effect of possible bias in the dataset, explicitly specifying the ascertainment bias.

“Our analysis relies on datasets of transmission pairs gathered from previously published studies and thus has several limitations that are difficult to correct for. Transmission pairs data can be prone to incorrect identification of transmission pairs, including the direction of transmission. In particular, presymptomatic transmission can cause infectors to report symptoms after their infectees, making it difficult to identify who infected whom. Data from the early outbreak might also be sensitive to ascertainment and reporting biases which could lead to missing links in transmission pairs, causing serial intervals to appear longer (For example, people who transmit asymptomatically might not be identified). Moreover, when multiple potential infectors are present, an individual who developed symptoms close to when the infectee became infected is more likely to be identified as the infector. These biases might increase the estimated correlation of the incubation period and the period of infectiousness. We have tried to account for these biases by using a bootstrapping approach, in which some data points are omitted in each bootstrap sample. The relatively narrow ranges of uncertainty suggest that the results are not very sensitive to specific transmission pairs data points being included in the analysis. We also performed a sensitivity analysis to address several potential biases such as the duration of the unmitigated transmission period, the inclusion of long serial intervals in the dataset, and the incorrect ordering of transmission pairs (see Methods). The sensitivity analysis shows that although these biases could decrease the inferred mean generation interval, our main conclusions about the long unmitigated generation intervals (high median length and substantial residual transmission after 14 days) remained robust (Figure 5).”

It would also be helpful to have some clarifications about methodology, particularly in how the main results about generation time are subsequently analyzed. For example, estimates such as the conversion of generation time to R0 and VOC scalings are described very briefly, so it is currently unclear exactly how these calculations are being performed.

Following the reviewer comments we made edits to the Methods section in order to make it more readable and clearer. We added subheadings for the various sections. Moreover, we added a section explaining the derivation of the basic reproduction number and clarified the section regarding the VOCs extrapolations.

We made some edits to the methods section in order to make it more accessible and clear, for example, we added subheadings for the various sections, added a section explaining the derivation of the basic reproduction number, and clarified the section regarding the VOCs extrapolations.

Reviewer #3 (Public Review):

Sender & Bar-On et al. perform robust analyses of early SARS-CoV-2 line list data from China to estimate the intrinsic generation interval in the absence of interventions. This is an important topic, as most SARS-CoV-2 data are from periods when transmission-reducing interventions are in place, which will lead to underestimation of the potential infectious period.

The authors highlight two shortcomings in previous approaches. First, the distribution of 'observed' serial intervals (the time between symptom onset in the infector and symptom onset in the infectee) depends not only on the timeline of each infector's infection, but also the epidemic growth rate, which weights the proportion of observed short vs. long serial intervals. The authors argue that by accounting for this weighting, more accurate estimates of the intrinsic generation interval - the metric on which isolation policies are based - can be obtained. Second, the authors find that the original SARS-CoV-2 generation interval distribution has both a higher mean and longer tail than previous estimates when using only data prior to the introduction of interventions. Finally, the authors use publicly available data on viral load trajectories to extrapolate their estimates to other SARS-CoV-2 variants, finding that alpha, delta, and omicron may have shorter generation intervals than original SARS-CoV-2. These findings are important, as case isolation policies are based on assumptions for how long individuals remain infectious. More broadly, these methods will be important for future work to correctly estimate generation intervals in other outbreaks.

The conclusions are well supported by the data, and a suite of sensitivity analyses give confidence that the findings are robust to deviations from many of the key assumptions. The code is well documented and publicly available, and thus the findings are easily reproducible. Key strengths of the paper include the clarity and rigor of the modeling methods, and the exhaustive consideration of potential biases and corresponding sensitivity analyses - it is very difficult to think of potential biases that the authors have not already considered! I think this is a well-written and well-executed study. The work is likely to be impactful for reconsidering SARS-CoV-2 isolation policies and revisiting generation interval estimates from other data sources. I also expect this to be a key reference and method for future studies estimating the generation interval.

I have some minor comments on potential weaknesses and interpretation:

1. Uncertainty in early generation interval estimates. One of the conclusions is that the estimated mean generation interval is longer than the observed mean serial interval. However, this conclusion does not seem justified given that the observed mean serial interval (9.1 days) is well within the 95% CI of 8.3-11.2 days for the mean generation interval. The confidence intervals for the serial interval in figure 2 are also wide for pre-Jan 17th (though presumably these would be reduced if all pre-Jan 17th serial intervals were combined). Further, only 77 of the ~1000 transmission pairs are actually from pre-January 17th. The actual sample size used for these estimates is much smaller than suggested by Figure S1 and thus this should be made clear. Therefore, although the intuition for why observed serial intervals may differ from the generation interval is correct, I do not think that the data alone demonstrate this. A related issue is on ascertainment bias - could the early serial interval data be biased longer because ascertainment is initially poor and thus more intermediate infectors are missed? The authors consider removing particularly long serial intervals to try and account for this, but that does not deal with e.g. chains of multiple short serial intervals being incorrectly recorded as a single long serial interval (but still within 16 days).

We agree with the reviewer that due the large uncertainty we cannot deduce that the mean generation interval is longer than the mean serial interval. We changed the phrasing to emphasize this statement is supported by mathematical theory.

“We note that our estimated mean generation-interval is longer than the observed mean serial-interval (9.1 days) of the period in question. This is supported by the theory (Park et al. 2021) of the dynamical effects of the epidemic -- in contrast to the common assumption that the mean generation and serial intervals are identical. During the exponential growth phase, the mean incubation period of the infectors is expected to be shorter than the mean incubation period of the infectee - this effect causes the mean forward serial interval to become longer than the mean forward generation interval of the cohorts that developed symptoms during the study period. However, these cohorts of infectors with short incubation periods will also have short forward generation (and therefore serial) intervals due to their correlations. When the latter effect is stronger, the mean forward serial interval becomes shorter than the mean intrinsic generation interval, as these findings suggest.“

Following the comment, we added to Figure S1 the filtering according to date, to reflect the true sample size we use for the main analysis (We renamed it: Appendix 1—figure 1).

We recognize the potential biases in the transmission pairs data. We therefore developed an extensive framework of sensitivity analyses for identifying biases that could substantially affect the results. In the results section and figure 5, we show that the main study result, that the unmitigated generation-interval distribution is longer than previously estimated, is robust to reasonable amounts of ascertainment bias. We discuss this point at length and have added several supplemental figures to support this claim.

As reviewer #3 mentioned, we conducted a sensitivity analysis for the inclusion of the longest serial intervals, to investigate possible effects of missing links in the longest transmission pairs. We also discuss why we think it’s not necessary to explicitly model the short intervals that may be unobserved due to missing links.

“Second, we considered the possibility that long serial intervals may be caused by omission of intermediate infections in multiple chains of transmission, which in turn would lead to overestimation of the mean serial and generation intervals. Thus, we refit our model after removing long serial intervals from the data (by varying the maximum serial interval between 14 and 24 days). We also considered “splitting” these intervals into smaller intervals, but decided this was unnecessarily complex, since several choices would need to be made, and the effects would likely be small compared to the effect of the choice of maximum, since the distribution of the resulting split intervals would not differ sharply from that of the remaining observed intervals in most cases.”

We added to the discussion text regarding the effect of possible bias in the dataset, explicitly specifying the ascertainment bias.

“Our analysis relies on datasets of transmission pairs gathered from previously published studies and thus has several limitations that are difficult to correct for. Transmission pairs data can be prone to incorrect identification of transmission pairs, including the direction of transmission. In particular, presymptomatic transmission can cause infectors to report symptoms after their infectees, making it difficult to identify who infected whom. Data from the early outbreak might also be sensitive to ascertainment and reporting biases which could lead to missing links in transmission pairs, causing serial intervals to appear longer (For example, people who transmit asymptomatically might not be identified). Moreover, when multiple potential infectors are present, an individual who developed symptoms close to when the infectee became infected is more likely to be identified as the infector. These biases might increase the estimated correlation of the incubation period and the period of infectiousness. We have tried to account for these biases by using a bootstrapping approach, in which some data points are omitted in each bootstrap sample. The relatively narrow ranges of uncertainty suggest that the results are not very sensitive to specific transmission pairs data points being included in the analysis. We also performed a sensitivity analysis to address several potential biases such as the duration of the unmitigated transmission period, the inclusion of long serial intervals in the dataset, and the incorrect ordering of transmission pairs (see Methods). The sensitivity analysis shows that although these biases could decrease the inferred mean generation interval, our main conclusions about the long unmitigated generation intervals (high median length and substantial residual transmission after 14 days) remained robust (Figure 5).”

1. Frailty of using viral loads to extrapolate generation intervals. The authors take the observation that variants of concern demonstrate faster viral clearance on average to estimate shorter generation intervals for alpha, delta, and omicron. The authors rightly point out in the discussion that using viral load as a proxy for infectiousness has many limitations. I would emphasize even further that it is very difficult to extrapolate from viral load data in this way, as infectiousness appears to vary far more between variants than can be explained by duration positive or peak viral load. Other factors are potentially at play, such as compartmentalization in the respiratory tract, aerosolization, receptor binding, immunity, etc. Further, there is considerable individual-level variation in viral trajectories and thus the use of a population-mean model overlooks a key component of SARS-CoV-2 infection dynamics. An important reference, which came out recently and thus makes sense to have been missed from the initial submission, is Puhach et al. Nature Medicine 2022 https://doi.org/10.1038/s41591-022-01816-0.

We agree with the reviewer about the frailty of using viral loads to extrapolate generation intervals. We therefore expanded our discussion of the limitation of using viral load data for inferring infectiousness including many of the points mentioned by the reviewer. We use viral load data in the most minimal way to try to enable some discussion of new VOC, and try to emphasize the needed caution.

Viral load trajectories data have potential for informing estimates of the infectiousness profile. However the relationship between viral load, culture positivity, symptom onset, and infectivity is complex and not well characterized. Due to this limitation we tried to use viral loads in a more limited way, extrapolating our results to variants of concerns (which lack unmitigated transmission data). Following the comment, we added a detailed discussion of the limitations of using viral loads as a proxy for infectiousness, including the variation of viral loads across individuals. We also added supplementary figures (Figure 6—figure supplements 1-2) to show the possible effect of an individual's viral loads in relation to the infectiousness and for comparison with new viral load and culture results (Chu et al. 2022; Killingley et al. 2022). As the viral load trajectories data for the different VOC is given only as a function of time from the onset of symptoms, it is not possible to directly link it to the fraction of transmission post 14 days from infection. We made changes to Figure 6 to clarify the possible connection of viral load with the TOST (time from symptoms onset to transmission) distribution and the resulting extrapolation to the unmitigated generation-interval distributions.

“SARS-CoV-2 viral load trajectories serve an important role in understanding the dynamics of the disease and modeling its infectiousness (Quilty et al. 2021; Cleary et al. 2021). Indeed, the general shapes of the mean viral load trajectories and culture positivity, based on longitudinal studies, are comparable with our estimated unmitigated infectiousness profile (Figure 6—figure supplements 1-2, comparison with (Chu et al. 2022; Killingley et al. 2022; Kissler et al. 2021)). However, the nature of the relationship between viral load, culture positivity, symptom onset, and real-world infectivity is complex and not well characterized. Therefore, the ability to infer infectiousness from viral load data is very limited, especially near the tail of infectiousness, several days following symptom onset and peak viral loads. Viral load models are usually made to fit the measurements during an initial exponential clearance phase and in many cases miss a later slow decay (Kissler et al. 2021). Furthermore, there is considerable individual-level variation in viral trajectories that isn’t accounted for in population-mean models (Kissler et al. 2021; Singanayagam et al. 2021). Other factors limiting the ability to compare generation-interval estimates with viral loads models are the variability of the incubation periods and its relation to the timing of the peak of the viral loads, and the great uncertainty and apparent non-linearity of the relation between viral loads and culture positivity (Jaafar et al. 2021; Jones et al. 2021). Due to these caveats and in order to avoid over interpretation of viral load data, we restrict our extrapolation of new VOCs’ infectiousness to a single parameter characterizing the viral duration of clearance.”

We also edited another paragraph in the discussion:

“Our extrapolations are necessarily crude given the complex relationship between viral load, symptomaticity, and infectiousness discussed above. Moreover, compartmentalization in the respiratory tract, aerosolization, receptor binding affinity, and immune history can also play important roles in determining the infectiousness profiles of SARS-CoV-2 variants (Puhach et al. ). ”

1. Lack of validation with other datasets This study hinges on data from a single setting in a short window of time. Although the data are from multiple publications, the fact that so many reported the same transmission pair data demonstrates that these are overlapping datasets. As the authors note, there are potential biases e.g., ascertainment rates and behavioral changes which will impact the generation interval estimates. Thus, generalizability to other settings is limited.

We agree with the reviewer that the dataset used in our study is limited, and consists of overlapping transmission pairs. We perform some analysis of the possible bias caused by inclusion of each dataset, as can be seen in Appendix 1—figure 4.

The best validation would have been a comparison with another independent dataset from the early spread of the epidemic, but no such dataset exists. We added a sentence to the discussion to emphasize this point.

“Due to the nature of early spread of a new unknown disease it is nearly impossible to find two completely unrelated datasets from the period prior to mitigation, limiting the ability of further validation of the current results.”

1. The impact of epidemic dynamics on infector vs. infectee serial intervals. It took me a long time to get my head around the assertion that the forward serial interval distribution will be longer during epidemic growth due to the overrepresentation of short incubation periods among infectors relative to infectees. A supplementary figure, similar to the way Figure 1 is laid out, to illustrate this concept may go a long way to aid the reader's understanding.

We added an explanation to the paragraph in order to make it clearer:

“A cohort of individuals that develop symptoms on a given day is a sample of all individuals who have been previously infected. When the incidence of infection is increasing, recently infected individuals represent a bigger fraction of this population and thus are over-represented in this cohort. Therefore, we are more likely to encounter infected individuals with a short incubation period in this cohort compared to an unbiased sample. The forward serial-interval is calculated for a cohort of infectors who developed symptoms at the same time and therefore is sensitive to this bias. These dynamical biases are demonstrated using epidemic simulations by Park et al."

1. Simulations to illustrate concepts and power Given the assertion that observed serial intervals will depend on epidemic growth rates, reporting, and timing of interventions, I think a simple simulation to illustrate some of these ideas would be very helpful. For example, a simple agent-based model with simulated infectivity profiles and incubation periods using the estimated bivariate distribution would be extremely helpful in illustrating how serial intervals and estimates of the generation interval can differ from the true intrinsic generation interval (I coded such a simulation to help me understand this paper in a couple of hours with <100 lines of R code, so I do not think this would be much work). This would also be very helpful for illustrating statistical power re. comment 1.

The current paper is based on a strong theoretical foundation provided by previous works, specifically Park et al. 2021, which used simulations similar to the reviewer’s suggestions to demonstrate the dynamical biases. We now mention these simulations somewhere in the introduction section:

“These dynamical biases are demonstrated using epidemic simulations by Park et al."

Author Response

Reviewer #1 (Public Review):

Bohère, Eldridge-Thomas and Kolahgar have studied the effect of mechanical signalling in tissue homeostasis in vivo, genetically manipulating the well known mechano-transductor vinculin in the adult Drosophila intestine. They find that loss of vinculin leads to accelerated, impaired differentiation of the enteroblast, the committed precursor of mature enterocytes, and stimulates the proliferation of the intestinal stem cell. This leads to an enlarged intestinal epithelium. They discriminate that this effect is mediated through its interaction with alpha-catenin and the reinforcement of the adherens junctions, rather than with talin and integrin-mediated interaction with the basal membrane. This results aligns well, as the authors note, with previous observations from Choi, Lucchetta and Ohlstein (2011) doi:10.1073/pnas.1109348108. Bohère et al then explore the impact that disrupting mechano-transduction has on the overall fitness of the adult fly, and find that vinculin mutant adult flies recover faster after starvation than wild types.

The main conclusions of the paper are convincing and informative. Some important results would benefit from a more detailed description of the phenotypes, and others could have alternative explanations that would warrant some additional clarification.

1) - Interpretation of phenotypes in vinc[102.1] mutants

The paper presents several adult phenotypes of the homozygous viable, zygotic null mutant vinculin[102.1], where the fly gut is enlarged (at least in the R4/5 region). In many cases, they correlate this phenotype with that of RNAi knockdown of vinculin in the gut induced in adult stages. This is a perfectly valid approach, but it presents the difficulty of interpretation that the zygotic mutant has lacked vinculin throughout development and in every fly tissue, including the visceral mesoderm that wraps the intestinal epithelium and that also seems enlarged in the vinc[102.1] mutant. So this phenotype, and others reported, could arise from tissue interactions. To me, the quickest way to eliminate this problem would be to express vinculin in ISCs and/or EBs the vinc[102.1] background, either throughout development or after pupariation or emergence, and observe a rescue.

We agree with the reviewer that we cannot exclude additional vinculin role(s) in other tissues during or after development that might have an impact on the intestinal epithelium. Our attempts to express a full-length Vinculin construct (Maartens et al, 2016) in the vinc102.1 flies, either in adulthood or throughout development, were not very conclusive: although we observed some degree of rescue, it was not fully penetrant. This was in contrast to the complete rescue observed with the genomic rescue of vinculin. Thus, it is possible that some form of tissue interaction contributes to the phenotype observed, for example if vinculin loss affects muscle structure. Alternatively, just like it was shown that too much active vinculin is detrimental to the fly (Maartens et al, 2016), our experiment suggests that too much vinculin may be deleterious to the intestine.

In any case, because of cell-specific knockdowns in the adult gut, we are confident that EB reduction of vinculin levels or activity is sufficient to accelerate tissue turnover, at least in a specific portion of the posterior midgut. We have amended the text to acknowledge a role for tissue interactions (see page 6 (end of first paragraph), page 7 (start of last paragraph), page 12 (starvation experiments).

An experiment where this is particularly difficult is with the starvation/refeeding experiment. The authors explored whether the disruption of tissue homeostasis, as a result of vinculin loss, matters to the fly. So they tested whether flies would be sensitive to starvation/re-feeding, where cellular density changes and vinculin mechano-sensing properties may be necessary. They correctly conclude that mutant flies are more resistant to starvation, and suggest that this may be due to the fact that intestines are larger and therefore more resilient. However, in these animals vinculin is absent in all tissues. It is equally likely that the resistance to starvation was due to the effect of Vinculin in the fat body, ovary, brain, or other adult tissues singly or in combination. The fact that the intestine recovers transiently to a size slightly larger than that of the fed flies seems anecdotal, considering the noise within the timeline of fed controls. I am not sure this experiment is needed in the paper at all, but to me, the healthy conclusion from this effort is that more work is needed to determine the impact of vinculin-mediated intestinal homeostasis in stress resistance, and that this is out of the scope of this paper.

Please the new data presented in Figure 8A-B (text page 12).

2) - Cell autonomy of the requirement of Vinculin and alpha-Catenin

Authors interpret that Vinculin is needed in the EB to maintain mechanical contact with the ISC, restrict ISC proliferation through contact inhibition, and maintain the EB quiescent. This interpretation explains seemingly well the lack of an obvious phenotype when knocking down vinculin in ISCs only, while knockdown in ISCs and EBs, or EBs only, does lead to differentiation problems. It also sits well with the additional observation that vinculin knockdown in mature ECs does not have an obvious phenotype. However, a close examination makes the results difficult to explain with this interpretation only. If the authors were correct, one would expect that in mutant clones, eventually, vinculin-deficient EBs will be produced, which should mis-differentiate and induce additional ISC proliferation. However, the clones only show a reduction in ISC proportions; the most straight forward interpretation of this is that vinculin is cell-autonomously necessary for ISC maintenance (which is at odds with the phenotype of vinculin knockdown using the ISC and ISC/EB drivers).

We apologise that we were unclear in the text. With hindsight, the confusion may have been caused by our describing the phenotype of MARCM clones before reporting the accumulation of EBs in the vinc102.1 guts. Therefore, we swapped these two sections and improved the description of these experiments in the manuscript (see section: “The pool of enterocyte progenitors expands upon vinculin depletion” pages 6-8).

In brief, we do not think that our results are at odds with the phenotype of vinculin knockdown using the ISC and ISC/EB drivers - we realise the text was misleading and hope to have clarified our observations in the revised manuscript (pages 7 and 8). From cell conditional RNAi experiments, like the reviewer, we would predict that vinculin knockdown or loss of function in mitotic clones (MARCM experiments, Figure 4E-G) will induce accelerated differentiation of vinculin deficient enteroblasts, which in turn will increase proliferation. We observed that vinc102.1 or vinc RNAi mitotic clones contained similar number of cells compared to control clones, but reduced proportion of stem cells (Figure 4G). We interpret this as indicating that to maintain an equivalent clone size, stem cells must have divided more frequently, with some divisions producing two differentiated daughter cells. This type of symmetric division would increase the EB pool (as seen in Figure 4-figure supplement 2B), at the expense of the ISC population, in turn decreasing long term clonal growth potential. Altogether, the results obtained with MARCM clones highlight changes in tissue dynamics compatible with those observed with cell-specific vinculin knockdowns.

Also, from the authors interpretation, it would follow induce that the phenotype of vinculin knockdown in ISCs+EBs and in EBs only should be the same. However, in ISCs+EBs vinculin knockdown, differentiation accelerates, which is likely accompanied by increased proliferation (judging by the increase in GFP area, PH3 staining would be more definitive).

Indeed, the accelerated differentiation observed with esgGal4>UAS VincRNAi is accompanied by increased proliferation with the two independent RNAi lines used. We have added this result in Figure 1-figure supplement 1G (and in text, page 5).

This contrasts with the knockdown only in EBs, which leads to accumulation of EBs due to misdifferentiation, and increased proliferation, mostly of ISCs, as measured directly with PH3 staining, but not additional late EBs or mature ECs. The authors call this "incomplete maturation due to accelerated differentiation". I think that one should expect to find incomplete differentiation/maturation when the rate of the process is very slow, not the other way around. To me, these are different phenotypes, which could perhaps be explained if vinculin was also needed in the ISC to transmit tension to the EB and prevent its differentiation, and removing it only in the EB may be revealing an additional, cell-autonomous requirement in maturation.

When vinculin is knocked down in EBs, cells appear bigger than controls (as judged by the RFP+ nuclei in Figure 5E). This, compared to yw and vinc102.1 guts shown in Figure 4D suggests that these cells are more advanced in their differentiation. We have removed the sentence, to not confuse the reader, and clarified the text (see page 8). The discrepancy in the differentiation index between the esgGal4 and KluGal4 experiments might result from differences in the drivers, or an additional role of vinculin in EC differentiation, which we now mention in the text (page 8).

So far, we have no evidence to support the idea that vinculin is also needed in the ISC to transmit tension to the EB and prevent its differentiation; for example, the lack of any phenotype when we knocked down vinculin specifically in ISCs (Figure 3) – notably, no increase in ISC ratio and no increase in cell density (unlike the reduction seen in Figure 1F with ISC+EB Knockdown).

Another unexpected result, considering the authors interpretation, is that the over expression of activated Vinculin (vinc[CO]) does not seem to have much of an effect. It does not change the phenotype of the wild type (where there is very little basal turnover to begin with) and it only partially rescues the phenotype of the vinc[102.1] mutants, when the rescue transgene vinc:RFP does. This again suggests that there may be tissue interactions, in development or adulthood, that may explain the vinc[102.1] phenotypes. It could also be that this incomplete rescue is due to the deleterious effect of Vinc[CO]; this is another reason for doing the vinc[102.1]; esg-Gal4; UAS-vincFL experiments suggested above). An alternative experiment to perform this rescue would be to knock down vinculin gene while overexpressing the Vinc[CO] transgene - this may be possible with the RNAi HSM02356, which targets the vinculin 3'UTR and is unlikely to affect UAS-vinc[CO].

Please refer to essential point 2c; as VincCO is not a simple overactive protein, like a constitutively active kinase, additional effects in the tissue can be expected.

The claims of the authors would be more solid if the reporting of the phenotypes was more homogeneous, so one could establish comparisons. Sometimes conditions are analysed by differentiation index, others by extension of the GFP domains, others with phospho-histone-3 (PH3), others through nuclear size or density, and combinations. I do not think the authors should evaluate all these phenotypes in all conditions, but evaluating mitotic index and abundance of EBs and "activated EBs/early ECs" to monitor proliferation and differentiation rates should be done across the board (ISC, ISC+EB, EB drivers).

To improve consistency, in all conditions we have compared cell types ratios and cellular density upon vinculin knockdown: see Figure 1E-F for ISC+EB, Figure 3B-C for ISC, and Figure 5 – figure supplement 1C-E for EB (with panel E newly added). As we did not observe any effect on ratio or density, we did not monitor cell proliferation for ISC knockdown.

Nonetheless, we added the mitotic index for the ISC+EB driver (new Figure 1- figure supplement 1G) to be consistent with the results from the EB driver (Figure 5- figure supplement 1C).

If the primary role of Vinculin is to induce contact inhibition in the ISC from the EB and prevent the EB differentiation and proliferation, one would expect that over expression of Vinc[CO] (or perhaps VincFL or sqhDD) in EBs should prevent or delay the differentiation and proliferation induced by a presumably orthogonal factor, like infection with Pseudomonas entomophila or Erwinia carotovora.

This is indeed an exciting prediction, but outside the scope of this manuscript.

3) - Relationship between Vinculin and alpha-Catenin

The authors establish a very clear difference in the phenotypes between focal adhesion components and Vinculin, whereas the similarity of alpha-catenin and vinculin knockdowns is very compelling. Therefore I am sure the authors are in the right path with their interpretation of this part of the paper. However, some of the alpha-Catenin experiments are not very clear. The result from the rescue experiment of alpha-Cat knockdown with alpha-Cat-deltaM1b does not seem to show what the authors claim, and differentiation does not seem affected, only the amount of extant older ECs (which may be due to other reasons as this is a non-autonomous effect).

Like the reviewer, we were surprised about the milder rescue with M1b compared to M1a and are unsure of the reasons for this. Nevertheless, quantifications of the differentiation and retention indices show significant differences for M1a and M1b compared to the FL control (Figure 6F-G), with phenotypes resembling the vinc knockdown. In Figure 6E, we have added a row of zoomed views to better highlight the similarity of phenotype between M1a and M1b and have acknowledged the mild differences in the text (bottom of page 9). For the sake of rigour, we think it is important to include results from both M1 deletions, even if there is not yet a logical reason to explain why they have different effects.

Ulrich Tepass produced a UAS-alpha-catenin construct with the full deletion of the M1 region, perhaps that would show a clearer phenotype.

This is a good suggestion, however for technical reasons this is not possible. The strategy devised by Ken Irvine and his group relies on rescuing the RNAi with an RNAi resistant construct, which is not the case for the constructs generated in the Tepass lab. Furthermore, we cannot adopt a MARCM strategy as -cat is too close to the centromere (80F).

Also, the autonomy of the phenotype is difficult to address with these experiments alone. It would be expected that the phenotype of alpha-catenin knockdown should be similar to that of vinculin knockdown in the ISCs only or EBs only.

This is not what our understanding of cadherin-mediated adhesion would predict. Forming cadherin adhesions requires cadherins and catenins in both cells, so we would expect similar phenotypes in ISCs only and EBs only. What is exciting about our findings is that the mechanosensitive machinery is not equally important in the two adherent cells, i.e. the EB is using vinculin to measure force on the contact and regulate differentiation, whereas the ISC needs to resist that force, but does not use vinculin to sense that force and regulate its behaviour.

We have added new data showing the role of the vinculin/α-catenin interaction in ISCs or EBs by co-expressing α-Cat RNAi and α-Cat ΔM1a. We observed that absence of VBS in α-catenin has no effect in ISCs but promotes EB differentiation and increase in numbers (new Figure 6 – figure supplement 2), similar to our observations with vincRNAi (see text page 10).

Reviewer #2 (Public Review):

Vinculin functions as an important structural bridge that connects cadherin and integrin-mediated adhesions to the F-actin cytoskeleton. This manuscript carefully examined the mutant phenotype of vinc in the Drosophila intestine and found that vinc mutant in EBs causes significant increases of EB to EC differentiation, stem proliferation, and tissue growth. By analyzing the mutant phenotype of the cadherin adaptor alpha-catenin, the authors suggest that the vinc functions through the cell-cell junctions instead of cell-CEM adhesions in EBs. Finally, manipulation of myosin activity in EBs phenocopies the vinc mutant, suggesting that vinculin is regulated by the mechanical tension transduced through the cytoskeleton.

The authors claim that the vinculin mutant phenotype is opposite compared to the loss of the major integrin components, suggesting a function independent of the cell-ECM adhesions. However, the phenotype of vinc and integrin may not be completely opposite. Besides loss of ISCs, both mys and talin knockdown in ISCs clearly causes ISCs differentiation into EC cells (Fig.3A), suggesting a possible involvement of integrin in EB to EC differentiation. Therefore, it will be important to test the phenotype of integrin KD in EBs using EB-specific Gal4.

The reviewer raised an important point. To test this we had to overcome the ISC defect of mys or talin RNAi, and specifically tested their function in enteroblasts using the KluGal4 driver. This revealed a similar phenotype of accelerated differentiation, assayed with the ReDDM system (see new Figure 6 -figure supplement 4). Thus, as the reviewer suggested both integrins and cadherins function in this process, we have amended the text to indicate this (see page 10, and sentence in the discussion page 12). It appears however that, unlike vinculin, they also have a key role in ISCs.

The authors proposed a model that the cell-cell adhesion between ISC and EBs is required for vinculin mediated differentiation suppression. However, this model is not directly supported by the data as the EB-ISC adhesion and EB-EC adhesion have not been tested separately.

This is an important point and we have amended the text to address this.

We have focussed our model on EB-ISC adhesion as the adherens junctions are stronger between progenitor cells than EBs-ECs, and because of previous data from the Ohlstein lab (Choi et al, 2011) demonstrating the relationship between adherens junction stability and EB differentiation/ISC proliferation. Nonetheless we agree it is possible that EB-EC adhesion might contribute to this mechanism and have modified the last sentence of the result section (page 12) and the legend associated to the model (Figure 8) to take this into account.

In addition, previous short-term manipulation of E-cadherin in ISCs and EBs shows no change in cell proliferation (Liang J. et al. 2017), which seems to contradict the authors' model. To support the authors' conclusion, long-term manipulation of E-cadherin in ISCs and EBs must be tested.

A main feature of the vinculin phenotype is the regional accelerated differentiation observed in R4/5, potentially reflecting areas more subject to mechanical forces. Strikingly, this accelerated differentiation is rarely observed more anteriorly (such as region R4a/b studied in Liang et al, 2017). In fact, these regional differences were previously reported with E-cadherin knockdown by the Adachi-Yamada group (see Figure S1, Maeda et al, 2008). This highlights the importance of considering regional control of cell fate for the field.

To test our hypothesis further, we have knocked down E-cadherin and α-catenin in EBs only (with Klu-Gal4). As shown in new Figure 6-figure supplement 3, we observed an accumulation of EBs as early as 3 days after induction, reminiscent of vinculin loss of function phenotype. Longer E-cadherin EB knock-down with KluGal4 appears particularly detrimental for survival as all flies died after 4 days of continuous RNAi expression preventing any further observations (see new text page 10). These observations support our model that junctional stability slows down EB differentiation. Our results are also in agreement with the work described in Choi et al (2011), whereby after 6 days of E-Cadherin RNAi expression in progenitors or EBs (using a different driver from us, Su(H)Gal4), the mitotic index increases, showing a feedback regulation on ISC proliferation. Therefore, our work and the Liang et al 2017 study are not in fact contradictory: the differences in the contribution of junctions to tissue dynamics might reflect the variety of molecular mechanisms involved along the small intestine.

The result of MARCM analysis seems inconsistent with the rest of the data. In MARCM, no significant change of clone sizes is observed between WT and vinc mutant (Fig. 3E). However, vinc mutant in EBs clearly promotes ISC proliferation in other experiments such as esg>vinc-RNAi and the EB>vinc-RNAi (Fig. 1A, Fig. 4).

Please refer to point 2a, essential revisions. We do not think that our results are at odds with the phenotype of vinculin knockdown using the ISC and ISC/EB drivers - we realise the text was misleading and hope to have clarified our observations in the revised manuscript (pages 7-8).

In Fig. 4H, the authors suggest that vinculin mutant prevent terminal EC formation. However, this may be simply caused by longer retention of Klu expression in the newborn ECs. To test if EB differentiation is indeed affected, the EC marker pdm1 staining will provide more convincing evidence. Another experiment to strengthen the conclusion will be the tracking of clone sizes generated from a single EB cell using the UAS-Flp system (such as G-trace).

These are good suggestions to strengthen our findings. Unfortunately, we have not managed to obtain a working Pdm1 antibody (or other commercially available EC marker), which is why we assayed nuclear size and the tracking of KluReDDM cells. Therefore, we have not been able to test if Klu is retained in newborn ECs.

As we agree this section of the text was misleading, we have rephrased and highlighted that the phenotype seen with KluGal4ReDDM resembles the accumulation of activated EBs and newborn ECs observed in vinc102.1 guts. (page 8).

In Fig. 6D, the survival rate of WT and vinc mutant flies were compared. However, as there is no additional assay about the feeding behavior or metabolic rate, the systematic mutant of vinc does not provide a direct link between animal survival and intestinal EBs. Therefore, an experiment with vinc level specifically manipulated in fly intestine using esg>vinc-RNAi or BE>vinc-RNAi will be more relevant.

This experiment has now been added in Figure 8B and the text modified to acknowledge the limitations of the survival experiments with whole mutant flies (see point 3, essential revisions above).

Reviewer #3 (Public Review):

Prior work had identified essential roles for Integrin signaling in regulating intestinal stem cell (ISC) proliferation, and the authors studies were motivated by trying to understand whether Vinculin (Vinc) might participate in this. However, Vinc is involved in mechanotransduction at both focal adhesions (FA) and adherens junctions (AJ), and their results revealed that Vinc phenotypes do not match those of FA proteins like Integrin. Conversely, they do match a-catenin (a-cat) RNAi phenotypes, and together with the localization of Vinc and the phenotypes associated with a-cat mutants that can't bind Vinc, this led to the conclusion that Vinc is acting at AJ rather than FA in this tissue. The results here are convincing, with clear presentation, nice images, and appropriate quantitation. It's also worth emphasizing that initial characterization of Vinc mutant flies failed to reveal any essential roles for this protein in Drosophila, so finding a mutant phenotype of any sort is significant.

While the manuscript is strong as a descriptive report on the requirement for Vinc in the Drosophila intestine, it doesn't provide us with much understanding of the mechanism by which Vinc exerts its effects, nor how its requirement is linked to intestinal physiology.

There is always more to learn, and the importance of our work so far is that it demonstrates a very specific role for vinculin as a mechanoeffector in regulating cell fate decisions in specific regions of the midgut, and provide the foundation for future work addressing the detailed mechanism of this function and physiological role.

Prior work has shown that mechanical stretching of intestines stimulates ISC proliferation (presumably through Integrin signaling), which is opposite to what Vinc does here.

We would like to stress that very little mechanistic knowledge is available regarding how mechanical stretching stimulates ISC proliferation, in Drosophila or mammalian systems. To our knowledge, the only work linking gut mechanical stretching to cell fate decisions in Drosophila identified Msn/Hippo pathway (Li et al., 2018) and the ion channel Piezo requirement (He et al., 2018). We agree with the reviewer that integrin signaling would most likely contribute, especially given the composition of gels for organoid cultures (Gjorevski et al, 2016), yet the actual molecular mechanisms remain to be elucidated.

There is a suggestion that Vinc is involved in maintaining homeostasis, but how its regulated remains a bit murky. The authors report that reductions in myosin activity result in phenotypes reminscent of Vinc phenotypes, which they interpret as supporting a model where Vinc's role is to help maintain tension at AJ. Of course it could also be reversed - maybe they are similar because tension is needed to maintain Vinc recruitment to AJ? They lack of epistasis tests and lack of analysis of whether Vinc localization to AJ in EBs is affected by tension or the M2 deletion of a-cat leaves us uncertain as to the actual basis for the relationship between Vinc and myosin phenotypes.

Thank you for all these suggestions. New experiments have been done to test the relationship between cellular tension and vinculin at junctions (see essential point 1).

Author Response:

Reviewer #3 (Public Review):

Murphy et al. further develop the linked selection model of Elyashiv et al. (2016) and apply it to human genetic variation data. This model is itself an extension of the McVicker et al. (2009) paper, which developed a statistical inference method around classic background selection (BGS) theory (Hudson and Kaplan, 1995, Nordborg et al., 1996). These methods fit a composite likelihood model to diversity data along the chromosome, where the level of diversity is reduced by a local factor from some initial "neutral" level π0 down to observed levels. The level of reduction is determined by a combination of both BGS and the expected reduction around substitutions due to a sweep (though the authors state that these models are robust to partial and soft sweeps). The expected reduction factor is a function of local recombination rates and genomic annotation (such as exonic and phylogenetically conserved sequences), as well as the selection parameters (i.e. mutation rates and selection coefficients for different annotation classes). Overall, this work is a nice addition to an important line of work using models of linked selection to differentiate selection processes. The authors find that positive selection around substitutions explains little of the variation in diversity levels across the genome, whereas a background selection model can explain up to 80% of the variance in diversity. Additionally, their model seems to have solved a mystery of the McVicker et al. (2009) paper: why the estimated deleterious mutation rate was unreasonably high. Throughout the paper, the authors are careful not only in their methodology but also in their interpretation of the results. For example, when interpreting the good fit of the BGS model, the authors correctly point out that stabilizing selection on a polygenic trait can also lead to BGS-like reductions.

Furthermore, the authors have carefully chosen their model's exogenous parameters to avoid circularity. The concern here is that if the input data into the model - in particular the recombination maps and segments liked to be conserved - are estimated or identified using signals in genetic variation, the model's good fit to diversity may be spurious. For example, often recombination maps are estimated from linkage disequilibrium (LD) data which is itself obtained from variation along the chromosome. Murphy et al. use a recombination map based on ancestry switches in African Americans which should prevent "information leakage" between the recombination map and the BGS model from leading to spuriously good fits. Likewise, the authors use phylogenetic conservation maps rather than those estimated from diversity reductions (such as McVicker et al.'s B maps) to avoid circularity between the conserved annotation track and diversity levels being modeled. Additionally, the authors have carefully assessed and modified the original McVicker et al. algorithm, reducing relative error (Figure A2).

One could raise the concern that non-equilibrium demography confounds their results, but the authors have a very nice analysis in Section 7 of the supplementary material showing that their estimates are remarkably stable when the model is fit separately in different human populations (Figure A35). Supporting previous work that emphasizes the dependence between BGS and demography, the authors find evidence of such an interaction with a clever decomposition of variance approach (Figure A37). The consistency of BGS estimates across populations (e.g. Figures A35 and A36) is an additional strong bit of evidence that BGS is indeed shaping patterns of diversity; readers would benefit if some of these results were discussed in the main text.

We appreciate the reviewer’s kind remarks. With regards to the results included in the main text vs the supplement, we attempted to strike a balance between having the main text remain communicative to a larger readership and providing experts with details they may find useful. We have, however, done our best for the supplementary analyses to be written clearly.

I have three major concerns about this work. First, it's unclear how accurate the selection coefficient estimates are given the non-equilibrium demography of humans (pre-Out of Africa split, and thus not addressed by the separate population analyses). The authors do not make a big point about the selection coefficient estimates in the main section of the paper, so I don't find this to be a big problem. Still, some mention of this issue might be helpful to readers trying to interpret the results presented in the supplementary text.

As the reviewer notes, we chose not to emphasize the inferred distributions of selection coefficients. Our main reason for this choice is the technical issue addressed in Appendix Section 1.5 (L561-564): “Second, thresholding potentially biases our estimates of the distribution of selection effects. While this bias is probably smaller than the bias without thresholding, its form and magnitude are not obvious. This is why we decided not to report the inferred distributions of selection effects in the Main Text.” We agree that if we were to focus on our estimates of the distribution of selection effects, the effects of demographic history would also need to be considered. This is, however, not the focus here.

Second, I'm curious whether the composite likelihood BGS model could overfit any variance along the chromosome - even neutral variance. At some level, the composite likelihood approach may behave like a sort of smoothing algorithm, albeit with a functional form and parameters of a BGS model. The fact that there is information sharing across different regions with the same annotation class should in principle prevent overfitting to local noise. Still, there are two ways I think to address this overfitting concern. First, a negative neutral control could help - how much variation in diversity along the chromosome can this model explain in a purely neutral simulation? I imagine very little, likely less than 5%, but I think this paper would be much stronger with the addition of a negative control like this. Second, I think the main text should include the R2 values from out-sample predictions, rather than just the R2 estimates from the model fit on the entire data. For example, one could fit the model on 20 chromosomes, use the estimated θΒ parameters to predict variation on the remaining two. The authors do a sort of leave-one-out validation at the window level (Figure A31); however, this may not be robust to linkage disequilibrium between adjacent windows in the way leaving out an entire chromosome would be.

The two requested analyses were done and their results are described above, in response to essential revisions (p. 2-3 here). In brief, there is no overfitting of neutral patterns or otherwise. We elaborate on why this finding is expected below.

Finally, I feel like this paper would be stronger with realistic forward simulations. The deterministic simulations described in the supplementary materials show the implementation of the model is correct, but it's an exact simulation under the model - and thus not testing the accuracy of the model itself against realistic forward simulations. However, this is a sizable task and efforts to add selection to projects like Standard PopSim are ongoing.

We agree that forward simulations would be a nice addition, but believe that it is a project in itself. Indeed, a major complication is that when, for computational tractability, purifying selection is simulated in small populations with realistic population-scaled parameters, the reduction in diversity due to selection at unlinked sites has a major effect on neutral diversity levels (see, e.g., Robertson 1961). We hope to address this issue in future work. Meanwhile, we note that the theory that we rely on has been tested against simulations in the past (e.g., Charlesworth et al., 1993; Hudson and Kaplan, 1995; Nordborg et al., 1996).

Author Response

Reviewer #1 (Public Review):

The largest point of improvement that I expect will unfold over this project's development lifecycle will be its documentation.”

This is indeed one of the biggest source code issues. In the next version, we plan to improve the source code documentation, add more examples and also some small HOWTOs for the RasPi setup.

Reviewer #2 (Public Review):

The Design section then introduces the actor model, the C++ library SObjectivizer used to implement it, and the binary message protocol used for transmission of data across nodes. As currently written, however, this section seems overly technical and hard to grasp for readers who might be interested in experimental neuroscience, but who lack the expertise to understand all mentioned functional constructs and required expertise in the C++ language. Several concepts are mentioned only in passing and without introductory references for the non-expert reader. The level of detail also seems to distract from conveying a more meaningful understanding of the remaining trade-offs involved between network communication, latency, synchronization, and bandwidth.

We wanted to briefly describe why the actor model was used and how it addresses the problem of multithreading programming. We think most of the concepts should be understandable even without prior C++ knowledge. This is also why these concepts are only described briefly. For a more in-depth look e.g. the SObjectizer has a detailed documentation.

The essence of the actor-model could probably be captured more succinctly, and more time spent discussing some of these critical decisions underlying LabNet's design principles. For example, although each Raspberry Pi device runs a LabNet server, the current implementation allows only one client connection per node. This might be surprising for some readers as it excludes a large number of possible network topologies, and the reason presented for the design decision as currently detailed is hard to understand without further clarification.

We have removed some unnecessary details about the actor model. In the beginning of the Design section we now describe more in depth why LabNet was designed as a distributed system and why this results in only one connection per node. The hardware low cost made also us prefer simplicity over more complex hardware topologies.

The main method for evaluating the performance of LabNet is a series of performance tests in the Raspberry Pi comparing clients written in C++, C# and Python, followed by a series of benchmarks comparing LabNet against other established hardware control platforms. While these are undoubtfully useful, especially the latter, the use of benchmarking methods as described in the paper should be carefully revisited, as there are a number of possible confounding factors.

For example, in the performance tests comparing clients written in C++, C# and Python, the Python implementation is running synchronously and directly on top of the low-level interface with system sockets, while the C++ and C# versions use complex, concurrent frameworks designed for resilience and scalability. This difference alone could easily skew the Python results in the simplistic benchmarks presented in the paper, which can leave the reader skeptical about all the comparisons with Python in Figure 3. Similarly, the complex nature of available frameworks also raises questions about the comparison between C# and C++. I don't think it is fair to say that Figure 3 is really comparing languages, as much as specific frameworks. In general, comparing the performance of languages themselves for any task, especially compiled languages, is a very difficult topic that I would generally avoid, especially when targeting a more general, non-technical audience.

This is true; comparisons between different languages are always difficult. This is now explicitly addressed in the text. However, since the implementations in C++, C# and Python were so close in all tests, this is more a demonstration then a comparison: the language and framework at the client side is not really important, at least for the simple cases considered here

The second set of benchmarks comparing LabNet to other established hardware control platforms is much more interesting, but it doesn't currently seem to allow a fair assessment of the different systems. Specifically, from the authors' description of the benchmarking procedure, it doesn't seem like the same task was used to generate the different latency numbers presented, and the values seem to have been mostly extracted from each of the platform's published results. This unfortunately reduces the value of the benchmarks in the sense that it is unclear what conditions are really being compared. For example, while the numbers for pyControl and Bpod seem to be reporting the activation of simple digital input and output lines, the latency presented for Autopilot uses as reference the start of a sound waveform on a stereo headphone jack. Audio DSP requires specialized hardware in the Pi which is likely to intrinsically introduce higher latency versus simply toggling a digital line, so it is not clear whether these scenarios are really comparable. Similarly, the numbers for Whisker and Bpod being presented without any variance make it hard to interpret the results.

We also saw this as a problem. Therefore, all tests were resigned and repeated. Now all platforms were subjected to the same test (with the exception of Whisker, where we did not have suitable hardware available). In this way we now have comparable measurements for all platforms.

One of the stated aims of LabNet was to provide a system where implementing new functionality extensions would be as simple as possible. This is another aspect of experimental neuroscience that is under active discussion and where more contributions are very much needed. Surprisingly, this topic receives very little attention in the paper itself. It is not clear whether the actor model is by itself supposed to make the implementation of new functionality easier, but if this is the case, this is not obvious from the way the design and evaluation sections are currently written, especially given the choice of language being C++.

One of the reasons behind the choice of Python for other hardware platforms such as pyControl and Autopilot is the growing familiarity and prevalence of Python within the neuroscience research community, which might assist researchers in implementing new functionality. Other open-hardware projects in neuroscience allowing for community extensions in C++ such as Open-Ephys have informally expressed the difficulty of the C++ language as a point of friction. I feel that the aim of "ease of extensibility" should merit much more discussion in any future revision of the paper.

Indeed, they only mention in passing that user extensibility is in the conclusion where it is stated that it is not currently possible to modify LabNet without directly modifying and recompiling the entire code base. A software plug-in system is suggested, and indeed this would be extremely beneficial in achieving the second stated aim.

With the simplicity of implementing new functionality, we rather meant the simplicity to adapt the LabNet source code to new requirements. For which the modularization and the use of the actor model is responsible. This is now explained more explicitly in the text. And yes, a plug-in system is on our roadmap but not a part of LabNet yet.

Finally, a set of example experimental applications would have been extremely useful to ground the design of LabNet in practical terms, in addition to the example listings. Even in diagrammatic form, describing how specific experiments have been powered by LabNet would give readers a better sense of the kind of designs that might be currently more appropriate for this platform. For example, video is being increasingly used in behavioral experiments, and Raspberry Pi drivers are available for several camera models, but this important aspect is not mentioned at all in the discussion, so readers interested in video would not know from reading this paper whether LabNet would be appropriate for their goals.

The section "Example" actually shows how a simple experiment can be realized with LabNet. Listings 1-3 are also responsible for this.

LabNet does not support video acquisition in the current version. Even though this video transmission would be quite easy to implement. Nevertheless, we have not needed this in our experiments so far.

As the manuscript currently stands, I don't feel the authors have achieved their second stated aim, and I am unfortunately not fully convinced that the experimental results are adequate to demonstrate the achievement of the first aim. I fully agree, however, that a robust, high-performance and flexible hardware layer for combining neuroscience instruments is desperately needed, and so I do expect that a more thorough treatment of the methods developed in LabNet will in the future have a very positive impact on the field.

Latency measurements are indeed very important, also because in this way a comparison with other tools can be achieved. With the test redesign and an own implementation for each tool the comparability is now a given. Of course, LabNet cannot beat Bpod. After all, Bpod is running on a microcontroller and LabNet has to send all commands via Ethernet. But the results are still very good. The stress test also demonstrates the scalability of LabNet. Above all, LabNet offers the possibility to control many systems at the same time, which cannot be done with other tools, or only in a complicated way.