Author Response

Reviewer #1 (Public Review):

Overall, the science is sound and interesting, and the results are clearly presented. However, the paper falls in-between describing a novel method and studying biology. As a consequence, it is a bit difficult to grasp the general flow, central story and focus point. The study does uncover several interesting phenomena, but none are really studied in much detail and the novel biological insight is therefore a bit limited and lost in the abundance of observations. Several interesting novel interactions are uncovered, in particular for the SPS sensor and GAPDH paralogs, but these are not followed up on in much detail. The same can be said for the more general observations, eg the fact that different types of mutations (missense vs nonsense) in different types of genes (essential vs non-essential, housekeeping vs. stress-regulated...) cause different effects.

This is not to say that the paper has no merit - far from it even. But, in its current form, it is a bit chaotic. Maybe there is simply too much in the paper? To me, it would already help if the authors would explicitly state that the paper is a "methods" paper that describes a novel technique for studying the effects of mutations on protein abundance, and then goes on to demonstrate the possibilities of the technology by giving a few examples of the phenomena that can be studied. The discussion section ends in this way, but it may be helpful if this was moved to the end of the introduction.

We modified the manuscript as suggested.

Reviewer #2 (Public Review):

Schubert et al. describe a new pooled screening strategy that combines protein abundance measurements of 11 proteins determined via FACS with genome-wide mutagenesis of stop codons and missense mutations (achieved via a base editor) in yeast. The method allows to identify genetic perturbations that affect steady state protein levels (vs transcript abundance), and in this way define regulators of protein abundance. The authors find that perturbation of essential genes more often alters protein abundance than of nonessential genes and proteins with core cellular functions more often decrease in abundance in response to genetic perturbations than stress proteins. Genes whose knockouts affected the level of several of the 11 proteins were enriched in protein biosynthetic processes while genes whose knockouts affected specific proteins were enriched for functions in transcriptional regulation. The authors also leverage the dataset to confirm known and identify new regulatory relationships, such as a link between the SDS amino acid sensor and the stress response gene Yhb1 or between Ras/PKA signalling and GAPDH isoenzymes Tdh1, 2, and 3. In addition, the paper contains a section on benchmarking of the base editor in yeast, where it has not been used before.

Strengths and weaknesses of the paper

The authors establish the BE3 base editor as a screening tool in S. cerevisiae and very thoroughly benchmark its functionality for single edits and in different screening formats (fitness and FACS screening). This will be very beneficial for the yeast community.

The strategy established here allows measuring the effect of genetic perturbations on protein abundances in highly complex libraries. This complements capabilities for measuring effects of genetic perturbations on transcript levels, which is important as for some proteins mRNA and protein levels do not correlate well. The ability to measure proteins directly therefore promises to close an important gap in determining all their regulatory inputs. The strategy is furthermore broadly applicable beyond the current study. All experimental procedures are very well described and plasmids and scripts are openly shared, maximizing utility for the community.

There is a good balance between global analyses aimed at characterizing properties of the regulatory network and more detailed analyses of interesting new regulatory relationships. Some of the key conclusions are further supported by additional experimental evidence, which includes re-making specific mutations and confirming their effects on protein levels by mass spectrometry.

The conclusions of the paper are mostly well supported, but I am missing some analyses on reproducibility and potential confounders and some of the data analysis steps should be clarified.

The paper starts on the premise that measuring protein levels will identify regulators and regulatory principles that would not be found by measuring transcripts, but since the findings are not discussed in light of studies looking at mRNA levels it is unclear how the current study extends knowledge regarding the regulatory inputs of each protein.

See response to Comment #10.

Specific comments regarding data analysis, reproducibility, confounders

1) The authors use the number of unique barcodes per guide RNA rather than barcode counts to determine fold-changes. For reliable fold changes the number of unique barcodes per gRNA should then ideally be in the 100s for each guide, is that the case? It would also be important to show the distribution of the number of barcodes per gRNA and their abundances determined from read counts. I could imagine that if the distribution of barcodes per gRNA or the abundance of these barcodes is highly skewed (particularly if there are many barcodes with only few reads) that could lead to spurious differences in unique barcode number between the high and low fluorescence pool. I imagine some skew is present as is normal in pooled library experiments. The fold-changes in the control pools could show whether spurious differences are a problem, but it is not clear to me if and how these controls are used in the protein screen.

Because of the large number of screens performed in this study (11 proteins, with 8 replicates for each) we had to trade off sequencing depth and power against cell sorting time and sequencing cost, resulting in lower read and barcode numbers than what might be ideally aimed for. As described further in the response to Comment #5, we added a new figure to the manuscript that shows that the correlation of fold-changes between replicates is high (Figure 3–S1A). The second figure below shows that the correlation between the number of unique barcodes and the number of reads per gRNA is highly significant (p < 2.2e-16).

2) I like the idea of using an additional barcode (plasmid barcode) to distinguish between different cells with the same gRNA - this would directly allow to assess variability and serve as a sort of replicate within replicate. However, this information is not leveraged in the analysis. It would be nice to see an analysis of how well the different plasmid barcodes tagging the same gRNA agree (for fitness and protein abundance), to show how reproducible and reliable the findings are.

We agree with the reviewer that this would be nice to do in principle, but our sequencing depth for the sorted cell populations was not high enough to compare the same barcode across the low/unsorted/high samples. See also our response to Comment #5 for the replicate analyses.

3) From Fig 1 and previous research on base editors it is clear that mutation outcomes are often heterogeneous for the same gRNA and comprise a substantial fraction of wild-type alleles, alleles where only part of the Cs in the target window or where Cs outside the target window are edited, and non C-to-T edits. How does this reflect on the variability of phenotypic measurements, given that any barcode represents a genetically heterogeneous population of cells rather than a specific genotype? This would be important information for anyone planning to use the base editor in future.

We agree with the reviewer that the heterogeneity of editing outcomes is an important point to keep in mind when working with base editors. In genetic screens, like the ones described here, often the individual edit is less important, and the overall effects of the base editor are specific/localized enough to obtain insights into the effects of mutations in the area where the gRNA targets the genome. For example, in our test screens for Canavanine resistance and fitness effects, in which we used gRNAs predicted to introduce stop codons into the CAN1 gene and into essential genes, respectively, we see the expected loss-of-function effect for a majority of the gRNAs (canavanine screen: expected effect for 67% of all gRNAs introducing stop codons into CAN1; fitness screen: expected effect for 59% of all gRNAs introducing stop codons into essential genes) (Figure 2). In the canavanine screen, we also see that gRNAs predicted to introduce missense mutations at highly conserved residues are more likely to lead to a loss-of-function effect than gRNAs predicted to introduce missense mutations at less conserved residues, further highlighting the differentiated results that can be obtained with the base editor despite the heterogeneity in editing outcomes overall. We would certainly advise anyone to confirm by sequencing the base edits in individual mutants whenever a precise mutation is desired, as we did in this study when following up on selected findings with individual mutants.

4) How common are additional mutations in the genome of these cells and could they confound the measured effects? I can think of several sources of additional mutations, such as off-target editing, edits outside the target window, or when 2 gRNA plasmids are present in the same cell (both target windows obtain edits). Could some of these events explain the discrepancy in phenotype for two gRNAs that should make the same mutation (Fig S4)? Even though BE3 has been described in mammalian cells, an off-target analysis would be desirable as there can be substantial differences in off-target behavior between cell types and organisms.

Generally, we are not very concerned about random off-target activity of the base editor because we would not expect this to cause a consistent signal that would be picked up in our screen as a significant effect of a particular gRNA. Reproducible off-target editing with a specific gRNA at a site other than the intended target site would be problematic, though. We limited the chance of this happening by not using gRNAs that may target similar sequences to the intended target site in the genome. Specifically, we excluded gRNAs that have more than one target in the genome when the 12 nucleotides in the seed region (directly upstream of the PAM site) are considered (DiCarlo et al., Nucleic Acids Research, 2013).

We do observe some off-target editing right outside the target window, but generally at much lower frequency than the on-target editing in the target window (Figure 1B and Figure 1–S2). Since for most of our analyses we grouped perturbations per gene, such off-target edits should not affect our findings. In addition, we validated key findings with independent experiments. For our study, we used the Base Editor v3 (Komor et al., Nature, 2016); more recently, additional base editors have been developed that show improved accuracy and efficiency, and we would recommend these base editors when starting a new study (see, e.g., Anzalone et al., Nature Biotechnology, 2020).

We are not concerned about cases in which one cell gets two gRNAs, since the chance that the same two gRNAs end up in one cell repeatedly is low, and such events would therefore not result in a significant signal in our screens.

We don’t think that off-target mutations can explain the discrepancy between pairs of gRNAs that should introduce the same mutation (Figure 3–S1. The effect of the two gRNAs is actually well-correlated, but, often, one of the two gRNAs doesn’t pass our significance cut-off or simply doesn’t edit efficiently (i.e., most discrepancies arise from false negatives rather than false positives). We may therefore miss the effects of some mutations, but we are unlikely to draw erroneous conclusions from significant signals.

5) In the protein screen normalization uses the total unique barcode counts. Does this efficiently correct for differences from sequencing (rather than total read counts or other methods)? It would be nice to see some replicate plots for the analysis of the fitness as well as the protein screen to be able to judge that.

We made a new figure that shows a replicate comparison for the protein screen (see below; in the manuscript it is Figure 3–S1A) and commented on it in the manuscript. For this analysis, the eight replicates for each protein were split into two groups of four replicates each and analyzed the same way as the eight replicates. The correlation between the two groups of replicates is highly significant (p < 2.2e-16). The second figure shows that the total number of reads and the total number of unique barcodes are well correlated.

For the fitness screen, we used read counts rather than barcode counts for the analysis since read counts better reflect the dropout of cells due to reduced fitness. The figure below shows a replicate comparison for the fitness screen. For this analysis, the four replicates were split into two groups of two replicates each and analyzed the same way as the four replicates. The correlation between the two groups of replicates is highly significant (p < 2.2e-16).

6) In the main text the authors mention very high agreement between gRNAs introducing the same mutation but this is only based on 20 or so gRNA pairs; for many more pairs that introduce the same mutation only one reaches significance, and the correlation in their effects is lower (Fig S4). It would be better to reflect this in the text directly rather than exclusively in the supplementary information.

We clarified this in the manuscript main text: “For 78 of these gRNA pairs, at least one gRNA had a significant effect (FDR < 0.05) on at least one of the eleven proteins; their effects were highly correlated (Pearson’s R2 = 0.43, p < 2.2E-16) (Figure 3–S1B). For the 20 gRNA pairs for which both gRNAs had a significant effect, the correlation was even higher (Pearson’s R2 = 0.819, p = 8.8e-13) (Figure 3–S1C). These findings show that the significant gRNA effects that we identify have a low false positive rate, but they also suggest that many real gRNA effects are not detected in the screen due to limitations in statistical power.”

7) When the different gRNAs for a targeted gene are combined, instead of using an averaged measure of their effects the authors use the largest fold-change. This seems not ideal to me as it is sensitive to outliers (experimental error or background mutations present in that strain).

We agree that the method we used is more sensitive to outliers than averaging per gene. However, because many gRNAs have no effect either because they are not editing efficiently or because the edit doesn’t have a phenotypic consequence, an averaging method across all gRNAs targeting the same gene would be too conservative and not properly capture the effect of a perturbation of that gene.

8) Phenotyping is performed directly after editing, when the base editor is still present in the cells and could still interact with target sites. I could imagine this could lead to reduced levels of the proteins targeted for mutagenesis as it could act like a CRISPRi transcriptional roadblock. Could this enhance some of the effects or alter them in case of some missense mutations?

To reduce potential “CRISPRi-like” effects of the base editor on gene expression, we placed the base editor under a galactose-inducible promoter. For both the fitness and protein screens we grew the cultures in media without galactose for another 24 hours (fitness screen) or 8-9 hours (protein screens) before sampling. In the latter case, this recovery time corresponded to more than three cell divisions, after which we assume base editor levels to have strongly decreased, and therefore to no longer interfere with transcription. This is also supported by our ability to detect discordant effects of gRNAs targeting the same gene (e.g., the two mutations leading to loss-of-function and gain-of-function of RAS2), which would otherwise be overshadowed by a CRISPRi effect.

9) I feel that the main text does not reflect the actual editing efficiency very well (the main numbers I noticed were 95% C to T conversion and 89% of these occurring in a specific window). More informative for interpreting the results would be to know what fraction of the alleles show an edit (vs wild-type) and how many show the 'complete' edit (as the authors assume 100% of the genotypes generated by a gRNA to be conversion of all Cs to Ts in the target window). It would be important to state in the main text how variable this is for different gRNAs and what the typical purity of editing outcomes is.

We now show the editing efficiency and purity in a new figure (Figure 1B), and discuss it in the main text as follows: “We found that the target window and mutagenesis pattern are very similar to those described in human cells: 95% of edits are C-to-T transitions, and 89% of these occurred in a five-nucleotide window 13 to 17 base pairs upstream of the PAM sequence (Figure 1A; Figure 1–S2) (Komor et al., 2016). Editing efficiency was variable across the eight gRNAs and ranged from 4% to 64% if considering only cases where all Cs in the window are edited; percentages are higher if incomplete edits are considered, too (Figure 1B).”

Comments regarding findings

10) It would be nice to see a comparison of the results to the effects of ~1500 yeast gene knockouts on cellular transcriptomes (https://doi.org/10.1016/j.cell.2014.02.054). This would show where the current study extends established knowledge regarding the regulatory inputs of each protein and highlight the importance of directly measuring protein levels. This would be particularly interesting for proteins whose abundance cannot be predicted well from mRNA abundance.

We agree with the reviewer that it would be very interesting to compare the effect of perturbations on mRNA vs protein levels. We have compared our protein-level data to mRNA-level data from Kemmeren and colleagues (Kemmeren et al., Cell 2014), and we find very good agreement between the effects of gene perturbations on mRNA and protein levels when considering only genes with q < 0.05 and Log2FC > 0.5 in both studies (Pearson’s R = 0.79, p < 5.3e-15).

Gene perturbations with effects detected only on mRNA but not protein levels are enriched in genes with a role in “chromatin organization” (FDR = 0.01; as a background for the analysis, only the 1098 genes covered in both studies were considered). This suggests that perturbations of genes involved in chromatin organization tend to affect mRNA levels but are then buffered and do not lead to altered protein levels. There was no enrichment of functional annotations among gene perturbations with effects on protein levels but not mRNA levels.

We did not include these results in the manuscript because there are some limitations to the conclusions that can be drawn from these comparisons, including that our study has a relatively high number of false negatives, and that the genes perturbed in the Kemmeren et al. study were selected to play a role in gene regulation, meaning that differences in mRNA-vs-protein effects of perturbations are limited to this function, and other gene functions cannot be assessed.

11) The finding that genes that affect only one or two proteins are enriched for roles in transcriptional regulation could be a consequence of 'only' looking at 10 proteins rather than a globally valid conclusion. Particularly as the 10 proteins were selected for diverse functions that are subject to distinct regulatory cascades. ('only' because I appreciate this was a lot of work.)

We agree with this, and we think it is clear in the abstract and the main text of the manuscript that here we studied 11 proteins. We made this point also more explicit in the discussion, so that it is clear for readers that the findings are based on the 11 proteins and may not extrapolate to the entire yeast proteome.

Reviewer #3 (Public Review):

This manuscript presents two main contributions. First, the authors modified a CRISPR base editing system for use in an important model organism: budding yeast. Second, they demonstrate the utility of this system by using it to conduct an extremely high throughput study the effects of mutation on protein abundance. This study confirms known protein regulatory relationships and detects several important new ones. It also reveals trends in the type of mutations that influence protein abundances. Overall, the findings are of high significance and the method appears to be extremely useful. I found the conclusions to be justified by the data.

One potential weakness is that some of the methods are not described in main body of the paper, so the reader has to really dive into the methods section to understand particular aspects of the study, for example, how the fitness competition was conducted.

We expanded the first section for better readability.

Another potential weakness is the comparison of this study (of protein abundances) to previous studies (of transcript abundances) was a little cursory, and left some open questions. For example, is it remarkable that the mutations affecting protein abundance are predominantly in genes involved in translation rather than transcription, or is this an expected result of a study focusing on protein levels?

We thank the reviewer for pointing out that this paragraph requires more explanation. We expanded it as follows: “Of these 29 genes, 21 (72%) have roles in protein translation—more specifically, in ribosome biogenesis and tRNA metabolism (FDR < 8.0e-4, Figure 5C). In contrast, perturbations that affect the abundance of only one or two of the eleven proteins mostly occur in genes with roles in transcription (e.g., GO:0006351, FDR < 1.3e-5). Protein biosynthesis entails both transcription and translation, and these results suggest that perturbations of translational machinery alter protein abundance broadly, while perturbations of transcriptional machinery can tune the abundance of individual proteins. Thus, genes with post-transcriptional functions are more likely to appear as hubs in protein regulatory networks, whereas genes with transcriptional functions are likely to show fewer connections.”

Overall, the strengths of this study far outweigh these weaknesses. This manuscript represents a very large amount of work and demonstrates important new insights into protein regulatory networks.

Author Response

Reviewer #2 (Public Review):

The authors seek to determine how various species combine their effects on the growth of a species of interest when part of the same community.

To this end, the authors carry out an impressive experiment containing what I believe must be one of the largest pairwise + third-order co-culture experiments done to date, using a high-throughput co-culture system they had co-developed in previous work. The unprecedented nature of this data is a major strength of the paper. The authors also discover that species combine their effect through "dominance", i.e. the strongest effect masks the others. This is important as it calls into question the common assumption of additivity that is implicit in the choice of using Lotka-Volterra models.

A stronger claim (i.e. in the abstract) is that joint effect of multiple species on the growth of another can be derived from the effect of individual species. Unless I am misunderstanding something, this statement may have to be qualified a little, as the authors show that a model based on pairwise dominance (i.e. the strongest pairwise) does a somewhat better job (lower RMSD, though granted, not by much, 0.57 vs 0.63) than a model based on single species dominance. This is, the effect of the strongest pair predicts better the effect of a trio than the effect of the larger species.

This issue makes one wonder whether, had the authors included higher-order combinations of species (i.e. five-member consortia or higher), the strongest-effect trio would have predicted better than the strongest-effect pair, which in turn is better predictor than the strongest-effect species. This is important, as it would help one determine to what extent the strongest-effect model would work in more diverse communities, such as those one typically finds in nature. Indeed, the authors find that the predictive ability of the strongest effect species is much stronger for pairs than it is for trios (RMSD of 0.28 vs 0.63). Does the predictive ability of the single species model decline faster and faster as diversity grows beyond 4-member consortia?

Thank you for raising this important point. It is true that in our study we see that single species predict pairs better than trios, and that pairs predict trios better than single species. As we did not perform experiments on more diverse communities (n>4), we are not sure if or how these rules will scale up. We explicitly address these caveats in our revised discussion.

Reviewer #3 (Public Review):

A problem in synthetic ecology is that one can't brute-force complex community design because combinatorics make it basically impossible to screen all possible communities from a bank of possible species. Therefore, we need a way to predict phenomena in complex communities from phenomena in simple communities. This paper aims to improve this predictive ability by comparing a few different simple models applied to a large dataset obtained with the use of the author's "kchip" microfluidics device. The main question they ask is whether the effect of two species on a focal species is predicted from the mean, the sum, or the max of the effect of each single "affecting" species on the focal species. They find that the max effect is often the best predictor, in the sense of minimizing the difference between predicted effect and measured effect. They also measure single-species trait data for their library of strains, including resource niche and antibiotic resistance, and then find that Pearson correlations between distance calculations generated from these metrics and the effect of added species are weak and unpredictive. This work is largely well-done, timely and likely to be of high interest to the field, as predicting ecosystem traits from species traits is a major research aim.

My main criticism is that the main take-home from the paper (fig 3B)-that the strongest effect is the best predictor-is oversold. While it is true that, averaged over their six focal species, the "strongest effect" was the best overall predictor, when one looks at the species-specific data (S9), we see that it is not the best predictor for 1/3 of their focal species, and this fraction grows to 1/2 if one considers a difference in nRMSE of 0.01 to be negligible.

As suggested, we have softened our language regarding the take-home message. This matter is addressed in detail above in response to 'Essential Revisions'. Briefly, we see that the strongest model works best when both single species have qualitatively similar effects, but is slightly less accurate when effects are mixed. We also see overall less accurate predictions for positive effects. In light of these findings, we propose that focal species for which the strongest model is not the most accurate is due to the interaction types, and not specific to the focal species.

We made substantial changes to the manuscript, including the first paragraph of the discussion which more accurately describes these findings and emphasizes the relevant caveats:

"By measuring thousands of simplified microbial communities, we quantified the effects of single species, pairs, and trios on multiple focal species. The most accurate model, overall and specifically when both single species effects were negative, was the strongest effect model. This is in stark contrast to models often used in antibiotic compound combinations, despite most effects being negative, where additivity is often the default model (Bollenbach 2015). The additive model performed well for mixed effects (i.e. one negative and one positive), but only slightly better than the strongest model, and poorly when both species had effects of the same sign. When both single species’ effects were positive, the strongest model was also the best, though the difference was less pronounced and all models performed worse for these interactions. This may be due to the small effect size seen with positive effects, as when we limited negative and mixed effects to a similar range of effects strength, their accuracy dropped to similar values (Figure 3–Figure supplement 5). We posit that the difference in accuracy across species is affected mainly by the effect type dominating different focal species' interactions, rather than by inherent species traits (Figure 3–Figure supplement 6)." (Lines 288-304)

The same criticism applies to the result from figure 2-that pairs of affecting species have more negative effects than single species. Considered across all focal species this is true (though minor in effect size, Fig 2A). But there is only a significant effect within two individual species. Again, this points to the effects being focal-species-specific, and perhaps not as generalizable as is currently being claimed.

Upon more rigorous analysis, and with regard to changes in the dataset after filtering, we see that the more accurate statement is that effects become stronger, not necessarily more negative (in line with the accuracy of the strongest model). The overall trend is towards more negative interactions, due to the majority of interactions being negative, but as stated this is not true for each individual focal. As such the following sentence in the manuscript has been changed:

"The median effect on each focal was more negative by 0.28 on average, though the difference was not significant in all cases; additionally, focals with mostly positive single species interactions showed a small increase in median effect (Fig. 2D)" (Lines 151-154)

As well as the title of this section: "Joint effects of species pairs tend to be stronger than those of individual affecting species" (Lines 127-128)

Another thing that points to a focal-species-specific response is Fig 2D, which shows the distributions of responses of each focal species to pairs. Two of these distributions are unimodal, one appears bimodal, and three appear tri-modal. This suggests to me that the focal species respond in categorically different ways to species addition.

We believe this distribution of pair effects is related to the distribution of single species effects, and not to the way in which different focal species respond to the addition of second species. Though this may be difficult to see from the swarm plots shown in the paper, below is a split violin plot that emphasizes this point.

Fig R1: Distribution of single species and pair effects. Distribution of the effect of single and pairs of affecting species for each focal species individually. Dashed lines represent the median, while dotted lines the interquartile range.

These differences occur even though the focal bacteria are all from the same family. This suggests to me that the generalizability may be even less when a more phylogenetically dispersed set of focal species are used.

We have added the following sentence to the discussion explicitly emphasizing the phylogenetic limitations of our study:

"Lastly, it is important to note that our focal species are all from the same order (Enterobacterales), which may also limit the purview of our findings." (Lines 364-366)

Considering these points together, I argue that the conclusion should be shifted from "strongest effect is the best" to "in 3 of our focal species, strongest effect was the best, but this was not universal, and with only 6 focal species, we can't know if it will always be the best across a set of focal species".

As mentioned above, we have softened our language regarding the take-home message in response to these evaluations.

My second main criticism is that it is hard to understand exactly how the trait data were used to predict effects. It seems like it was just pearson correlation coefficients between interspecies niche distances (or antibiotic distances) and the effect. I'm not very surprised these correlations were unpredictive, because the underlying measurements don't seem to be relevant to the environment tested. What if, rather than using niche data across 20 nutrients, only the growth data on glucose (the carbon source in the experiments) was used? I understand that in a field experiment, for example, one might not know what resources are available, and so measuring niche across 20 resources may be the best thing to do. Here though it seems imperative to test using the most relevant data.

It is true that much of the profiling data is not directly related to the experimental conditions (different carbon sources and antibiotics), but in addition to these we do use measurements from experiments carried out in the same environment as the interactions assays (i.e. growth rate and carrying capacity when growing on glucose), which also showed poor correlation with the effects on focals. Additionally, we believe that these profiles contain relevant information regarding metabolic similarity between species (similar to metabolic models often constructed computationally). To improve clarity, we added the following sentence to the figure legend of Figure 3–Figure supplement 1:

"The growth rate, and maximum OD shown in panel A were measured only in M9 glucose, similar to conditions used in the interaction assays." (Lines 591-592)

Additionally and relatedly, it would be valuable to show the scatterplots leading to the conclusion that trait data were uninformative. Pearson's r only works on an assumption of linearity. But there could be strong relationships between the trait data and effect that are monotonic but not linear, or even that are non-monotonic yet still strong (e.g. U-shaped). For the first case, I recommend switching to Spearman's rho over Pearson's r, because it only assumes monotonicity, not linearity. If there are observable relationships that are not monotonic, a different test should be used.

Per your suggestion, we have changed the measurement of correlation in this analysis from Pearson's r, to Spearman's rho. As we observed similar, and still mostly weak correlations, we did not investigate these relationships further. See Figure 3–Figure supplement 1.

Additionally, we generated heat maps including scatterplots mapping the data leading to these correlations. We found no notable dependency in these plots, and visually they were quite crowded and difficult to interpret. As this is not the central point of our study, we ultimately decided against adding this information to the plots.

In general, I think the analyses using the trait data were too simplistic to conclude that the trait data are not predictive.

We agree that more sophisticated analyses may help connect between species traits and their effects on focal species. In fact, other members of our research group have recently used machine learning to accomplish similar predictions (https://doi.org/10.1101/2022.08.02.502471). As such we have changed the wording in to reflect that this correlation is difficult to find using simple analyses:

"These results indicate that it may be challenging to connect the effects of single and pairs of species on a focal strain to a specific trait of the involved strains, using simple analysis." (Lines 157-159)

Author Response

Reviewer #1 (Public Review):

Slusarczyk et al present a very well written manuscript focused on understanding the mechanisms underlying aging of erythrophagocytic macrophages in the spleen (RPM) and its relationship to iron loading with age. The manuscript is diffuse with a broad swath of data elements. Importantly, the manuscript demonstrates that RPM erythrophagocytic capacity is diminished with age, restored in iron restricted diet fed aged mice. In addition, the mechanism for declining RPM erythrophagocytic capacity appears to be ferroptosis-mediated, insensitive to heme as it is to iron, and occur independently of ROS generation. These are compelling findings. However, some of the data relies on conjecture for conclusion and a clear causal association is not clear. The main conclusion of the manuscript points to the accumulation of unavailable insoluble forms of iron as both causing and resulting from decreased RPM erythrophagocytic capacity.

We are proposing that intracellular iron accumulation progresses first and leads to global proteotoxic damage and increased lipid peroxidation. This eventually triggers the death of a fraction of aging RPMs, thus promoting the formation of extracellular iron-rich protein aggregates. More explanation can be found below. Besides, iron loading suppresses the erythrophagocytic activity of RPMs, hence further contributing to their functional impairment during aging.

In addition, the finding that IR diet leads to increased TF saturation in aged mice is surprising.

We believe that this observation implies better mobilization of splenic iron stores, and corroborates our conclusion that mice that age on an iron-reduced diet benefit from higher iron bioavailability, although these differences are relatively mild. More explanation can be found in our replies to Reviewer #2.

Furthermore, whether the finding in RPMs is intrinsic or related to RBC-related changes with aging is not addressed.

We now addressed this issue and we characterized in more detail both iron and ROS levels in RBCs.

Finally, these findings in a single strain and only female mice is intriguing but warrants tempered conclusions.

We tempered the conclusions and provided a basic characterization of the RPM aging phenotype in Balb/c female mice.

Major points:

1) The main concern is that there is no clear explanation of why iron increases during aging although the authors appear to be saying that iron accumulation is both the cause of and a consequence of decreased RPM erythrophagocytic capacity. This requires more clarification of the main hypothesis on Page 4, line 17-18.

We thank the reviewer for this comment. It was previously reported that iron accumulates substantially in the spleen during aging, especially in female mice (Altamura et al., 2014). Since RPMs are those cells that process most of the iron in the spleen, we aimed to explore what is the relationship between iron accumulation and RPM functions during aging. This investigation led us to uncover that indeed iron accumulation is both the cause and the consequence of RPM dysfunction. Specifically, we propose that intracellular iron loading of RPMs precedes extracellular deposition of iron in a form of protein-rich aggregates, driven by RPMs damage. To support this, we now show that the proteome of RPMs overlaps with those proteins that are present in the age-triggered aggregates (Fig. 3F). Furthermore, corroborating our model, we now demonstrate that transient iron loading of RPMs via iron-dextran injection (new Fig. 3G) leads to the formation of protein-rich aggregates, closely resembling those present in aged spleens (new Fig. 3H). This implies that high iron content in RPMs is indeed a major driving factor that leads to aggregation of their proteome and cell damage. Importantly, we now supported this model with studies using iRPMs. We demonstrated that iron loading and blockage of ferroportin by synthetic mini-hepcidin (PR73)(Stefanova et al., 2018) cause protein aggregation in iRPMs and lead to their decreased viability only in cells that were exposed to heat shock, a well-established trigger of proteotoxicity (new Fig. 5K and L). We propose that these two factors, namely age-triggered decrease in protein homeostasis and exposure to excessive iron levels, act in concert and render RPMs particularly sensitive to damage during aging (see also Discussion, p. 16).

In parallel, our data imply that the increased iron content in aged RPMs drives their decreased erythrophagocytic activity, as we now better documented by more extensive in vitro experiments in iRPMs (new Fig 6E-H). We cannot exclude that some of the senescent splenic RBCs that are retained in the red pulp and evade erythrophagocytosis due to RPM defects in aging, may also contribute to the formation of the aggregates. This is supported by the fact that mice that lack RPMs as well exhibit iron loading in the spleen (Kohyama et al., 2009; Okreglicka et al., 2021), and that the proteome of aggregates overlaps to some extent with the proteome of erythrocytes (new Fig. 3F).

We believe that during aging intracellular iron accumulation is chiefly driven by ferroportin downregulation, as also suggested by Reviewer#3. We now show that ferroportin drops significantly already in mice aged 4 and 5 months (new Fig. 4H), preceding most of the other impairments. This drop coincides with the increase in hepcidin expression, but if this is the sole reason for ferroportin suppression during early aging would require further investigation outside the scope of the present manuscript.

In sum, to address this comment, we now modified the fragment of the introduction that refers to our hypothesis and major findings to be more clear (p. 4), we improved our manuscript by providing new data mentioned above and we added more explanation in the corresponding sections of the Results and Discussion.

2) It is unclear if RPMs are in limited supply. Based on the introduction (page 4, line 13-15), they have limited self-renewal capacity and blood monocytes only partially replenished. Fig 4D suggests that there is a decrease in RPMs from aged mice. The %RPM from CD45+ compartment suggests that there may just be relatively more neutrophils or fewer monocytes recruited. There is not enough clarity on the meaning of this data point.

Thank you for this comment. We fully agree that %RPMs of CD45+ splenocytes, although well-accepted in literature (Kohyama et al., 2009; Okreglicka et al., 2021), is only a relative number. Hence, we now included additional data and explanations regarding the loss of RPMs during aging.

It was reported that the proportion of RPMs derived from bone marrow monocytes increases mildly but progressively during aging (Liu et al., 2019). This implies that due to the loss of the total RPM population, as illustrated by our data, the cells of embryonic origin are likely even more affected. We could confirm this assumption by re-analysis of the data from Liu et al. that we now included in the manuscript as Fig. 5E. These data clearly show that the representation of embryonically-derived RPMs drops more drastically than the percent of total RPMs, whereas the replenishment rate from monocytes is not affected significantly during aging. Consistent with this, we have not observed any robust change in the population of monocytes (F4/80-low, CD11b-high) or pre-RPMs (F4/80-high, CD11b-high) in the spleen at the age of 10 months (Figure 5-figure supplement 2A and B). We also have detected a mild decrease, not an increase, in the number of granulocytes (new Figure 5-figure supplement 2C). Furthermore, we measured in situ apoptosis marker and found a clear sign of apoptosis in the aged spleen (especially in the red pulp area), a phenotype that is less pronounced in mice on an IR diet (new Fig. 5O). This is consistent with the observation that apoptosis markers can be elevated in tissues upon ferroptosis induction (Friedmann Angeli et al., 2014) and that the proteotoxic stress in aged RPMs, which we now emphasized better in our manuscript, may also lead to apoptosis (Brancolini & Iuliano, 2020). Taken together, we strongly believe that the functional defect of embryonically-derived RPMs chiefly contributes to their shortage during aging.

3) Anemia of aging is a complex and poorly understood mechanistically. In general, it is considered similar to anemia of chronic inflammation with increased Epo, mild drop in Hb, and erythroid expansion, similar to ineffective erythropoiesis / low Epo responsiveness. It is not surprising that IR diet did not impact this mild anemia. However, was the MCV or MCH altered in aged and IR aged mice?

We now included the data for hematocrit, RBC counts, MCV, and MCH in Figure 1-figure supplement 5. Hematocrit shows a similar tendency as hemoglobin levels, but the values for RBC counts, MCV, and MCH seem not to be altered. We also show now that the erythropoietic activity in the bone marrow is not affected in aged versus young mice. Taken together, the anemic phenotype in female C57BL/6J mice at this age is very mild, which we emphasized in the main text, and is likely affected by other factors than serum iron levels (p. 6).

4) Page 6, line 23 onward: the conclusion is that KC compensate for the decreased function of RPM in the spleen, based on the expansion of KC fraction in the liver. Is there evidence that KCs are engaged in more erythrophagocytosis in aged mice? Furthermore, iron accumulation in the liver with age does not demonstrate specifically enhanced erythrophagocytosis of KC. Please clarify why liver iron accumulation would not be simply a consequence of increased parenchymal iron similar to increased splenic iron with age, independent of erythrophagocytic activity in resident macrophages in either organ.

Thanks for these questions. For the quantification of the erythrophagocytosis rate in KC, we show, as for the RPMs (Fig. 1K), the % of PKH67-positive macrophages, following transfusion of PKH67-stained stressed RBCs (Fig. 1M). The data implies a mild (not statistically significant) drop (of approx. 30%) in EP activity. We believe that it is overridden by a more pronounced (on average, 2-fold) increase in the representation of KCs (Fig. 1N). The mechanisms of iron accumulation between the spleen and the liver are very different. In the liver, we observed iron deposition in the parenchymal cells (not non-parenchymal, new Fig. 1P) that we currently characterizing in more detail in a parallel manuscript. Our data demonstrate a drop in transferrin saturation in aged mice. Hence, it is highly unlikely that aging would be hallmarked by the presence of circulating non-transferrin-bound iron that would be sequestered by hepatocytes, as shown previously (Jenkitkasemwong et al., 2015). Thus, the iron released locally by KCs is the most likely contributor to progressive hepatocytic iron loading during aging. The mechanism of iron delivery to hepatocytes from erythrophagocytosing KCs was demonstrated by Theurl et al.(Theurl et al., 2016), and we propose that it may be operational, although in a much more prolonged time scale, during aging. We now discussed this part better in our Results sections (p. 7).

5) Unclear whether the effect on RPMs is intrinsic or extrinsic. Would be helpful to evaluate aged iRPMs using young RBC vs. young iRPMs using old RBCs.

We are skeptical if the generation of iRPMs cells from aged mice would be helpful – these cells are a specific type of primary macrophage culture, derived from bone marrow monocytes with MCSF1, and exposed additionally to heme and IL-33 for 4 days. We do not expect that bone marrow monocytes are heavily affected by aging, and would thus recapitulate some aspects of aged RPMs from the spleen, especially after 8-day in vitro culture. However, to address the concerns of the reviewer, we now provide additional data regarding RBC fitness. Consistent with the time life-span experiment (Fig, 2A), we show that oxidative stress in RBCs is only increased in splenic, but not circulating RBCs (new Fig. 2C, replacing the old Fig. 2B and C). In addition, we show no signs of age-triggered iron loading in RBCs, either in the spleen (new Fig. 2F) or in the circulation (new Fig. 2B). Hence, we do not envision a possibility that RPMs become iron-loaded during aging as a result of erythrophagocytosis of iron-loaded RBCs. In support of this, we also have observed that during aging first RPMs’ FPN levels drop, afterward erythrophagocytosis rate decreases, and lastly, RBCs start to exhibit significantly increased oxidative stress (presented now in new Fig. 4H, J and K).

6) Discussion of aggregates in the spleen of aged mice (Fig 2G-2K and Fig 3) is very descriptive and non-specific. For example, if the iron-rich aggregates are hemosiderin, a hemosiderin-specific stain would be helpful. This data specifically is correlatory and difficult to extract value from.

Thanks for these comments. To the best of our knowledge Prussian blue Perls’ staining (Fig. 2J) is considered a hemosiderin staining. Our investigations aimed to better understand the nature and the origin of splenic iron deposits that to some extent are referred to as hemosiderin. Most importantly, as mentioned in our reply R1 Ad. 1. to assign causality to our data, we now demonstrated that iron accumulation in RPMs in response to iron-dextran (Fig. 3G) increases lipid peroxidation (Fig. 5F), tends to provoke RPMs depletion (Fig. 5G) and triggers the formation of protein-rich aggregates (new Fig. 3H). Of note, we assume that the loss of embryonically-derived RPMs in this model may be masked by simultaneous replenishment of the niche from monocytes, a phenomenon that may be addressed by future studies using Ms4a3-driven reporter mice (as shown for aged mice in our new Fig. 5E).

7) The aging phenotype in RPMs appears to be initiated sometime after 2 months of age. However, there is some reversal of the phenotype with increasing age, e.g. Fig 4B with decreased lipid peroxidation in 9 month old relative to 6 month old RPMs. What does this mean? Why is there a partial spontaneous normalization?

Thanks for this comment and questions. Indeed, the degree of lipid peroxidation exhibits some kinetics, suggestive of partial normalization. Of note, such a tendency is not evident for other aging phenotypes of RPMs, hence, we did not emphasize this in the original manuscript. However, in a revised version of the manuscript, we now present the re-analysis of the published data which implies that the number of embryonically-derived RPMs drops substantially between mice at 20 weeks and 36 weeks (new Fig. 5E). We think that the higher proportion of monocyte-derived RPMs in total RPM population later in aging (9 months) might be responsible for the partial alleviation of lipid peroxidation. We now discussed this possibility in the Results sections (p. 12).

8) Does the aging phenotype in RPMs respond to ferristatin? It appears that NAC, which is a glutathione generator and can reverse ferroptosis, does not reverse the decreased RPM erythrophagocytic capacity observed with age yet the authors still propose that ferroptosis is involved. A response to ferristatin is a standard and acceptable approach to evaluating ferroptosis.

We fully agree with the Reviewer that using ferristatin or Liproxstatin-1 would be very helpful to fully characterize a mechanism of RPMs depletion in mice. However, previous in vivo studies involving Liproxstatin-1 administration required daily injections of this ferroptosis inhibitor (Friedmann Angeli et al., 2014). This would be hardly feasible during aging. Regarding the experiments involving iron-dextran injection, using Liproxstatin-1 would require additional permission from the ethical committee which takes time to be processed and received. However, to address this question we now provide data from iRPMs cell cultures (new Fig.5 K-L). In essence, our results imply that both proteotoxic stress and iron overload act in concert to trigger cytotoxicity in RPM in vitro model. Interestingly, this phenomenon does not depend solely on the increased lipid peroxidation, but when we neutralize the latter with Liproxstatin-1, the cytotoxic effect is diminished (please, see also Results on p. 13 and Discussion p. 15/16).

9) The possible central role for HO-1 in the pathophysiology of decreased RPM erythrophagocytic capacity with age is interesting. However, it is not clear how the authors arrived at this hypothesis and would be useful to evaluate in the least whether RBCs in young vs. aged mice have more hemoglobin as these changes may be primary drivers of how much HO-1 is needed during erythrophagocytosis.

Thanks for this comment. We got interested in HO-1 levels based on the RNA sequencing data, which detected lower Hmox-1 expression in aged RPMs (Figure 3-figure supplement 1). We now show that the content of hemoglobin is not significantly altered in aged RBCs (MCH parameter, Figure 1-figure supplement 5E), hence we do not think that this is the major driver for Hmox-1 downregulation. Likewise, the levels of the Bach1 message, a gene encoding Hmox-1 transcriptional repressor, are not significantly altered according to RNAseq data. Hence, the reason for the transcriptional downregulation of Hmox-1 is not clear. Of note, HO-1 protein levels in the total spleen are higher in aged versus young mice, and we also detected a clear appearance of its nuclear truncated and enzymatically-inactive form (see a figure below, we opt not to include this in the manuscript for better clarity). The appearance of truncated HO-1 seems to be partially rescued by the IR diet. It is well established that the nuclear form of HO-1 emerges via proteolytic cleavage and migrates to the nucleus under conditions of oxidative stress (Mascaro et al., 2021). This additionally confirms that the aging spleen is hallmarked by an increased burden of ROS. Moreover, we also detected HO-1 as one of the components of the protein iron-rich aggregates. Thus, we propose that the low levels of the cytoplasmic enzymatically active form of HO-1 in RPMs (that we preferentially detect with our intracellular staining and flow cytometry) may be underlain by its nuclear translocation and sequestration in protein aggregates that evade antibody binding [this is also supported by our observation that the protein aggregates, despite the high content of ferritin (as indicated by MS analysis) are negative for L-ferritin staining. Of note, we also cannot exclude that other cell types in the aging spleen (eg. lymphocytes) express higher levels of HO-1 in response to splenic oxidative stress.

Fig. Total splenic levels of HO-1 in young, aged IR and aged mice.

Reviewer #2 (Public Review):

Slusarczyk et al. investigate the functional impairment of red pulp macrophages (RPMs) during aging. When red blood cells (RBCs) become senescent, they are recycled by RPMs via erythrophagocytosis (EP). This leads to an increase in intracellular heme and iron both of which are cytotoxic. The authors hypothesize that the continuous processing of iron by RPMs could alter their functions in an age-dependent manner. The authors used a wide variety of models: in vivo model using female mice with standard (200ppm) and restricted (25ppm) iron diet, ex vivo model using EP with splenocytes, and in vitro model with EP using iRPMs. The authors found iron accumulation in organs but markers for serum iron deficiency. They show that during aging, RPMs have a higher labile iron pool (LIP), decreased lysosomal activity with a concomitant reduction in EP. Furthermore, aging RPMs undergo ferroptosis resulting in a non-bioavailable iron deposition as intra and extracellular aggregates. Aged mice fed with an iron restricted diet restore most of the iron-recycling capacity of RPMs even though the mild-anemia remains unchanged.

Overall, I find the manuscript to be of significant potential interest. But there are important discrepancies that need to be first resolved. The proposed model is that during aging both EP and HO-1 expression decreases in RPMs but iron and ferroportin levels are elevated. In their model, the authors show intracellular iron-rich proteinaceous aggregates. But if HO-1 levels decrease, intracellular heme levels should increase. If Fpn levels increase, intracellular iron levels should decrease. How does LIP stay high in RPMs under these conditions? I find these to be major conflicting questions in the model.

We thank the Reviewer for her/his valuable feedback. As we mentioned in our replies we can only assume that a small misunderstanding in the interpretation of the presented data underlies this comment. We show that ferroportin levels in RPMs (Fig. 1F) are modulated in a manner that fully reflects the iron status of these cells (both labile and total iron levels, Figs. 1H and I). FPN levels drop in aged RPMs and are rescued when mice are maintained on a reduced iron diet. As pointed out by Reviewer#3, and explained in our replies we believe that ferroportin levels are critical for the observed phenotypes in aging. We now described our data in a more clear way to avoid any potential misinterpretation (p.6).

Reviewer #3 (Public Review):

This is a comprehensive study of the effects of aging of the function of red pulp macrophages (RPM) involved in iron recycling from erythrocytes. The authors document that insoluble iron accumulates in the spleen, that RPM become functionally impaired, and that these effects can be ameliorated by an iron-restricted diet. The study is well written, carefully done, extensively documented, and its conclusions are well supported. It is a useful and important addition for at least three distinct fields: aging, iron and macrophage biology.

The authors do not explain why an iron-restricted diet has such a strong beneficial effect on RPM aging. This is not at all obvious. I assume that the number of erythrocytes that are recycled in the spleen, and are by far the largest source of splenic iron, is not changed much by iron restriction. Is the iron retention time in macrophages changed by the diet, i.e. the recycled iron is retained for a short time when diet is iron-restricted (making hepcidin low and ferroportin high), and long time when iron is sufficient (making hepcidin high and ferroportin low)? Longer iron retention could increase damage and account for the effect. Possibly, macrophages may not empty completely of iron before having to ingest another senescent erythrocyte, and so gradually accumulate iron.

We are very grateful to this Reviewer for emphasizing the importance of the iron export capacity of RPMs as a possible driver of the observed phenotypes. Indeed, as mentioned above, we now show in the revised version of the manuscript that ferroportin drops early during aging (revised Fig. 4). Importantly, we now also observed that iron loading and limitation of iron export from iRPMs via ferroportin aggravate the impact of heat shock (a well-accepted trigger of proteotoxicity) on both protein aggregation and cell viability (new Fig. 5K and L). Physiologically, recent findings show that aging promotes a global decrease in protein solubility [BioRxiv manuscript (Sui X. et al., 2022)], and it is very likely that the constant exposure of RPMs to high iron fluxes renders these specialized cells particularly sensitive to proteome instability. This could be further aggravated by a build-up of iron due to the drop of ferroportin early during aging, ultimately leading to the appearance of the protein aggregates as early as at 5 months of age in C57BL/6J females. Based on the new data, we emphasized this model in the revised version of the manuscript (please, see Discussion on p. 16)

Author Response:

Reviewer #2:

Cai & Padoa-Schioppa recorded from macaque dorsal anterior cingulate cortex (ACCd) while requiring animals to choose between different juice types offered in variable amounts and with different action costs. Authors compared neural activity in ACCd (present study) with previous, directly comparable, findings on this same task when recording in macaque orbitofrontal cortex. The behavioral task is very powerful and the analyses of both the choice behavior and neural data are rigorous. Authors conclude that ACCd is unique in representing more post-decision variables and in its encoding of chosen value and binary outcome in several reference frames (chosen juice, chosen cost, and chosen action), not offer value, like OFC. Indeed, the encoding of choice outcomes in ACCd was skewed toward a cost-based reference frame. Overall, this is important new information about primate ACCd. I have only a few suggestions to enhance clarity. Figures 5 and 7 are maximally informative, but it is not clear that Figure 6 adds much to the reported Results. It is also suggested to abbreviate the comparison with Hosokawa et al. as it presently takes up 3 paragraphs in the Discussion: it is clear the methods and task designs were different enough to not be so easily compared with the present study. An additional suggestion would be to include mention of the comparison with OFC in the abstract and possibly also in the title, since the finding and direct comparison in Figure 7 are some of the most novel and interesting effects of the paper. Other suggestions are minor, and have to do with definition of time windows, variables, and additional papers that authors may cite for a well-rounded Discussion.

Please refer to Essential Revisions point #4. And we added “In contrast to the OFC” in the abstract to highlight the difference between these two regions.

Essential Revisions Point #4 Response:

We shortened the discussion from 3 paragraphs to 1 paragraph as follows.

"In another study, Hosokawa, Kennerley et al. (2013) compared the neuronal coding in ACCd and OFC in a choice task involving cost-benefit tradeoff. Our findings differ in two aspects. First, Hosokawa et. al. (2013) reported contralateral action value coding in ACCd while we did not discover significant offer value coding in either spatial- or action-based reference frames in our ACCd recordings. Second, they reported that there was no action-based value representation in the OFC therefore concluded that OFC does not integrate action cost in economic choice. Two elements may help explain the discrepancies between our findings in ACCd and OFC (Cai and Padoa-Schioppa 2019) and those of Hosokawa et. al. (2013). First, we recall that Hosokawa et. al. (2013) only tested value-related variables such as the benefit, cost and discounted value in action-based reference frame. Most importantly, they did not test the variable that is related to the saccade direction, which is highly correlated with the spatial value signal. As a consequence, contralateral value signal may not be significant if chosen target location was included in their regression analysis. Indeed, in our analysis, saccade direction (or chosen target location) was identified as one of the variables that explained a significant portion of neuronal activity in ACCd (Cai and Padoa-Schioppa 2012, Cai and Padoa-Schioppa 2019).The second and often overlooked aspect is that value may be encoded in schemes other than the action-based reference frame. In their study, each unique combination of reward quantity and cost was presented by a unique picture. Thus, information on good attributes were conveyed to the animal with an “integrated” visual representation. Accordingly, a distinct group of neurons may have been recruited to encode the reward and cost conjunctively represented by a unique fractal, which would result in 16 groups of offer value coding neurons."

Reviewer #3:

Cai and Padoa-Schioppa present a paper titled 'Neuronal Activity in Dorsal Anterior Cingulate Cortex during Economic Choices under Variable Action Costs'. They used a binary choice task where both offers indicated the reward type, reward amount, and the action cost (but not the specific action.) Variable action costs were then operationalized by placing targets on concentric circles of different radius. Here, and in a previous study that included OFC recordings (Cai and Padoa-Schioppa, 2019), monkeys integrated action costs into their decisions. Single-unit recordings in ACCd revealed that neurons predominantly coded for post-decision variables, such as cost of the chosen target and the juice type of the chosen offer, but not pre-decision variables, such as offer values. Given this finding, the authors compared the percentage of neurons in OFC and ACCd that coded for decision variables. In OFC neurons, the activity was mostly restricted to the offer presentation phase, whereas ACCd neurons showed sustained coding of chosen value and costs that lasted until the appearance of the saccade targets. Overall, this is an interesting study that provides evidence that decision-related signals evolve from coding offer values in the OFC to representing chosen costs in the ACC. This finding could highlight the roles of ACC neurons in learning and decision making. We have only a few questions.

1) Do any of the variables used in this study correlate with a conflict? When the authors previously studied ACC, they discarded the conflict monitoring hypothesis - a hypothesis that is well established for ACC hemodynamic responses - for ACC single cell activity based on neural data from 'difficult' decisions (Cai and Padoa-Schioppa, 2012). The definition of difficulty they used, then, was descriptive and based on reaction times (RTs). They defined the most difficult trials as those trials with the longest RTs and discovered that those trials had options with similar offer values. This definition of choice difficulty appears to be contrived from evidence accumulation models/tasks, where normatively harder judgments elicit longer RTs. However, there is no normative economic reason that trials with similar offer values are more difficult or should cause conflict. After all, according to theory, choosing between two options with the same value is as easy as flipping a coin. Here, it seems like the authors could have a more fitting definition of conflict. For example, conflict can be operationalized by considering trials when the animal must choose between a high value/high-cost option and a low-value/low-cost option. In that case, the costs and benefits are in conflict. What do the RTs look like? Do the RTs indicate conflict resolution? If so, is this reflected in neuronal responses?

We thank the reviewer for raising this important point. First, we would like to clarify that both in this study and in our previous study of ACC (Cai and Padoa-Schioppa 2012) we imposed a delay between offer presentation and the go signal. Such delay is critical to disentangle value comparison from action selection. However, the delay effectively dissociates reaction times from the decision difficulty. Normally, we operationalize the decision difficulty (or conflict) with the variable value ratio = chosen value / unchosen value. In an early behavioral study conducted in capuchin monkeys, where no delay was imposed between offer presentation and the go signal, we found that reaction times were strongly correlated with the value ratio, as one would naturally expect (Padoa-Schioppa, Jandolo et al. 2006). In the previous study of ACC (Cai and Padoa-Schioppa 2012) we referenced that earlier result but, again, we did not analyze reaction times.

Coming to the present study, we addressed this question by including in the variable selection analyses the two variables value ratio and cost/benefit conflict = cost of A * sign(offer value A – offer value B) (see also Table 2). The results of the updated analysis are illustrated in the new Figure 4, which we include here below. In essence, including these two variables did not affect the results of the variable selection analysis. That is, both the stepwise and best-subset methods selected the variables chosen value, chosen cost, chosen juice, chosen offer location only and chosen target location only.

Figure 4. Population summary of ANCOVA (all time windows). (A) Explained responses. Row and columns represent, respectively, time windows and variables. In each location, the number indicates the number of responses explained by the corresponding variable in that time window. For example, chosen value (juice) explained 34 responses in the post-offer time window. The same numbers are also represented in gray scale. Note that each response could be explained by more than one variable and thus could contribute to multiple bins in this panel. (B) Best fit. In each location, the number indicates the number of responses for which the corresponding variable provided the best fit (highest R2 in that time window. For example, chosen value (juice) provided the best fit for 40 responses in the late-delay time window. The numerical values are also represented in gray scale. In this plot, each response contributes to at most one bin.

2) The authors claimed that the ACCd neurons integrated juice identity, juice quantity and action costs later in the trial. As they acknowledge, the evidence for this claim is marginal. The conclusion the authors made in line 211, therefore, could be moderated. Given that the model containing cost-related variables is more complex, it is equally valid and more appropriately to write '… we cannot reject the null hypothesis that action cost was not integrated by chosen value responses later in the trial.

We acknowledge the complexity of this claim. However, results from previous studies (Kennerley, Dahmubed et al. 2009, Kennerley and Wallis 2009, Hosokawa, Kennerley et al. 2013) are in favor of establishing a null hypothesis of integration rather than non-integration. Therefore, we feel that it is more appropriate to keep the null hypothesis of cost integration while in the meantime acknowledging that in our study the evidence for cost integration is rather weak.

Author Response

Reviewer #1 (Public Review):

1) It would be helpful to include some sort of comparison in Fig. 4, e.g. the regressions shown in Fig 3, to indicate to what extent the ICCl data corresponds to the "control range" of frequency tuning.

Figure 4 was modified to show the frequency range typically found in the ICCls. This range is based on results from Wagner et al., 2007, which extensively surveyed ICCls responses. This modification shows that our ICCls recordings in the ruff-removed owls cover the normal frequency hearing range of the owl.

2) A central hypothesis of the study is that the frequency preference of the high-frequency neurons is lower in ruff-removed owls because of the lowered reliability caused by a lack of the ruff. Yet, while lower, the frequency range of many neurons in juvenile and ruff-removed owls seems sufficiently high to be still responsive at 7-8 kHz. I think it would be important to know to what extent neurons are still ITD sensitive at the "unreliable high frequencies" even if the CFs are lower since the "optimization" according to reliability depends not on the best frequency of each neuron per se, but whether neurons are less ITD sensitive at the higher, less reliable frequencies.

The concern regarding the frequency range that elicits responsivity was largely addressed above. Specifically, Figure L1 showing frequency tuning of frontally tuned ICx neurons in ruff-removed owls indicates that while there is some variability of tuning across neurons, there is little responsivity above 6 kHz. In contrast, equivalent analysis in juvenile owls (Figure L3), shows there is much more responsiveness and variability across neurons to high and low frequencies. This evidence supports our hypothesis that the juvenile owl brain is still highly plastic, which facilitates learning during development. Although the underlying data was already reported in Figure 7 of our previously submitted manuscript, we can include Figures L1 and L2, potentially as supplemental figures, if considered useful by editors and reviewers. Nevertheless, this argumentation was further expanded in the revised text (Line 229).

Figure L1. Frequency tuning of frontally-tuned ICx neurons in ruff-removed owls. Tuning curves are normalized by the max response. Thick black line indicates the average tuning curve. Dashed black line indicates basal response.

Figure L2. ITD sensitivity across frequencies in ruff-removed owl. Two example neurons shown in a and b. ITD tuning for tones (colored) and broadband (black) plotted by firing rate (non-normalized). Solid colored lines indicate responses to frequencies that are within the neuron’s preferred frequency range (i.e. above the half-height, see Methods), dashed lines indicate frequencies outside of the neuron’s frequency range.

Figure L3. Frequency tuning of frontally-tuned ICx neurons in juvenile owls. Tuning curves are normalized by the max response. Thick black line indicates the average tuning curve. Dashed black line indicates basal response.

3) It would be interesting to have an estimate of the time scale of experience dependency that induces tuning changes. Do the authors have any data on this question? I appreciate the authors' notion that the quantifications in Fig 7 might indicate that juvenile owls are already "beginning to be shaped by ITD reliability" (line 323 in Discussion). How many days after hearing onset would this correspond to? Does this mean that a few days will already induce changes?

While tracking changes induced by ruff-removal over development were outside of the scope of this study, many other studies have assessed experience-dependent plasticity in the barn owl. The recordings in this study were performed approximately 20 days after hearing onset, suggesting that the juveniles had ample time to begin learning. These points were expanded upon in the discussion (Lines 254, 280-283).

Reviewer #2 (Public Review):

1) Why is IPD variability plotted instead of ITD variability (or indeed spatial reliability)? The relationship between these measures is likely to vary across frequency, which makes it difficult to compare ITD variability across frequency when IPDs are plotted. Normalizing data across frequencies also makes it difficult to compare different locations and acoustical conditions. For example, in Fig.1a and Fig.1b, the data shown for 3 kHz at ~160 degrees seems quantitatively and visually quite different, but the difference (in Fig.1c) appears to be negligible.

Justification of why IPD variability is used as an estimate of ITD variability was added to introduction (Lines 55-60), results (Line 100) and methods (Lines 371-374) sections of the manuscript, explaining the fact that because ITD detection is based on phase locking by auditory nerve and ITD detector neurons tuned to narrow frequency bands, responses of ITD detector neurons forwarded to downstream midbrain regions are therefore determined by IPD variability. Additionally, ITD is calculated by dividing IPD by frequency, which makes comparisons of ITD reliability across frequency mathematically uninformative.

2) How well do the measures of ITD reliability used reflect real-world listening? For example, the model used to calculate ITD reliability appears to assume the same (flat) spectral profile for targets and distractors, which are presented simultaneously with the same temporal envelope, and a uniform spatial distribution of sounds across space. It is therefore unclear how robust the study's results are to violations of these assumptions.

While we agree that our analysis cannot completely capture real-world listening for the barn owl, a general analysis using similar flat spectral profiles for targets and concurrent sounds provides a broad assessment of reliability of ITD cues. While a full recapitulation of real-world listening is beyond the scope of this study (i.e. recording natural scenes from the ear canals of wild barn owls), we included additional analyses of ITD reliability in Figure 1-figure supplement 1, described above.

3) Does facial ruff removal produce an isolated effect on ITD variability or does it also produce changes in directional gain, and the relationship between spatial cues and sound location? Although the study considers this issue in some places (e.g. Fig.2, Fig.5), a clearer presentation of the acoustical effects of facial ruff removal and their implications (for all locations, not just those to the front), as well as an attempt to understand how these acoustical changes lead to the observed changes in ITD reliability, would greatly strengthen the study. In addition, Fig.1 shows average ITD reliability across owls, but it would be helpful to know how consistent these measures are across owls, given individual variability in Head-Related Transfer Functions (HRTFs). This potentially has implications for the electrophysiological experiments, if the HRTFs of those animals were not measured. One specific question that is potentially very relevant is whether the facial ruff attenuates sounds presented behind the animal and whether it does so in a frequency-dependent way. In addition, if facial ruff removal enables ILDs to be used for azimuth, then ITDs may also become less necessary at higher frequencies, even if their reliability remains unchanged.

Additional analysis was conducted to generate representation of changes in directional gain induced by ruff removal, added to new figure (Fig 5). This analysis shows that changes in gain following ruff-removal are largely frequency-independent: there is a de-attenuation of peripherally and rearwardly located sounds, but the highest gain remains for high frequencies in frontal space. There is an additional increase in gain for high frequencies from rearward space, these changes would not explain the changes in frequency tuning we report. As mentioned in new additions to the manuscript, the changes at the most rearward-located auditory spatial locations are unlikely to have an effect on the auditory midbrain. No studies in the barn owl have found neurons in the ICx or optic tectum tuned to >120° (Knudsen, 1982; Knudsen, 1984; Cazettes et al., 2014). In addition, variability of IPD reliability across owls was analyzed and reported in the amended Figure 1, which notes very little changes across owls. In this analysis, we did realize that the file of one of the HRTFs obtained from von Campenhausen et al. 2006 was mislabeled, which explains slight differences in revised Fig 1b. Nevertheless, added analysis of IPD reliability across owls indicates that the pattern in ITD reliability is stable across owls (Fig. 1d,e), which supports our decision to not record HRTFs from owls used in this study. Finally, we added to the discussion that clarifies that the use of ILD for azimuth would not provide the same resolution as ITD would (Lines 295-303). We also do not believe that the use of ILD for azimuth would make “ITDs… less necessary at higher frequencies”, given that the ICCls is still computing ITD at these high frequencies (Fig 4), and that ILDs also have higher resolution at higher frequencies, with and without the facial ruff (Olsen et al, 1989; Keller et al., 1998; von Campenhausen et al., 2006).

1) It is unclear why some analyses (Fig.5, Fig.7) are focused on frontal locations and frontally-tuned neurons. It is also unclear why neurons with a best ITDs of 0 are described as frontally tuned since locations behind the animal produce an ITD of 0 also. Related to this, in Fig.1, facial ruff removal appears to reduce IPD variability at low frequencies for locations to the rear (~160 degrees), where the ITD is likely to be close to 0. Neurons with a best ITD of 0 might therefore be expected to adjust their frequency tuning in opposite directions depending on whether they are tuned to frontal or rearward locations.

An extensive explanation was added to the methods detailing why we do not believe the neurons recorded in this study are tuned to the rear. Namely, studies mapping the barn owl’s ICx and optic tectum have not reported neurons tuned to locations >120°, with the number of neurons representing a given spatial location decreasing with eccentricity (Knudsen, 1982; Knudsen, 1984; Cazettes et al., 2014). While we agree that there does seem to be a change in ITD reliability at ~160° following ruff-removal, the result is largely similar to the change that occurs in frontal space (Fig 1b), which is consistent with the ruff-removed head functioning as a sphere. Thus, we wouldn’t expect rearwardly-tuned neurons, if they could be readily found, to adjust their frequency tuning to higher frequencies. Finally, we want to clarify that we focused our analyses on frontally-tuned neurons because frontal space is where we observed the largest change in ITD reliability. Text was added to the Discussion section to clarify this point (Lines 313-321).

2) The study suggests that information about high-frequency ITDs is not passed on to the ICX if the ICX does not contain neurons that have a high best frequency. However, neurons might be sensitive to ITDs at frequencies other than the best frequency, particularly if their frequency tuning is broader. It is also unclear whether the best frequency of a neuron always corresponds to the frequency that provides the most reliable ITD information, which the study implicitly assumes.

The concern about ITD sensitivity at non-preferred frequencies was addressed under the essential revision #3, as well as under Reviewer 1’s concerns.

Author Response

Reviewer #1 (Public Review):

This manuscript reports a systematic study of the cortical propagation patterns of human beta bursts (~13-35Hz) generated around simple finger movements (index and middle finger button presses).

The authors deployed a sophisticated and original methodology to measure the anatomical and dynamical characteristics of the cortical propagation of these transient events. MEG data from another study (visual discrimination task) was repurposed for the present investigation. The data sample is small (8 participants). However, beta bursts were extracted over a +/- 2s time window about each button press, from single trials, yielding the detection and analysis of hundreds of such events of interest. The main finding consists of the demonstration that the cortical activity at the source of movement related beta bursts follows two main propagation patterns: one along an anteroposterior directions (predominantly originating from pre central motor regions), and the other along a medio- lateral (i.e., dorso lateral) direction (predominantly originating from post central sensory regions). Some differences are reported, post-hoc, in terms of amplitude/cortical spread/propagation velocity between pre and post-movement beta bursts. Several control tests are conducted to ascertain the veracity of those findings, accounting for expected variations of signal-to-noise ration across participants and sessions, cortical mesh characteristics and signal leakage expected from MEG source imaging.

One major perceived weakness is the purely descriptive nature of the reported findings: no meaningful difference was found between bursts traveling along the two different principal modes of propagation, and importantly, no relation with behavior (response time) was found. The same stands for pre vs. post motor bursts, except for the expected finding that post-motor bursts are more frequent and tend to be of greater amplitude (yielding the observation of a so-called beta rebound, on average across trials).

Overall, and despite substantial methodological explorations and the description of two modes of propagation, the study falls short of advancing our understanding of the functional role of movement related beta bursts.

For these reasons, the expected impact of the study on the field may be limited. The data is also relatively limited (simple button presses), in terms of behavioral features that could be related to the neurophysiological observations. One missed opportunity to explain the functional role of the distinct propagation patterns reports would have been, for instance, to measure the cortical "destination" of their respective trajectories.

In response to this comment, we would like to highlight two important points.

First, our work constitutes the first non-invasive human confirmation of invasive work in animals (Balasubramanian et al., 2020; Roberts et al., 2019; Rule et al., 2018; (Balasubramanian et al., 2020; Best et al., 2016; Rubino et al., 2006; Takahashi et al., 2011, 2015) and patients (Takahashi et al., 2011). Thus, these results bridges between recordings limited to the size of multielectrode arrays (roughly 0.16 cm2; Balasubramanian et al., 2020; Best et al., 2016; Rubino et al., 2006; Takahashi et al., 2011, 2015) and human EEG recordings spanning across large areas of the cortex and several functionally distinct regions (Alexander et al., 2016; Stolk et al., 2019). The ability to access these neural signatures non- invasively is important for cross-species comparison. This further enables us, to provide an in-depth analysis of the spatiotemporal diversity of human MEG signals and a detailed characterisation of the two propagation directions, which significantly extends previous reports. We note that their functional role remains undetermined also in these animal studies, but being able to identify these signals now in humans can provide a steppingstone for identifying their role.

Second, and related, the reviewers are correct that we did not observe distinct propagation directions between pre- and post-movement bursts, nor a relationship with reaction time. However, such a null result would be relevant, in our view, towards understanding what the functional relevance of these signals, if any, might be. Recent work in macaques indicates that the spatiotemporal patterns of high-gamma activity carry kinematic information about the upcoming movement (Liang et al 2023). The functional role of beta may therefore be more complex and not relate to reaction times or kinematics in a straightforward manner. We believe this is a relevant observation, and in keeping with the continued efforts to identify how sensorimotor beta relates to behaviour. It is increasingly clear that spatiotemporal diversity in animal recordings and human E/MEG and intracranial recordings can constitute a substantial proportion of the measured dynamics. As such, our report is relevant in narrowing down what these signals may reflect.

Together, we think that our work provides new insights into the multidimensional and propagating features of burst activity. This is important for the entire electrophysiology community, as it transforms how we commonly analyse and interpret these important brain signals. We anticipate that our work will guide and inspire future work on the mechanistic underpinnings of these dominant neural signals. We are confident that our article has the scope to reach out to the diverse readership of eLife.

Reviewer #2 (Public Review):

The authors devised novel and interesting experiments using high precision human MEG to demonstrate the propagation of beta oscillation events along two axes in the brain. Using careful analysis, they show different properties of beta events pre- and post movement, including changes in amplitude. Due to beta's prominent role in motor system dynamics, these changes are therefore linked to behavior and offer insights into the mechanisms leading to movement. The linking of wave-like phenomena and transient dynamics in the brain offers new insight into two paradigms about neural dynamics, offering new ways to think about each phenomena on its own.

Although there is a substantial, and recent, body of literature supporting the conclusions that beta and other neural oscillations are transient, care must be taken when analyzing the data and the resulting conclusions about beta properties in both time and space. For example, modifying the threshold at which beta events are detected could alter their reported properties and expression in space and time. The authors should therefore performing parameter sweeps on e.g. the thresholds for detection of oscillation bursts to determine whether their conclusions on beta properties and propagation hold. If this additional analysis does not change their story, it would lend confidence in the results/conclusions.

We thank the reviewing team for this comment. As suggested, we evaluated the effect of different burst thresholds on the burst parameters.

The threshold in the main analysis was determined empirically from the data, as in previous work (Little et al., 2019). Specifically, trial-wise power was correlated with the burst probability across a range of different threshold values (from median to median plus seven standard deviations (std), in steps of 0.25, see Figure 6-figure supplement 1). The threshold value that retained the highest correlation between trial-wise power and burst probability was used to binarize the data.

We repeated our original analysis using four additional thresholds, i.e., original threshold - 0.5 std, -0.25 std, +0.25 std, +0.5 std. As one would expect, burst threshold is negatively related to the number of bursts (i.e., higher thresholds yield fewer bursts, Figure R4a [top]), and positively related to burst amplitude (i.e., higher thresholds yield higher burst amplitudes, Figure R4a [bottom]).

Similarly, the temporal duration of bursts and apparent spatial width are modulated by the burst threshold: lowering the threshold leads to longer temporal duration and larger apparent spatial width while increasing the threshold leads to shorter temporal duration and smaller apparent spatial width Figure R4b. Note that for the temporal and spectral burst characteristics, the difference to the original threshold can be numerically zero, i.e., changing the burst threshold did not lead to changes exceeding the temporal and spectral resolution of the applied time-frequency transformation (i.e., 200ms and 1Hz respectively).

Importantly, across these threshold values, the propagation direction and propagation speed remain comparable.

We now include this result as Figure 6-figure supplement 2and refer to this analysis in the manuscript (page 28 line 717).

“To explore the robustness of the results analyses were repeated using a range of thresholds (Figure 6-figure supplement 2).”

Determining the generators of beta events at different locations is a tricky issue. The authors mentioned a single generator that is responsible for propagating beta along the two axes described. However, it is not clear through what mechanism the beta events could travel along the neural substrate without additional local generators along the way. Previous work on beta events examined how a sequence of synaptic inputs to supra and infragranular layers would contribute to a typical beta event waveform. Although it is possible other mechanisms exist, how might this work as the beta events propagate through space? Some further explanation/investigation on these issues is therefore warranted.

Based on this and other comments (i.e., comments 7 and 8) we re-evaluated the use of the term ‘generator’ in this manuscript.

While the term generator can be used across scales, from micro- to macroscale, ifor the purpose of the present paper, we believe one should differentiate at least two concepts: a) generator of beta bursts, and b) generator of travelling waves.

We realised that in the previous version of the manuscript the term ‘generator’ was at times used without context. We removed the term where no longer necessary.

Further, the previous version of the manuscript discussed putative generators of travelling waves (page 19f.) but not generators of beta bursts. We now address this as follows:

“Studies using biophysical modelling have proposed that beta bursts are generated by a broad infragranular excitatory synaptic drive temporally aligned with a strong supragranular synaptic drive (Law et al., 2022; Neymotin et al., 2020; Sherman et al., 2016; Shin et al., 2017) whereby layer specific inhibition acts to stabilise beta bursts in the temporal domain (West et al., 2023). The supragranular drive is thought to originate in the thalamus (E. G. Jones, 1998, 2001; Mo & Sherman, 2019; Seedat et al., 2020), indicating thalamocortical mechanisms (page 22f).”

Once the mechanisms have been better understood, a question of how much the results generalize to other oscillation frequencies and other brain areas. On the first question of other oscillation frequencies, the authors could easily test whether nearby frequency bands (alpha and low gamma) have similar properties. This would help to determine whether the observations/conclusions are unique to beta, or more generally applicable to transient bursts/waves in the brain. On the second issue of applicability to other brain areas, the authors could relate their work to transient bursts and waves recorded using ECoG and/or iEEG. Some recent work on traveling waves at the brain-wide level would be relevant for such comparisons.

We appreciate the enthusiasm and the suggestions. To comment on the frequency specificity of the observed effects we conducted the same analysis focusing on the gamma frequency range (60-90 Hz). For computational reasons, we limited this analysis to one subject. Figure R1 shows the polar probability histogram for the beta frequency range (left) and the gamma frequency range (right). In contrast to the beta frequency range, no dominant directions were observed for the gamma range and von Mises functions did not converge. These preliminary results suggest some frequency specificity of the spatiotemporal pattern in sensorimotor beta activity. We believe this paves the way for future analysis mapping propagation direction across frequency and space.

Here we did not investigate the spatial specificity of the effects, as the beta frequency range is dominant in sensorimotor areas. Investigating beta bursts in other cortical areas would have likely resulted in very few bursts. We discuss our results across spatial scales in the section: Distinct anatomical propagation axes of sensorimotor beta activity. However, please note that most of the previous literature operates on a different spatial scale (roughly 4mm; Balasubramanian et al., 2020; Best et al., 2016; Rubino et al., 2006; Rule et al., 2018; Takahashi et al., 2011, 2015) and different species (e.g., non-human primates). Non-invasive recordings in humans capture temporospatial patterns of a very different scale, i.e., often across the whole cortex (Alexander et al., 2016; Roberts et al., 2019). Comparing spatiotemporal patterns, across different spatial scales is inherently difficult. Work

investigating different spatial scales simultaneously, such as Sreekumar et al. 2020, is required to fully unpack the relationship between mesoscopic and macroscopic spatiotemporal patterns.

Figure R1: Spatiotemporal organisation for the beta (β, 13-30Hz) and gamma (γ, 60-90) frequency range for one exemplar subject. Same as Figure 4a, but for one exemplar subject.

If the source code could be provided on github along with documentation and a standard "notebook" on use other researchers would benefit greatly.

All analyses are performed using freely available tools in MATLAB. The code carrying out the analysis in this paper can be found here: [link provided upon acceptance]. The 3D burst analyses can be very computationally intensive even on a modern computer system. The analyses in this paper were computed on a MacBook Pro with a 2.6 GHz 6-Core Intel Core i7 and 32 Gb of RAM. Details on the installation and setup of the dependencies can be found in the README.md file in the main study repository.

This information has been added to the paper in the methods section on page 35.

Author Response

Reviewer #1 (Public Review):

This manuscript provides a comprehensive investigation of the effects of the genetic ablation of three different transcription factors (Srf, Mrtfa, and Mrtfb) in the inner ear hair cells. Based on the published data, the authors hypothesized that these transcription factors may be involved in the regulation of the genes essential for building the actin-rich structures at the apex of hair cells, the mechanosensory stereocilia and their mechanical support - the cuticular plate. Indeed, the authors found that two of these transcription factors (Srf and Mrtfb) are essential for the proper formation and/or maintenance of these structures in the auditory hair cells. Surprisingly, Srf- and Mrtfb- deficient hair cells exhibited somewhat similar abnormalities in the stereocilia and in the cuticular plates even though these transcription factors have very different effects on the hair cell transcriptome. Another interesting finding of this study is that the hair cell abnormalities in Srfdeficient mice could be rescued by AAV-mediated delivery of Cnn2, one of the downstream targets of Srf. However, despite a rather comprehensive assessment of the novel mouse models, the authors do not have yet any experimentally testable mechanistic model of how exactly Srf and Mrtfb contribute to the formation of actin cytoskeleton in the hair cells. The lack of any specific working model linking Srf and/or Mrtfb with stereocilia formation decreases the potential impact of this study.

Major comments:

Figures 1 & 3: The conclusion on abnormalities in the actin meshwork of the cuticular plate was based largely on the comparison of the intensities of phalloidin staining in separate samples from different groups. In general, any comparison of the intensity of fluorescence between different samples is unreliable, no matter how carefully one could try matching sample preparation and imaging conditions. In this case, two other techniques would be more convincing: 1) quantification of the volume of the cuticular plates from fluorescent images; and 2) direct examination of the cuticular plates by transmission electron microscopy (TEM).

In fact, the manuscript provides no single TEM image of the F-actin abnormalities either in the cuticular plate or in the stereocilia, even though these abnormalities seem to be the major focus of the study. Overall, it is still unclear what exactly Srf or Mrtfb deficiencies do with F-actin in the hair cells.

Yes, we agree. As suggested by the reviewer, to directly examine the defects in F-actin organization within the cuticular plate of mutant mice, we conducted Transmission Electron Microscopy (TEM) analyses. The results, as presented in the revised Figures 1 and 4 (panels F, G, and E, F, respectively), provide crucial insights into the structural changes in the cuticular plate. Meanwhile, the comparison of the volume of the phalloidin labeled cuticular plate after 3-D reconstruction using Imaris software was conducted and shown in Author response image 1. The results of the cuticular plate (CP) volume were consistent with the relative F-actin intensity change of the cuticular plate in the revised Figures 1B and 4B. For the TEM analysis of the stereocilia, we regret that due to time constraints, we were unable to collect TEM images of stereocilia with sufficient quality for a meaningful comparison. However, we believe that the data we have presented sufficiently addresses the primary concerns, and we appreciate the reviewers’ understanding of these limitations.

Author response image 1.

Figures 2 & 4 represent another example of how deceiving could be a simple comparison of the intensity of fluorescence between the genotypes. It is not clear whether the reduced immunofluorescence of the investigated molecules (ESPN1, EPS8, GNAI3, or FSCN2) results from their mis-localization or represents a simple consequence of the fact that a thinner stereocilium would always have a smaller signal of the protein of interest, even though the ratio of this protein to the number of actin filaments remains unchanged. According to my examination of the representative images of these figures, loss of Srf produces mis-localization of the investigated proteins and irregular labeling in different stereocilia of the same bundle, while loss of Mrtfb does not. Obviously, a simple quantification of the intensity of fluorescence conceals these important differences.

Yes, we agree. In addition to the quantification of tip protein intensity, we have added a few more analyses in the revised Figure 3 and Figure 6, such as the percentage of row 1 tip stereocilia with tip protein staining and the percentage of IHCs with tip protein staining on row 2 tip. Using the results mentioned above, the differences in the expression level, the row-specific distribution and the irregular labeling of tip proteins between the control and the mutants can be analyzed more thoroughly.

Reviewer #2 (Public Review):

The analysis of bundle morphology using both confocal and SEM imaging is a strength of the paper and the authors have some nice images, especially with SEM. Still, the main weakness is that it is unclear how significant their findings are in terms of understanding bundle development; the mouse phenotypes are not distinct enough to make it clear that they serve different functions so the reader is left wondering what the main takeaway is.

Based on the reviewer’s comments, in this revised manuscript, we put more emphasis on describing the effects of SRF and MRTFB on key tip proteins’ localization pattern during stereocilia development, represented by ESPN1, EPS8 and GNAI3, as well as the effects of SRF and MRTFB on the F-actin organization of cuticular plate using TEM. We have made substantial efforts to interpret the mechanistic underpinnings of the roles of SRF and MRTFB in hair cells. This is reflected in the revised Figures 1, 3, 4, 6, and 10, where we provide more comprehensive insights into the mechanisms at play.

We interpret our data in a way that both SRF and MRTF regulate the development and maintenance of the hair cell’s actin cytoskeleton in a complementary manner. Deletion of either gene thus results in somewhat similar phenotypes in hair cell morphology, despite the surprising lack of overlap of SRF and MRTFB downstream targets in the hair cell.

In Figure 1 and 3, changes in bundle morphology clearly don't occur until after P5. Widening still occurs to some extent but lengthening does not and instead the stereocilia appear to shrink in length. EPS8 levels appear to be the most reduced of all the tip proteins (Srf mutants) so I wonder if these mutants are just similar to an EPS8 KO if the loss of EPS8 occurred postnatally (P0-P5).

To address this question, we performed EPS8 staining on the control and Srf cKO hair cells at P4 and P10. We found that the dramatic decrease of the row 1 tip signal for EPS8 started since P4 in Srf cKO IHCs. Although the major hair bundle phenotype of Eps8 KO, including the defects of row 1 stereocilia lengthening and additional rows of short stereocilia also appeared in Srf cKO IHCs, there are still some bundle morphology differences between Eps8 KO and Srf cKO. For example, firstly, both Eps8 KO OHCs and IHCs showed additional rows of short stereocilia, but we only observed additional rows of short stereocilia in Srf cKO IHCs. Secondly, in Valeria Zampini’s study, SEM and TEM images did not show an obvious reduction of row 2 stereocilia widening (P18-P35), while our analysis of SEM images confirmed that the width of row 2 IHC stereocilia was drastically reduced by 40% in Srf cKO (P15). Generally, we think although Srf cKO hair bundles are somewhat similar to Eps8 KO, the Srf cKO hair bundle phenotype might be governed by multiple candidate genes cooperatively.

Reference:

Valeria Zampini, et al. Eps8 regulates hair bundle length and functional maturation of mammalian auditory hair cells. PLoS Biol. 2011 Apr;9(4): e1001048.

A major shortcoming is that there are few details on how the image analyses were done. Were SEM images corrected for shrinkage? How was each of the immunocytochemistry quantitation (e.g., cuticular plates for phalloidin and tip staining for antibodies) done? There are multiple ways of doing this but there are few indications in the manuscript.

We apologize for not making the description of the procedure of images analyses clear enough. As described in Nicolas Grillet group’s study, live and mildly-fixed IHC stereocilia have similar dimensions, while SEM preparation results in a hair bundle at a 2:3 scale compared to the live preparation. In our study, the hair cells selected for SEM imaging and measurements were located in the basal turn (30-32kHz), while the hair cells selected for fluorescence-based imaging and measurements were located in the middle turn (20-24kHz) or the basal turn (32-36kHz). Although our SEM imaging and fluorescence-based imaging of basal turn’s hair bundles were not from the same area exactly, the control hair bundles with SEM imaging have reduced row 1 stereocilia length by 10%-20%, compared to the control hair bundles with fluorescence-based imaging (revised Figure 2 and Figure 5). Generally, our stereocilia dimensions data showed appropriate shrinkage caused by the SEM preparation.

Recognizing the need for clarity, we have provided a detailed description of our image quantification and analysis procedures in the “Materials and Methods” section, specifically under “Immunocytochemistry.” This will aid readers in understanding our methodologies and ensure transparency in our approach.

Reference:

Katharine K Miller, et al. Dimensions of a Living Cochlear Hair Bundle. Front Cell Dev Biol. 2021 Nov 25:9:742529.

The tip protein analysis in Figs 2 and 4 is nice but it would be nice for the authors to show the protein staining separately from the phalloidin so you could see how restricted to the tips it is (each in grayscale). This is especially true for the CNN2 labeling in Fig 7 as it does not look particularly tip specific in the x-y panels. It would be especially important to see the antibody staining in the reslices separate from phalloidin.

Thank you for the suggestions. We have shown tip proteins staining in grayscale separately from the phalloidin in the revised Figure 3 and Figure 6. To clearly show the tip-specific localization of CNN2, we conducted CNN2 staining at different ages during hair bundle development and showed CNN2 labeling in grayscale and in reslices in revised Figure 9-figure supplement 1B.

In Fig 6, why was the transcriptome analysis at P2 given that the phenotype in these mice occurs much later? While redoing the transcriptome analysis is probably not an option, an alternative would be to show more examples of EPS8/GNAI/CNN2 staining in the KO, but at younger ages closer to the time of PCR analysis, such as at P5. Pinpointing when the tip protein intensities start to decrease in the KOs would be useful rather than just showing one age (P10).

We agree with the reviewer. To address this question, we have performed ESPN1, EPS8 and GNAI3 staining on the control and the mutant’s hair cells at P4, P10 and P15 (the revised Figures 3 and 6). According to the new results, we found that the dramatic decreases of the row 1 tip signal for ESPN1 and EPS8 started since P4 in Srf cKO IHCs, is consistent with the appearance of the mild reduction of row 1 stereocilia length in P5 Srf cKO IHCs. For Mrtfb cKO hair cells, the obvious reduction of the row 1 tip signal for ESPN1 was observed until P10. However, a few genes related to cell adhesion and regulation of actin cytoskeleton were significantly down-regulated in P2 Mrtfb deficient hair cell transcriptome. We think that in hair cells the MRTFB may not play a major role in the regulation of stereocilia development, so the morphological defects of stereocilia happened much later in the Mrtfb mutant than in the Srf mutant.

While it is certainly interesting if it turns out CNN2 is indeed at tips in this phase, the experiments do not tell us that much about what role CNN2 may be playing. It is notable that in Fig 7E in the control+GFP panel, CNN2 does not appear to be at the tips. Those images are at P11 whereas the images in panel A are at P6 so perhaps CNN2 decreases after the widening phase. An important missing control is the Anc80L65-Cnn2 AAV in a wild-type cochlea.

We agree with the reviewer. We have conducted more immunostaining experiments to confirm the expression pattern of CNN2 during the stereocilia development, from P0 to P11. The results were included in the revised Figure 9-figure supplement 1B. As the reviewer suggested, CNN2 expression pattern in control cochlea injected with Anc80L65-Cnn2 AAV has also been provided in revised Figure 9E.

Author Response

Reviewer #1 (Public Review):

This is an awesome comprehensive manuscript. Authors start by sorting putative stromal cellcontaining BM non-hematopoietic (CD235a-/CD45-) plus additional CD271+/CD235a/CD45- populations to identify nine individual stromal identities by scRNA-seq. The dual sorting strategy is a clever trick as it enriches for rare stromal (progenitor) cell signals but may suffer a certain bias towards CD271+ stromal progenitors. The lack of readable signatures already among CD45-/CD45- sorts might argue against this fear. This reviewer would appreciate a brief discussion on number & phenotype of putative additional MSSC phenotypes in light of the fact that the majority of 'blood lineage(s)'-negative scRNA-seq signatures identified blood cell progenitor identities (glycophorin A-negative & leukocyte common antigen-negative). The nine stromal cell entities share the CXCL12, VCAN, LEPR main signature. Perhaps the authors could speculate if future studies using VCAN or LEPRbased sort strategies could identify additional stromal progenitor identities?

We would like to thank the reviewer for critically evaluating our work and for the generally positive evaluation of the paper. We apologize for delayed resubmission as it took a long time for a specific antibody to arrive to complete the confocal microscopy analyses.

The reviewer asks for a brief discussion on the cell numbers and phenotypes of MSSC phenotypes. The cell numbers and percentages of MSSC in sorted CD45low/-CD235a- and CD45low/-CD235a-CD271+ cells can be found in Supplementary File 3 and we have added a summary of the phenotypes of MSSC in the new Supplementary File 7.

Due to the extremely low frequency of stromal cells in human bone marrow, we chose a sorting strategy that also included CD45low cells (Fig 1A) to ensure that no stromal cells were excluded from the analysis. Although stromal elements are certainly enriched using this approach, the CD45low population contains several different hematopoietic cell types. These include CD34+ HSPCs which are characterized by low CD45 expression2, as well as the CD45low-expressing fractions of other hematopoietic cell populations such as B cells, T cells, NK cells, megakaryocytes, monocytes, dendritic cells, and granulocytes. Furthermore, CD235a- late-stage erythroid progenitors, which are negative for CD45, are represented as well. Of note, our data are consistent with previously reported murine studies showing the presence of a number of hematopoietic populations in CD45- cells, which accounted for the majority of CD45-Ter119-CD31- murine BM cells3,4. However, despite a certain enrichment of stromal elements in the CD45low cell fraction, frequencies were still too low to allow for a detailed analysis of this important bone marrow compartment. This prompted us to adopt the stromal cell-enrichment strategy as described in the manuscript to achieve a better resolution of the stromal compartment. In fact, sorting based on CD45low/-CD235a-CD271+ allowed us to sufficiently enrich bone marrow stromal cells to be clearly detectable in scRNAseq analysis. According to the reviewer’s suggestion, a brief discussion on this issue is now included in the Discussion (page 28, lines 10-15).

The reviewer also suggested using VCAN or LEPR-based sorting strategy to identify additional stromal identities in future studies.

However, as an extracellular matrix protein, FACS analysis of cellular VCAN expression can only be achieved based on its intracellular expression after fixation and permeabilization5,6. Additionally, while VCAN is highly and ubiquitously expressed by stromal clusters, VCAN is also expressed by monocytes (cluster 36). Therefore, VCAN is not an optimal marker to isolate viable stromal cells.

LEPR is the marker that was reported to identify the majority of colony-forming cells in adult murine bone marrow7. We have previously reported that the majority of human adult bone marrow CFU-Fs is contained in the LEPR+ fraction 8. In our current scRNAseq surface marker profiling analysis, group A cells showed high expression of several canonical stromal markers including VCAM1, PDGFRB, ENG (CD73), as well as LEPR (Fig. 4A). However, the four stromal clusters in Group A could not be separated based on the expression of LEPR. Therefore, we chose not to use LEPR as a marker to prospectively isolate the different stromal cell types.

The authors furthermore localized CD271+, CD81+ and NCAM/CD56+ cells in BM sections in situ. Finally, referring to the strong background of the group in HSC research, in silico prediction by CellPhoneDB identified a wide range of interactions between stromal cells and hematopoietic cells. Evidence for functional interdependence of FCU-F forming cells is completing the novel and more clear bone marrow stromal cell picture.

We thank the reviewer for the positive comments.

An illustrative abstract naming the top9 stromal identities in their top4 clusters by their "top10 markers" + functions would be highly appreciated.

We thank the reviewer for the suggestion. A summary of the characteristics of stromal clusters is now shown in the new Supplementary File 7, which we hope matches the reviewer’s expectations.

Reviewer #2 (Public Review):

Knowledge about composition and function of the different subpopulations of the hematopoietic niche of the BM is limited. Although such knowledge about the mouse BM has been accumulating in recent years, a thorough study of the human BM still needs to be performed. The present manuscript of Li and coworkers fills this gap by performing single cell RNA sequencing (scRNAseq) on control BM as well as CD271+ BM cells enriched for non-hematopoietic niche cells.

We apologize for delayed resubmission as it took a long time for a specific antibody to arrive to complete the confocal microscopy analyses. We thank the reviewer for the critical expert review and overall positive comments.

Based on their scRNAseq, the authors propose 41 different BM cell populations, ten of which represented non-hematopoietic cells, including one endothelial cell cluster. The nine remaining skeletal subpopulations were subdivided into multipotent stromal stem cells (MSSC), four distinct populations of osteoprogenitors, one cluster of osteoblasts and three clusters of pre-fibroblasts. Using bioinformatic tools, the authors then compare their results and divisions of subpopulations to some previously published work from others and attempt to delineate lineage relationships using RNA velocity analyses. From these, they propose different paths from which MSSC enter the progenitor stages, and might differentiate into pre-osteoblasts and -fibroblasts.

It is of interest to note, that apparently adipo-primed cells may also differentiate into osteolineage cells, something that should be further explored or validated. Furthermore, although this analysis yields a large adipo-primed populations, pre-adipocytes and mature adipocytes appear not to be included in the data set the authors used, which should also be explained.

We thank the reviewer for this comment. We chose to annotate Cluster 5 as adipoprimed cluster based on the higher expression of adipogenic differentiation markers as well as a group of stress-related transcription factors (FOS, FOSB, JUNB, EGR1) (Fig. 2B-C, Figure 2-figure supplement 1C) some of which had been shown to mark bone marrow adipogenic progenitors1. Although at considerably lower levels compared to adipogenic genes, osteogenic genes were also expressed in cluster 5 cells (Fig. 2B and D), indicating the multi-potent potential of this cluster. Therefore, our initial annotation of these cells as adipoprimed progenitors was too narrow as it did not include the possible osteogenic differentiation potential. We apologize for the confusion caused by the inappropriate annotation and, in order to avoid any further confusion, cluster 5 has now been re-annotated as ‘highly adipocytic gene-expressing progenitors (HAGEPs), which we believe is a better representation of the cells. We furthermore agree with the reviewer that in-vivo differentiation needs to be performed to address potential differentiation capacities in future studies.

With regard to the lack of adipocytes in our data set, we described in the Materials and Methods section that human bone marrow cells were isolated based on density gradient centrifugation. After centrifugation, the mononuclear cell-containing monolayers were harvested for further analysis. However, the resulting supernatant containing mature adipocytic cells was discarded14. Therefore, adipocyte clusters were not identified in our dataset. We have amended the manuscript accordingly (page 5, line 7).

Regarding the pre-adipocytes, we are not aware of any specific markers for pre-adipocytes in the bone marrow. We examined the only known markers (ICAM1, PPARG, FABP4) that have been shown to mark committed pre-adipocytes in human adipose tissue15. As illustrated in Fig. R1 (below), low expression of all three markers was not restricted to a single distinct cluster but could be found in almost all stromal clusters. These data thus allow us to neither confirm nor exclude the presence of pre-adipocytes in the dataset. Due to the lack of specific markers for pre-adipocytes and the absence of mature adipocytes in the current dataset, it is therefore difficult to identify a well-defined pre-adipocytes cluster.

Figure R1. UMAP illustration of the normalized expression of the markers for pre-adipocytes in stromal clusters.

In addition, based on a separate analysis of surface molecules, the authors propose new markers that could be used to prospectively isolate different human subpopulations of BM niche cells by using CD52, CD81 and NCAM1 (=CD56). Indeed, these analyses yield six different populations with differential abilities to form fibroblast-like colonies and differentiate into adipo-, osteo-, and chondrogenic lineages. To explore how the scRNAseq data may help to understand regulatory processes within the BM, the authors predict possible interactions between hematopoietic and non-hematopoietic subpopulations in the BM. These should be further validated, to support statements as the suggestion in the abstract that separate CXCL12- and SPP1-regulated BM niches might exist.

We agree with the reviewer that functional validation of the CellPhoneDB results using for example in vivo humanized mouse models would be needed to demonstrate the presence of different niches in the bone marrow. At this point of time we only put forward the hypothesis that different niche types exist while we will work on providing experimental proof in our future studies.

The scRNAseq analysis is indeed a strong and important resource, also for later studies meant to increase knowledge about the hematopoietic niche of the BM. Although the analyses using different bioinformatic tools is very helpful, they remain mostly speculative, since validatory experiments, as already mentioned, are missing. As such, I feel the authors did not succeed in achieving their goals of understanding how non-hematopoietic cells of the BM regulate the different hematopoietic processes within the BM. Nevertheless, they have created valuable resources, both in the scRNAseq data they generated, as well as the different predictions about different cell populations, their lineage relationships, and how they might interact with hematopoietic cells.

We thank the reviewer for the appreciation of the value of this dataset. We agree with the reviewer that it is of great importance to validate the contribution of potential driver genes for stromal cell differentiation and verify the in vitro data and in-silico prediction using in-vivo models. As the main goal of the current study was to formulate hypotheses based on the scRNAseq data for future studies, we believe that in vivo validation experiments using engineered human bone marrow models or humanized bone marrow ossicles are out of the scope of the current study, but certainly need to be performed in the future.

The impact of this work is difficult to envision, since validations still need to be performed. Also, it has the born in mind that humans are not mice, which can be studied in neat homogeneous inbred populations. Human populations on the other hand, are quite diverse, so that the data generated in this manuscript and others will probably have to be combined to extrapolate data relevant to the whole of the human population. However, as it is equally difficult to generate reliable scRNAseq data from human BM, it seems likely that the data will indeed an important resource, when more data from different donors become available.

We thank the reviewer for the generally positive evaluation of this study.

Taken at point value, the authors provide evidence that human counterparts exist to several BM populations described in mice. In my opinion, the lineage relationships predicted using the RNA velocity analyses need more substance, as it seems the differentiation-paths may diverge from what is known from mice. If so, this issue should be studied more stringently. Similarly, the paper would have been strengthened considerably if a relevant experimental validation would have been attempted, perhaps by using genetically modified (knockdown) MSSC, similar to Battula et al. (doi: 10.1182/blood-2012-06-437988).

In the study from Welner’s group, stromal differentiation trajectory was inferred based on scRNAseq analysis of murine bone marrow cells using Velocyto16. Velocyto identified MSCs as the ‘source’ cell state with pre-adipocytes, pro-osteoblasts, and prochondrocytes being end states. In our study, the MSSC population was predicted to be at the apex of the trajectory and the pre-osteoblast cluster was placed close to the terminal state of differentiation, which is consistent with the murine study. However, different stromal cell types were identified in mice compared with humans. For example, we have identified prefibroblasts in our dataset which are absent in the murine study, while a well-defined murine pre-adipocyte population was not identified in our human dataset. Therefore, it is not surprising to find some discrepancies between human and murine stromal differentiation trajectories. Of course and as mentioned before, critical in-vivo functional validations need to be carried out to address these important issues in the future.

In summary, this is a very interesting but also descriptive paper with highly important resources. However, to prospectively identify or isolate human non-hematopoietic/nonendothelial niche populations, more stringent validations should have been performed to strengthen the validity of the different analyses that have been performed. As such, it remains an open question which niche subpopulations has the most impact on the different hematopoietic processes important for normal and stress hematopoiesis, as well as malignancies.

Thank you for this comment. We completely agree that more stringent validations are necessary but are outside of the aim of our current hypothesis-generating study. Accordingly, we are planning functional verification studies using genetically manipulated stromal cells in combination with in-vivo humanized ossicles. Furthermore, other groups will hopefully use our database and contribute with functional studies in model systems that are currently not available to us, e.g. iPS-derived bone marrow in-vitro proxies.

Specific remarks

• Since CD45, CD235a, and CD271 are used as distinguishing markers in the sample preparation of the scRNAseq, it would be helpful to highlight these markers in the different analyses (Figures 1D, 2B, 2C-F, and 4A), and restrict the analyses to those cells that also not express CD45, CD235a (why use CD71?) and highly express CD271.

Thank you for this comment. As shown in Fig. R2, we have modified figures Fig. 1D, 2B, and 4A showing now also the expression of PTPRC (CD45), GYPA (CD235a), and NGFR (CD271) on the top (Fig. 1D and 2B) or right (Fig. 4A) panel of the figures. To complement Fig. 2C-F, we have generated new stacked violin plots showing the expression level of three markers by all 9 stromal clusters (Fig. R2B). As we believe that including these three markers in the figures does not provide a better strategy to improve the analyses, we decided to leave the original figures unchanged in this respect.

Figure R2. (A) Modified Fig. 1D, 2B and 4A with PTPRC (CD45), GYPA (CD235a) and NGFR (CD271) expression. (B) Stacked violin plots of PTPRC, GYPA and NGFR expressed by stromal clusters to complement Fig. 2C-F.

With regard to cell exclusion based on CD45, as shown in the modified Figure corresponding to Fig 1A in the manuscript (Fig R2A), CD45 gene expression is observed also in the endothelial cluster, basal cluster, and neuronal cluster (Fig. R2A). These clusters represent non-hematopoietic clusters that we would like to keep in our dataset for further analysis, such as cell-cell interaction. Therefore, we choose to not restrict the analysis to solely CD45 nonexpressing cells.

With regard to CD235a (GYPA), expression of CD235a is not detected in any of the nonhematopoietic clusters. Thus, CD235a-expressing cell exclusion is not necessary.

For CD271, according to our previous results (own unpublished data, belonging to a dataset of which only significantly expressed genes were reported in Li et al.8), protein expression of CD271 is not necessarily reflected by gene expression. In the other words, stromal cells with CD271 protein expression do not always have high mRNA expression. A significant fraction of stromal cells would be excluded if we restrict the analyses only to those cells that show high CD271 gene expression, which would not reflect the real cellular composition of human bone marrow stroma. In order to not risk losing stromal cells, we therefore kept our previous analyses which included stromal cells with various CD271 expression levels.

With regard to using CD71 as an exclusion marker, please see also the comments to reviewer 1. Briefly, according to our data, CD71 (TFRC)-expressing erythroid precursors could still be found after excluding CD45 and CD235a positive cells (Figure 1-figure supplement 1B and R3). As furthermore shown in Figure 1-figure supplement 1G and R2, CD71 expression in the stromal clusters is negligible. Therefore, we believe that this justifies the use of CD71 as an additional marker to exclude erythroid cells. We have amended the discussion to address this issue (page 19, lines 7-8).

Figure R3. FACS plots illustrating the expression of (A) CD71 (TFRC) vs CD271 in CD45- CD235a- cells and (B) FSC-A vs CD81 in CD45-CD235a-CD271+CD71+ cells following exclusion of doublets and dead cells.

• Despite a distinct neuronal cluster (39), there does not seem to be a distinctive marker for these cells. Is this true?

Yes, the reviewer is correct that there is no significantly-expressed distinctive marker for neuronal cells. Multiple markers indicating the presence of different cell types were identified in cluster 39 (Supplementary File 4). Among them, several neuronal markers (NEUROD1, CHGB, ELAVL2, ELAVL3, ELAVL4, STMN2, INSM1, ZIC2, NNAT) were found to be enriched in this cluster (Supplementary File 4 and Fig. 1D) with higher fold changes compared to other identified genes. However, the expression of these genes was not statistically significant, which is mainly due to the heterogeneity of the cluster and thus does not allow us to draw any firm conclusions.

Several genes including MALAT1, HNRNPH1, AC010970.1, and AD000090.1 were identified to be statistically highly expressed by cluster 39 (Supplementary File 4). The expression of these genes is not restricted to any specific cell type. It is therefore impossible to annotate the cluster based on this and our data thus indicated that cluster 39 is a heterogeneous population containing multiple cell types. Based on the expression of neuronal markers, we nevertheless chose to annotate Cluster 39 as “neuronal” as the prominent expression of neuronal markers indicated the presence of neurons in this cluster. To be more accurate, the annotation of cluster 39 has been changed to ‘neuronal cell-containing cluster’ to correctly reflect the presence of non-neuronal gene expressing cells as well (page 29, lines 3-8).

• Since based on 2C and 2D, the authors are unable to distinguish adipo- from osteogenic cells, would the authors use the same molecules to distinguish different populations of 2C-D, or would they use other markers, if so which and why.

We agree with the reviewer that at the first glance adipo-primed (cluster 5, now annotated as “highly adipocytic gene-expressing progenitors”, HAGEPs), balanced progenitors (cluster 16), and pre-osteoblasts (cluster 38) shared a similar expression pattern according to the violin plots in Fig. 2C and 2D. However, as illustrated in the heatmap (Fig. 2B), the expression patterns of adipo-primed (HAGEP) and balanced progenitors were quite different in terms of their expression of adipogenic and osteogenic markers. Both adipogenic and osteogenic marker expression was detected in HAGEPs, balanced progenitors, and preosteoblasts. Thus, as violin plots are summarizing the overall expression levels of a certain marker in a certain cluster, these plots tend to make it more difficult to detect differential expression patterns between different clusters. In this case, the heatmap shown in Fig. 2B is a good complement to the violin plots as it is demonstrating the different expression patterns of every cell in the different stromal clusters.

Additionally, cluster 5 showed the expression of a group of stress-related transcription factors (FOS, FOSB, JUNB, EGR1) (Fig. 2B and Figure 2-figure supplement 1C), some of which had been shown to mark bone marrow adipogenic progenitors1. The expression of the abovementioned stress-related transcription factors (putative adipogenic progenitor markers) was generally lower in cluster 38 compared to cluster 5, further demonstrating that clusters were different.

Furthermore, there was a gradual upregulation of more mature osteogenic markers such as RUNX1, CDH11, EBF1, and EBF3 from cluster 5 to cluster 16 and finally cluster 38. As shown in Fig. 2D, the expression of these markers was higher in cluster 38 compared to cluster 5. Therefore, cluster 38 was annotated as pre-osteoblasts.

Most of the stromal clusters form a continuum (Fig. 2A), which correlates very well with the gradual transition of different cellular states during stromal cell development. It is highly unlikely that abrupt and dramatic gene expression changes would occur during the cellular state transition of cells of the same lineage. Therefore, it is not surprising to find the differences in gene expression profiles between stromal clusters share a certain level of similarities.

In summary, we rely on several factors to distinguish different stromal clusters, which include canonical adipo-, osteo- and chondrogenic markers, stress markers, heatmap, violin plots, and the gradual up-regulation of certain lineage-specific markers.

To directly answer the reviewer’s question, we believe that we are able to distinguish different stromal clusters based on our data.

• In de Jong et al., an inflammatory MSC population (iMSC) is defined. Since the Schneider group showed that inflammatory S100A8 and A9 are expressed by inflamed MSC, is it possible that the some of the designated pre-fibroblasts actually correspond to these S100A8/A9-expressing iMSC?

We thank the reviewer for raising this interesting question.

First of all, we would like to point out that scRNAseq was performed using viably frozen bone marrow aspirates in de Jong’s study while freshly isolated bone marrows were used in our study. There might be discrepancies between frozen and fresh bone marrow samples in terms of cellular composition including stromal composition and, importantly, processinginduced stress-related gene expression profiles.

To investigate if designated pre-fibroblasts actually correspond to iMSCs as suggested by the reviewer, we have re-examined the expression of some of the key iMSC genes as reported by de Jong et al 17. As shown in Fig. R6, the markers that can distinguish iMSC from other MSC clusters in de Jong et al. study were not exclusively expressed by pre-fibroblasts, but also by other stromal cell types including HAGEPs, balanced progenitors, and pre-osteoblasts.

In the study by R. Schneider’s group18, significant upregulation of S100A8/S100A9 was observed in stromal cells from patients with myelofibrosis. Furthermore, base-line expression of S100A8/A9 was also observed in the fibroblast clusters in the control group, which correlates very well with our data of S100A8/9 expression in pre-fibroblasts in normal donors (Fig. 2F). Our data thus indicate – in line with Schneider’s findings - that there is a baseline level expression of S100A8/9 in fibroblasts in hematologically normal samples and that the expression of S100A8/9 is not restricted to inflamed MSC.

In summary, the gene expression profiles observed in our study do not indicate the presence of iMSC in the healthy bone marrow.

• Figure 3A: Do human adipo-primed cells (cluster 5) indeed differentiate into osteogenic cells (clusters 6, 38, and 39). This would be highly unexpected. Can the authors substantiate this "reliable outcome of the RNA velocity analysis"?

Please refer to our previous responses regarding this topic. Briefly, as shown in Fig. 2B and D, both osteogenic and adipogenic genes are expressed in cluster 5, indicating the multi-potent potentials of this cluster. Although the cluster was initially annotated as adipo-primed progenitors, this was not intended to exclude the osteogenic differentiation potential of these progenitors. Nevertheless, this annotation did not correctly reflect the differentiation potential and might thus have caused confusion, for which we apologize. In order to more correctly describe the characteristics of these cells, cluster 5 has now been reannotated as ‘highly adipocytic gene-expressing progenitors (HAGEPs)’.

In general, the outcome of the RNA velocity analysis needs to be corroborated by in-vivo differentiation experiments. But we believe that functional verification, which would be extensive, is out of the scope of the current study and we will address these questions in future studies.

• How statistically certain are the authors, that the populations in Figure 4B as defined by flow cytometry, correspond to MSSC, adipo-primed cells, osteoprogenitors, etc., as defined by scRNAseq?

To address this question, we sorted the A1-A4 populations and performed RT- PCR to examine the CD81 expression level in each cluster. As shown in Figure 4-figure supplement 1B, CD81 expression levels were higher in A1 and A2 compared with A3 and A4, which is consistent with the scRNAseq data that showed the highest CD81 expression in MSSCs compared to other clusters (Supplementary File 4).

The phenotypes defined in this study allowed us to isolate different stromal cell types which demonstrated significant functional differences as described in the manuscript (page 19, lines 17-25; page 20, lines 1-11). These results, in combination with the quantitative real-time PCR results (Figure 4-figure supplement 1B), demonstrated that the A1-A4 subsets in FACS are functionally distinct populations and are likely to be – at least in large parts – identical or equivalent to the transcriptionally identified clusters in group A stromal cells. However, at this point, we do not have performed the required experiments (scRNAseq of sorted cells) that would provide sufficient proof to confirm this statement statistically.

• The immunohistochemistry results shown do not allow distinct conclusions as the colors give unequivocal mix-colors, and surface expression cannot be distinguished from intracellular expression. Please use a 3D (confocal) method for such statements.

We thank the reviewer for the suggestion and we have performed additional confocal microscopy analysis of human bone marrow biopsies as suggested by the reviewer. Representative confocal images are now presented in the middle and right panel of Fig. 6E. We also include a separate file (Supplemental confocal image file). Here, confocal scans of all maker combinations are shown as ortho views in addition to detailed intensity profile analyses of the cells of interest clearly distinguishing surface staining from intracellular staining.

Confocal analysis of bone marrow biopsies confirmed our findings presented in the manuscript. As observed in the scanning images, CD271-expressing cells were negative for CD45 and were located in perivascular, endosteal, and peri-adipocytic regions. CD271/CD81double positive cells could be found either in the peri-adipocytic regions or perivascular regions while CD271/NCAM1 double-positive cells were exclusively situated at the bone-lining endosteal regions. The results of the confocal analysis have been added to the revised manuscript (page 21, lines 15-17).

• Figure 5A: as all cells seem to interact with all other cells, this figure does not convey relevant information about BM regions using for instance CXCL12 or SPP1. Please reanalyze to show specificity of the interactions of the single clusters. Also, since it is unlikely the CellPhoneDB2-predicted interactions are restricted to hematopoietic responders, please also describe the possible interactions between non-hematopoietic cells.

Fig. 5A was used to demonstrate the complexity of the interactions between hematopoietic cells and stromal cells.

To gain a more detailed understanding of the interactions, we also performed an analysis with the top-listed ligand-receptor pairs as shown in Fig. 5B-C and Figure 5-figure supplement 1B. Here, each dot represents the interaction of a specific ligand-receptor pair listed on the x-axis between the two individual clusters indicated in the y-axis, which we believe shows what the reviewer is asking for.

The specificity of the interactions between single clusters were shown in Fig. 5B-C and Figure 5-figure supplement 1B. The CXCL12- and SPP1-mediated interactions between MSSC/OC and hematopoietic clusters clearly suggested stromal cell type-specific interactions.

Regarding non-hematopoietic cells, both inter- and intra-stromal interactions were identified to be operative between different stromal subsets as well as within the same stromal cell population as shown in Figure 5-figure supplement 3B. In addition, we have also analyzed the interaction pattern between endothelial cells and hematopoietic cells as shown in Fig. 7A, and thus we believe that we have sufficiently described these interactions as requested by the reviewer.

Author Response

Reviewer #2 (Public Review):

Point 1: The transcriptomic analysis of E12.5 endocardial cushion cells in the various mouse models is informative in the extraction of Igf2- and H19-specific gene functions. In Fig. 6D, a huge sex effect is obvious with many more DEGs in female embryos compared to males. How can this be explained given that Igf2/H19 reside on Chr7 and do not primarily affect gene expression on the X chromosome? Is any chromosomal bias observed in the genomic distribution of DEGs?

We examined chromosomal distribution of DEGs between WT and +/hIC1 (Supplemental Figure 6D) and did not see any bias on X chromosome. We described this result on lines 278-280: “Although the number of +/hIC1-specific DEGs largely differed between males and females, there was no sex-specific bias on the X chromosome (Supplemental Figure 6D).” Additionally, we agree with the reviewer that it is noteworthy that the dysregulated H19/Igf2 expression affected transcriptome in a sex-specific manner, especially when the mutation is located on a somatic chromosome. Although investigating the role of hormones versus sex chromosome in these effects would be quite interesting, it is beyond the scope of current study.

Point 2: A separate issue is raised by Fig. 6E that shows a most dramatic dysregulation of a single gene in the delta3.8/hIC1 "rescue" model. Interestingly, this gene is Shh. Hence, these embryos should exhibit some dramatic skeletal abnormalities or other defects linked to sonic hedgehog function.

The reason why Shh appeared to be differentially expressed between wild-type and d3.8/hIC1 samples was that Shh expression was 0 across all the samples except for two wild-type samples. In order to detect all the DEGs that might be lowly expressed, we did not want to filter DEGs based on the level of total expression. As a result, Shh was represented as significantly differently expressed in d3.8/hIC1 samples, although its expression in our samples appears to be too low to have any significant effect on development. This explanation was added to lines 310-312. To confirm that this was an exceptional case, we analyzed the expression of DEGs obtained from other pairwise comparisons. In the volcano plots below, genes of which expression is not statistically different between two groups are marked grey. Genes of which expression is statistically different and detected in both groups are marked red. Genes with statistically different but not detected in one group at all, such as Shh, are marked blue (Figure G). It is clear that that almost all of our DEGs are expressed consistently across the groups, and genes with no expression detected in one group are very rare.

Point 3: The placental analysis needs to be strengthened. Placentas should be consistently positioned with the decidua facing up, and the chorionic plate down. The placentas in Fig. 3F are sectioned at an angle and the chorionic plate is missing. These images must be replaced with better histological sections.

As requested, we have replaced placental images with better representative sections (Figure 3F and 4E). In addition, we have improved alignment of placental histology figures.

Point 4: The CD34 staining has not worked and does not show any fetal vasculature, in particular not in the WT sample.

As requested, we have replaced the CD34 vascular stained images with those that better represent fetal vasculature (Figure 3G).

Point 5: The "thrombi" highlighted in Fig. 4E are well within the normal range, to make the point that these are persistent abnormalities more thorough measurements would need to be performed (number, size, etc).

As requested, we measured the number and relative size of the thrombi that are found in dH19/hIC1 placentas with lesions. No thrombi were found in wild-type placentas whereas an average of 1.3 thrombi were found in six dH19/hIC1 placentas. The size of the thrombi widely varied, but occupied average of 2.58% of the labyrinth zone where these lesions were found (Supplemental Figure 4D). Additionally, we replaced the image in Figure 4E into the section that better represents the lesion.

Point 6: The statement that H19 is disproportionately contributing to the labyrinth phenotype (lines 154/155) is not warranted as Igf2 expression is reduced to virtually nothing in these mice. Even though there is more H19 in the labyrinth than in the junctional zone, the phenotype may still be driven by a loss of Igf2. Given the quasi Igf2-null situation in +/hIC1 mice, is the glycogen cell type phenotype recapitulated in these mice, and how do glycogen numbers compare in the other mouse models?

The sentence was edited in line 157. We performed Periodic acid Schiff (PAS) staining on +/hIC1 placentas to address if glycogen cells are affected by abnormal H19/Igf2 expression (Supplemental Figure 1E). In contrary to previous reports where Igf2-null mice had lower placental glycogen concentration (Lopez et al., 1996) and H19 deletion led to increased placental glycogen storage (Esquiliano et al., 2009), our quantification on PAS-stained images showed that the glycogen content is not significantly different between wild-type and +/hIC1 placentas. We have described this result in lines 166-168.

Point 7: How do delta3.8/+ and delta3.8/hIC1 mice with a VSD survive? Is it resolved some time after birth such that heart function is compatible with postnatal viability? And more importantly, do H19 expression levels correlate with phenotype severity on an individual basis?

Our study was limited to phenotypes prior to birth, thus postnatal/adult phenotypes were not examined. Because the VSD showed only partial penetrance in these mice, we cannot state that the d3.8/+ or d3.8/hlC1 mice with VSDs survive. It has also been previously reported in another mouse model with incomplete penetrance of a VSD that the mice which survived to adulthood did not have the VSDs (Sakata et al., 2002). We find it highly unlikely that either mouse model would survive significantly past the postnatal timepoint with a VSD. We have examined two PN0 d3.8/hIC1 neonates, and both did not have VSD.

Regarding the second point, the only way to quantitatively address this question would be to do qPCR or RNA-seq on individual hearts, which then makes it impossible for those hearts to be examined for histology to confirm the VSD. Thus, hearts used to identify VSDs via histology could not also be used for quantitative H19 measurements. One thing to note is that the H19/Igf2 expression in independent replicates of d3.8/hIC1 cardiac ECs used in our RNA-seq experiment is quite variable, not clustering together in contrast to other mouse models used in this study (Fig. 6A). Such wide range of variability in the extent of H19/Igf2 dysregulation suggests that H19/Igf2 levels could have an impact on the penetrance or the severity of the VSD phenotype in d3.8/hIC1 embryos.

Author Response

Reviewer #2 (Public Review):

Weaknesses:

1) The relevance of the LPS-induced calvarial osteolysis model is not clear. Calvaria is mostly composed of cortical bone-like structures lacking marrow space, though small marrow space exists near the suture. Osteolysis appears to occur in areas apart from where marrow is located. The authors did not show in the manuscript which cells Adipoq-Cre marks in the calvaria.

We have shown in a recent publication that MALPs exist in the calvarial bone marrow (2). As shown in Fig. R1A, Td+ cells are layer of cortical bone (Fig. R1B, blue arrows). In WT mice, after LPS injection, the normal bone structure, including suture and cortical bone, were mostly eroded, and filled with inflammatory cells (green arrows). Thus, osteolysis does occur at the area where bone marrow is originally located. On the contrary, calvarial bone structure was preserved in the CKO mice, demonstrating that Csf1 deficiency in MALPs suppresses LPS-induced osteolysis. We included the H&E staining data in the revised manuscript:

"H&E staining showed that calvarial bone marrow is surrounded by a thin layer of cortical bone (Fig. 5C). After the LPS injection, normal calvarial structure, including suture and cortical bone, were mostly eroded and filled with inflammatory cells in WT mice, but unaltered in CKO mice."

Figure R1. Calvarial bone marrow structure. (A) Representative coronal section of 1.5-month-old Adipoq/Td mouse calvaria. Bone surfaces are outlined by dashed lines. Boxed areas in the low magnification image (top) are enlarged to show periosteum (bottom left), suture (bottom middle), and bone marrow (BM, bottom right) regions. Red: Td; Blue: DAPI. Adopted from our previous publication (2). (B) H&E staining of coronal sections of WT and Csf1 CKOAdipoq mice after LPS injection. Blue arrows point to bone marrow space close to suture (indicated by *). Green arrows point to the osteolytic lesion where cortical bone was eroded, and the space were filled with inflammatory cells.

2) Although the contrast between the two Csf1 conditional deletion models (Adipoq-Cre and Prx1-Cre) is very interesting, the relationship between these two cell populations are not well described. The authors did not clarify if MALPs are also targeted by Prx1-Cre, or these two cell types are from different cell lineages. "Other mesenchymal lineage cells" in the subtitle is not extremely helpful to place this finding in context.

We thank the Reviewer for this comment. The original article constructing Prx1-Cre mouse line demonstrates that Prx1-Cre targets all mesenchymal cells in the limb bud at early as 10.5 dpc (10). This early expression pattern ensures that all bone marrow mesenchymal lineage cells, including MALPs, are targeted by Prx1-Cre. In addition, based on our scRNA-seq data (1), Adipoq is mainly expressed in MALPs, while Prrx1 (Prx1) is highly expressed not only in MALPs but also in EMPs, IMPs, LMPs, LCPs, and OBs (Fig. R2). Thus, the fact that Prx1-Cre driven CKO mice have much more severer bone phenotypes than AdipoqCre driven CKO mice indicates that mesenchymal lineage cells other than MALPs also contribute Csf1 to regulate bone resorption. To avoid confusion, we changed the title and the first sentence in the Result session about Prx1 mice to the following:

"Csf1 from mesenchymal lineage cells other than MALPs regulate bone structure.

To explore whether Csf1 from MALPs plays a dominant role in regulating bone structure, we generated Prx1-Cre Csf1flox/flox (Csf1 CKOPrx1) mice to knockout Csf1 in all mesenchymal lineage cells in bone (10), including MALPs."

Figure R2. Dotplot of Prrx1 and Adipoq expression in bone marrow mesenchymal lineage cells based on our scRNA-seq analysis of 1-month-old mice.

3) The data supporting defective bone marrow hematopoiesis in Csf1 CKO mice are not particularly strong. They observed a reduction in bone marrow cellularity, but this was only associated with an expected reduction in macrophages and a mild reduction in overall HSPC populations. More in-depth analyses might be required to define mechanisms underlying reduced bone marrow cellularity in CKO mice.

We thank the Reviewer for this constructive comment. Accordingly, we performed a thorough analysis of bone marrow hematopoietic compartments and observed significant decreases of monocytes and erythroid progenitors in CKO mice compared to WT mice. These results are now included as Fig. 6E.

4) Some of the phenotypic analyses are still incomplete. The authors did not report whether CHet (Adipoq-Cre Csf1(flox/+)) showed any bone phenotype. Further, the authors did not report whether Csf1 mRNA or M-Csf protein is indeed expressed by MALPs, with current evidence solely reliant on scRNAseq and qPCR data of bulk-isolated cells. More specific histological methods will be helpful to support the premise of the study.

A pilot microCT study revealed the same femoral trabecular bone structure in WT and Adipoq-Cre Csf1flox/+ (Csf1 Het) mice at 3 months of age (Fig. R3). While the sample number for Het is low, we are confident about this conclusion.

Figure R3. MicroCT measurement of trabecular bone structural parameters from WT and Csf1 Het mice. BV/TV: bone volume fraction; BMD: bone mineral density; Tb.N: trabecular number; Tb.Th: trabecular thickness; Tb.Sp: trabecular separation; SMI: structural model index. n=3-8 mice/group.

Author response:

Reviewer #1 (Public Review):

In this paper, Tompary & Davachi present work looking at how memories become integrated over time in the brain, and relating those mechanisms to responses on a priming task as a behavioral measure of memory linkage. They find that remotely but not recently formed memories are behaviorally linked and that this is associated with a change in the neural representation in mPFC. They also find that the same behavioral outcomes are associated with the increased coupling of the posterior hippocampus with category-sensitive parts of the neocortex (LOC) during a post-learning rest period-again only for remotely learned information. There was also correspondence in rest connectivity (posterior hippocampus-LOC) and representational change (mPFC) such that for remote memories specifically, the initial post-learning connectivity enhancement during rest related to longer-term mPFC representational change.

This work has many strengths. The topic of this paper is very interesting, and the data provide a really nice package in terms of providing a mechanistic account of how memories become integrated over a delay. The paper is also exceptionally well-written and a pleasure to read. There are two studies, including one large behavioral study, and the findings replicate in the smaller fMRI sample. I do however have two fairly substantive concerns about the analytic approach, where more data will be required before we can know whether the interpretations are an appropriate reflection of the findings. These and other concerns are described below.

Thank you for the positive comments! We are proud of this work, and we feel that the paper is greatly strengthened by the revisions we made in response to your feedback. Please see below for specific changes that we’ve made.

1) One major concern relates to the lack of a pre-encoding baseline scan prior to recent learning.

a) First, I think it would be helpful if the authors could clarify why there was no pre-learning rest scan dedicated to the recent condition. Was this simply a feasibility consideration, or were there theoretical reasons why this would be less "clean"? Including this information in the paper would be helpful for context. Apologies if I missed this detail in the paper.

This is a great point and something that we struggled with when developing this experiment. We considered several factors when deciding whether to include a pre-learning baseline on day two. First, the day 2 scan session was longer than that of day 1 because it included the recognition priming and explicit memory tasks, and the addition of a baseline scan would have made the length of the session longer than a typical scan session – about 2 hours in the scanner in total – and we were concerned that participant engagement would be difficult to sustain across a longer session. Second, we anticipated that the pre-learning scan would not have been a ‘clean’ measure of baseline processing, but rather would include signal related to post-learning processing of the day 1 sequences, as multi-variate reactivation of learned stimuli have been observed in rest scans collected 24-hours after learning (Schlichting & Preston, 2014). We have added these considerations to the Discussion (page 39, lines 1047-1070).

b) Second, I was hoping the authors could speak to what they think is reflected in the post-encoding "recent" scan. Is it possible that these data could also reflect the processing of the remote memories? I think, though am not positive, that the authors may be alluding to this in the penultimate paragraph of the discussion (p. 33) when noting the LOC-mPFC connectivity findings. Could there be the reinstatement of the old memories due to being back in the same experimental context and so forth? I wonder the extent to which the authors think the data from this scan can be reflected as strictly reflecting recent memories, particularly given it is relative to the pre-encoding baseline from before the remote memories, as well (and therefore in theory could reflect both the remote + recent). (I should also acknowledge that, if it is the case that the authors think there might be some remote memory processing during the recent learning session in general, a pre-learning rest scan might not have been "clean" either, in that it could have reflected some processing of the remote memories-i.e., perhaps a clean pre-learning scan for the recent learning session related to point 1a is simply not possible.)

We propose that theoretically, the post-learning recent scan could indeed reflect mixture of remote and recent sequences. This is one of the drawbacks of splitting encoding into two sessions rather than combining encoding into one session and splitting retrieval into an immediate and delayed session; any rest scans that are collected on Day 2 may have signal that relates to processing of the Day 1 remote sequences, which is why we decided against the pre-learning baseline for Day 2, as you had noted.

You are correct that we alluded to in our original submission when discussing the LOC-mPFC coupling result, and we have taken steps to discuss this more explicitly. In Brief, we find greater LOC-mPFC connectivity only after recent learning relative to the pre-learning baseline, and cortical-cortical connectivity could be indicative of processing memories that already have undergone some consolidation (Takashima et al., 2009; Smith et al., 2010). From another vantage point, the mPFC representation of Day 1 learning may have led to increased connectivity with LOC on Day 2 due to Day 1 learning beginning to resemble consolidated prior knowledge (van Kesteren et al., 2010). While this effect is consistent with prior literature and theory, it's unclear why we would find evidence of processing of the remote memories and not the recent memories. Furthermore, the change in LOC-mPFC connectivity in this scan did not correlate with memory behaviors from either learning session, which could be because signal from this scan reflects a mix of processing of the two different learning sessions. With these ideas in mind, we have fleshed out the discussion of the post-encoding ‘recent’ scan in the Discussion (page 38-39, lines 1039-1044).

c) Third, I am thinking about how both of the above issues might relate to the authors' findings, and would love to see more added to the paper to address this point. Specifically, I assume there are fluctuations in baseline connectivity profile across days within a person, such that the pre-learning connectivity on day 1 might be different from on day 2. Given that, and the lack of a pre-learning connectivity measure on day 2, it would logically follow that the measure of connectivity change from pre- to post-learning is going to be cleaner for the remote memories. In other words, could the lack of connectivity change observed for the recent scan simply be due to the lack of a within-day baseline? Given that otherwise, the post-learning rest should be the same in that it is an immediate reflection of how connectivity changes as a function of learning (depending on whether the authors think that the "recent" scan is actually reflecting "recent + remote"), it seems odd that they both don't show the same corresponding increase in connectivity-which makes me think it may be a baseline difference. I am not sure if this is what the authors are implying when they talk about how day 1 is most similar to prior investigation on p. 20, but if so it might be helpful to state that directly.

We agree that it is puzzling that we don’t see that hippocampal-LOC connectivity does not also increase after recent learning, equivalently to what we see after remote learning. However, the fact that there is an increase from baseline rest to post-recent rest in mPFC – LOC connectivity suggests that it’s not an issue with baseline, but rather that the post-recent learning scan is reflecting processing of the remote memories (although as a caveat, there is no relationship with priming).

On what is now page 23, we were referring to the notion that the Day 1 procedure (baseline rest, learning, post-learning rest) is the most straightforward replication of past work that finds a relationship between hippocampal-cortical coupling and later memory. In contrast, the Day 2 learning and rest scan are less ‘clean’ of a replication in that they are taking place in the shadow of Day 1 learning. We have clarified this in the Results (page 23, lines 597-598).

d) Fourth and very related to my point 1c, I wonder if the lack of correlations for the recent scan with behavior is interpretable, or if it might just be that this is a noisy measure due to imperfect baseline correction. Do the authors have any data or logic they might be able to provide that could speak to these points? One thing that comes to mind is seeing whether the raw post-learning connectivity values (separately for both recent and remote) show the same pattern as the different scores. However, the authors may come up with other clever ways to address this point. If not, it might be worth acknowledging this interpretive challenge in the Discussion.

We thought of three different approaches that could help us to understand whether the lack of correlations in between coupling and behavior in the recent scan was due to noise. First, we correlated recognition priming with raw hippocampal-LOC coupling separately for pre- and post-learning scans, as in Author response image 1:

Author response image 1.

Note that the post-learning chart depicts the relationship between post-remote coupling and remote priming and between post-recent coupling and recent priming (middle). Essentially, post-recent learning coupling did not relate to priming of recently learned sequences (middle; green) while there remains a trend for a relationship between post-remote coupling and priming for remotely learned sequences (middle; blue). However, the significant relationship between coupling and priming that we reported in the paper (right, blue) is driven both by the initial negative relationship that is observed in the pre-learning scan and the positive relationship in the post-remote learning scan. This highlights the importance of using a change score, as there may be spurious initial relationships between connectivity profiles and to-be-learned information that would then mask any learning- and consolidation-related changes.

We also reasoned that if comparisons between the post-recent learning scan and the baseline scan are noisier than between the post-remote learning and baseline scan, there may be differences in the variance of the change scores across participants, such that changes in coupling from baseline to post-recent rest may be more variable than coupling from baseline to post-remote rest. We conducted F-tests to compare the variance of the change in these two hippocampal-LO correlations and found no reliable difference (ratio of difference: F(22, 22) = 0.811, p = .63).

Finally, we explored whether hippocampal-LOC coupling is more stable across participants if compared across two rest scans within the same imaging session (baseline and post-remote) versus across two scans across two separate sessions (baseline and post-recent). Interestingly, coupling was not reliably correlated across scans in either case (baseline/post-remote: r = 0.03, p = 0.89 Baseline/post-recent: r = 0.07, p = .74).

Finally, we evaluated whether hippocampal-LOC coupling was correlated across different rest scans (see Author response image 2). We reasoned that if such coupling was more correlated across baseline and post-remote scans relative to baseline and post-recent scans, that would indicate a within-session stability of participants’ connectivity profiles. At the same time, less correlation of coupling across baseline and post-recent scans would be an indication of a noisier change measure as the measure would additionally include a change in individuals’ connectivity profile over time. We found that there was no difference in the correlation of hipp-LO coupling is across sessions, and the correlation was not reliably significant for either session (baseline/post-remote: r = 0.03, p = 0.89; baseline/post-recent: r = 0.07, p = .74; difference: Steiger’s t = 0.12, p = 0.9).

Author response image 2.

We have included the raw correlations with priming (page 25, lines 654-661, Supplemental Figure 6) as well as text describing the comparison of variances (page 25, lines 642-653). We did not add the comparison of hippocampal-LOC coupling across scans to the current manuscript, as an evaluation of stability of such coupling in the context of learning and reactivation seems out of scope of the current focus of the experiment, but we find this result to be worthy of follow-up in future work.

In summary, further analysis of our data did not reveal any indication that a comparison of rest connectivity across scan sessions inserted noise into the change score between baseline and post-recent learning scans. However, these analyses cannot fully rule that possibility out, and the current analyses do not provide concrete evidence that the post-recent learning scan comprises signals that are a mixture of processing of recent and remote sequences. We discuss these drawbacks in the Discussion (page 39, lines 1047-1070).

2) My second major concern is how the authors have operationalized integration and differentiation. The pattern similarity analysis uses an overall correspondence between the neural similarity and a predicted model as the main metric. In the predicted model, C items that are indirectly associated are more similar to one another than they are C items that are entirely unrelated. The authors are then looking at a change in correspondence (correlation) between the neural data and that prediction model from pre- to post-learning. However, a change in the degree of correspondence with the predicted matrix could be driven by either the unrelated items becoming less similar or the related ones becoming more similar (or both!). Since the interpretation in the paper focuses on change to indirectly related C items, it would be important to report those values directly. For instance, as evidence of differentiation, it would be important to show that there is a greater decrease in similarity for indirectly associated C items than it is for unrelated C items (or even a smaller increase) from pre to post, or that C items that are indirectly related are less similar than are unrelated C items post but not pre-learning. Performing this analysis would confirm that the pattern of results matches the authors' interpretation. This would also impact the interpretation of the subsequent analyses that involve the neural integration measures (e.g., correlation analyses like those on p. 16, which may or may not be driven by increased similarity among overlapping C pairs). I should add that given the specificity to the remote learning in mPFC versus recent in LOC and anterior hippocampus, it is clearly the case that something interesting is going on. However, I think we need more data to understand fully what that "something" is.

We recognize the importance of understanding whether model fits (and changes to them) are driven by similarity of overlapping pairs or non-overlapping pairs. We have modified all figures that visualize model fits to the neural integration model to separately show fits for pre- and post-learning (Figure 3 for mPFC, Supp. Figure 5 for LOC, Supp. Figure 9 for AB similarity in anterior hippocampus & LOC). We have additionally added supplemental figures to show the complete breakdown of similarity each region in a 2 (pre/post) x 2 (overlapping/non-overlapping sequence) x 2 (recent/remote) chart. We decided against including only these latter charts rather than the model fits since the model fits strike a good balance between information and readability. We have also modified text in various sections to focus on these new results.

In brief, the decrease in model fit for mPFC for the remote sequences was driven primarily by a decrease in similarity for the overlapping C items and not the non-overlapping ones (Supplementary Figure 3, page 18, lines 468-472).

Interestingly, in LOC, all C items grew more similar after learning, regardless of their overlap or learning session, but the increase in model fit for C items in the recent condition was driven by a larger increase in similarity for overlapping pairs relative to non-overlapping ones (Supp. Figure 5, page 21, lines 533-536).

We also visualized AB similarity in the anterior hippocampus and LOC in a similar fashion (Supplementary Figure 9).

We have also edited the Methods sections with updated details of these analyses (page 52, lines 1392-1397). We think that including these results considerably strengthen our claims and we are pleased to have them included.

3) The priming task occurred before the post-learning exposure phase and could have impacted the representations. More consideration of this in the paper would be useful. Most critically, since the priming task involves seeing the related C items back-to-back, it would be important to consider whether this experience could have conceivably impacted the neural integration indices. I believe it never would have been the case that unrelated C items were presented sequentially during the priming task, i.e., that related C items always appeared together in this task. I think again the specificity of the remote condition is key and perhaps the authors can leverage this to support their interpretation. Can the authors consider this possibility in the Discussion?

It's true that only C items from the same sequence were presented back-to-back during the priming task, and that this presentation may interfere with observations from the post-learning exposure scan that followed it. We agree that it is worth considering this caveat and have added language in the Discussion (page 40, lines 1071-1086). When designing the study, we reasoned that it was more important for the behavioral priming task to come before the exposure scans, as all items were shown only once in that task, whereas they were shown 4-5 times in a random order in the post-learning exposure phase. Because of this difference in presentation times, and because behavioral priming findings tend to be very sensitive, we concluded that it was more important to protect the priming task from the exposure scan instead of the reverse.

We reasoned, however, that the additional presentation of the C items in the recognition priming task would not substantially override the sequence learning, as C items were each presented 16 times in their sequence (ABC1 and ABC2 16 times each). Furthermore, as this reviewer suggests, the order of C items during recognition was the same for recent and remote conditions, so the fact that we find a selective change in neural representation for the remote condition and don’t also see that change for the recent condition is additional assurance that the recognition priming order did not substantially impact the representations.

4) For the priming task, based on the Figure 2A caption it seems as though every sequence contributes to both the control and primed conditions, but (I believe) this means that the control transition always happens first (and they are always back-to-back). Is this a concern? If RTs are changing over time (getting faster), it would be helpful to know whether the priming effects hold after controlling for trial numbers. I do not think this is a big issue because if it were, you would not expect to see the specificity of the remotely learned information. However, it would be helpful to know given the order of these conditions has to be fixed in their design.

This is a correct understanding of the trial orders in the recognition priming task. We chose to involve the baseline items in the control condition to boost power – this way, priming of each sequence could be tested, while only presenting each item once in this task, as repetition in the recognition phase would have further facilitated response times and potentially masked any priming effects. We agree that accounting for trial order would be useful here, so we ran a mixed-effects linear model to examine responses times both as a function of trial number and of priming condition (primed/control). While there is indeed a large effect of trial number such that participants got faster over time, the priming effect originally observed in the remote condition still holds at the same time. We now report this analysis in the Results section (page 14, lines 337-349 for Expt 1 and pages 14-15, lines 360-362 for Expt 2).

5) The authors should be cautious about the general conclusion that memories with overlapping temporal regularities become neurally integrated - given their findings in MPFC are more consistent with overall differentiation (though as noted above, I think we need more data on this to know for sure what is going on).

We realize this conclusion was overly simplistic and, in several places, have revised the general conclusions to be more specific about the nuanced similarity findings.

6) It would be worth stating a few more details and perhaps providing additional logic or justification in the main text about the pre- and post-exposure phases were set up and why. How many times each object was presented pre and post, and how the sequencing was determined (were any constraints put in place e.g., such that C1 and C2 did not appear close in time?). What was the cover task (I think this is important to the interpretation & so belongs in the main paper)? Were there considerations involving the fact that this is a different sequence of the same objects the participants would later be learning - e.g., interference, etc.?

These details can be found in the Methods section (pages 50-51, lines 1337-1353) and we’ve added a new summary of that section in the Results (page 17, lines 424- 425 and 432-435). In brief, a visual hash tag appeared on a small subset of images and participants pressed a button when this occurred, and C1 and C2 objects were presented in separate scans (as were A and B objects) to minimize inflated neural similarity due to temporal proximity.

Reviewer #2 (Public Review):

The manuscript by Tompary & Davachi presents results from two experiments, one behavior only and one fMRI plus behavior. They examine the important question of how to separate object memories (C1 and C2) that are never experienced together in time and become linked by shared predictive cues in a sequence (A followed by B followed by one of the C items). The authors developed an implicit priming task that provides a novel behavioral metric for such integration. They find significant C1-C2 priming for sequences that were learned 24h prior to the test, but not for recently learned sequences, suggesting that associative links between the two originally separate memories emerge over an extended period of consolidation. The fMRI study relates this behavioral integration effect to two neural metrics: pattern similarity changes in the medial prefrontal cortex (mPFC) as a measure of neural integration, and changes in hippocampal-LOC connectivity as a measure of post-learning consolidation. While fMRI patterns in mPFC overall show differentiation rather than integration (i.e., C1-C2 representational distances become larger), the authors find a robust correlation such that increasing pattern similarity in mPFC relates to stronger integration in the priming test, and this relationship is again specific to remote memories. Moreover, connectivity between the posterior hippocampus and LOC during post-learning rest is positively related to the behavioral integration effect as well as the mPFC neural similarity index, again specifically for remote memories. Overall, this is a coherent set of findings with interesting theoretical implications for consolidation theories, which will be of broad interest to the memory, learning, and predictive coding communities.

Strengths:

1) The implicit associative priming task designed for this study provides a promising new tool for assessing the formation of mnemonic links that influence behavior without explicit retrieval demands. The authors find an interesting dissociation between this implicit measure of memory integration and more commonly used explicit inference measures: a priming effect on the implicit task only evolved after a 24h consolidation period, while the ability to explicitly link the two critical object memories is present immediately after learning. While speculative at this point, these two measures thus appear to tap into neocortical and hippocampal learning processes, respectively, and this potential dissociation will be of interest to future studies investigating time-dependent integration processes in memory.

2) The experimental task is well designed for isolating pre- vs post-learning changes in neural similarity and connectivity, including important controls of baseline neural similarity and connectivity.

3) The main claim of a consolidation-dependent effect is supported by a coherent set of findings that relate behavioral integration to neural changes. The specificity of the effects on remote memories makes the results particularly interesting and compelling.

4) The authors are transparent about unexpected results, for example, the finding that overall similarity in mPFC is consistent with a differentiation rather than an integration model.

Thank you for the positive comments!

Weaknesses:

1) The sequence learning and recognition priming tasks are cleverly designed to isolate the effects of interest while controlling for potential order effects. However, due to the complex nature of the task, it is difficult for the reader to infer all the transition probabilities between item types and how they may influence the behavioral priming results. For example, baseline items (BL) are interspersed between repeated sequences during learning, and thus presumably can only occur before an A item or after a C item. This seems to create non-random predictive relationships such that C is often followed by BL, and BL by A items. If this relationship is reversed during the recognition priming task, where the sequence is always BL-C1-C2, this violation of expectations might slow down reaction times and deflate the baseline measure. It would be helpful if the manuscript explicitly reported transition probabilities for each relevant item type in the priming task relative to the sequence learning task and discussed how a match vs mismatch may influence the observed priming effects.

We have added a table of transition probabilities across the learning, recognition priming, and exposure scans (now Table 1, page 48). We have also included some additional description of the change in transition probabilities across different tasks in the Methods section. Specifically, if participants are indeed learning item types and rules about their order, then both the control and the primed conditions would violate that order. Since C1 and C2 items never appeared together, viewing C1 would give rise to an expectation of seeing a BL item, which would also be violated. This suggests that our priming effects are driven by sequence-specific relationships rather than learning of the probabilities of different item types. We’ve added this consideration to the Methods section (page 45, lines 1212-1221).

Another critical point to consider (and that the transition probabilities do not reflect) is that during learning, while C is followed either by A or BL, they are followed by different A or BL items. In contrast, a given A is always followed by the same B object, which is always followed by one of two C objects. While the order of item types is semi-predictable, the order of objects (specific items) themselves are not. This can be seen in the response times during learning, such that response times for A and BL items are always slower than for B and C items. We have explained this nuance in the figure text for Table 1.

2) The choice of what regions of interest to include in the different sets of analyses could be better motivated. For example, even though briefly discussed in the intro, it remains unclear why the posterior but not the anterior hippocampus is of interest for the connectivity analyses, and why the main target is LOC, not mPFC, given past results including from this group (Tompary & Davachi, 2017). Moreover, for readers not familiar with this literature, it would help if references were provided to suggest that a predictable > unpredictable contrast is well suited for functionally defining mPFC, as done in the present study.

We have clarified our reasoning for each of these choices throughout the manuscript and believe that our logic is now much more transparent. For an expanded reasoning of why we were motivated to look at posterior and not anterior hippocampus, see pages 6-7, lines 135-159, and our response to R2. In brief, past research focusing on post-encoding connectivity with the hippocampus suggests that posterior aspect is more likely to couple with category-selective cortex after learning neutral, non-rewarded objects much like the stimuli used in the present study.

We also clarify our reasoning for LOC over mPFC. While theoretically, mPFC is thought to be a candidate region for coupling with the hippocampus during consolidation, the bulk of empirical work to date has revealed post-encoding connectivity between the hippocampus and category-selective cortex in the ventral and occipital lobes (page 6, lines 123-134).

As for the use of the predictable > unpredictable contrast for functionally defining cortical regions, we reasoned that cortical regions that were sensitive to the temporal regularities generated by the sequences may be further involved in their offline consolidation and long-term storage (Danker & Anderson, 2010; Davachi & Danker, 2013; McClelland et al., 1995). We have added this justification to the Methods section (page 18, lines 454-460).

3) Relatedly, multiple comparison corrections should be applied in the fMRI integration and connectivity analyses whenever the same contrast is performed on multiple regions in an exploratory manner.

We now correct for multiple comparisons using Bonferroni correction, and this correction depends on the number of regions in which each analysis is conducted. Please see page 55, lines 1483-1490, in the Methods section for details of each analysis.

Reviewer #3 (Public Review):

The authors of this manuscript sought to illuminate a link between a behavioral measure of integration and neural markers of cortical integration associated with systems consolidation (post-encoding connectivity, change in representational neural overlap). To that aim, participants incidentally encoded sequences of objects in the fMRI scanner. Unbeknownst to participants, the first two objects of the presented ABC triplet sequences overlapped for a given pair of sequences. This allowed the authors to probe the integration of unique C objects that were never directly presented in the same sequence, but which shared the same preceding A and B objects. They encoded one set of objects on Day 1 (remote condition), another set of objects 24 hours later (recent condition) and tested implicit and explicit memory for the learned sequences on Day 2. They additionally collected baseline and post-encoding resting-state scans. As their measure of behavioral integration, the authors examined reaction time during an Old/New judgement task for C objects depending on if they were preceded by a C object from an overlapping sequence (primed condition) versus a baseline object. They found faster reaction times for the primed objects compared to the control condition for remote but not recently learned objects, suggesting that the C objects from overlapping sequences became integrated over time. They then examined pattern similarity in a priori ROIs as a measure of neural integration and found that participants showing evidence of integration of C objects from overlapping sequences in the medial prefrontal cortex for remotely learned objects also showed a stronger implicit priming effect between those C objects over time. When they examined the change in connectivity between their ROIs after encoding, they also found that connectivity between the posterior hippocampus and lateral occipital cortex correlated with larger priming effects for remotely learned objects, and that lateral occipital connectivity with the medial prefrontal cortex was related to neural integration of remote objects from overlapping sequences.

The authors aim to provide evidence of a relationship between behavioral and neural measures of integration with consolidation is interesting, important, and difficult to achieve given the longitudinal nature of studies required to answer this question. Strengths of this study include a creative behavioral task, and solid modelling approaches for fMRI data with careful control for several known confounds such as bold activation on pattern analysis results, motion, and physiological noise. The authors replicate their behavioral observations across two separate experiments, one of which included a large sample size, and found similar results that speak to the reliability of the observed behavioral phenomenon. In addition, they document several correlations between neural measures and task performance, lending functional significance to their neural findings.

Thank you for this positive assessment of our study!

However, this study is not without notable weaknesses that limit the strength of the manuscript. The authors report a behavioral priming effect suggestive of integration of remote but not recent memories, leading to the interpretation that the priming effect emerges with consolidation. However, they did not observe a reliable interaction between the priming condition and learning session (recent/remote) on reaction times, meaning that the priming effect for remote memories was not reliably greater than that observed for recent. In addition, the emergence of a priming effect for remote memories does not appear to be due to faster reaction times for primed targets over time (the condition of interest), but rather, slower reaction times for control items in the remote condition compared to recent. These issues limit the strength of the claim that the priming effect observed is due to C items of interest being integrated in a consolidation-dependent manner.

We acknowledge that the lack of a day by condition interaction in the behavioral priming effect should discussed and now discuss this data in a more nuanced manner. While it’s true that the priming effect emerges due to a slowing of the control items over time, this slowing is consistent with classic time-dependent effects demonstrating slower response times for more delayed memories. The fact that the response times in the primed condition does not show this slowing can be interpreted as a protection against this slowing that would otherwise occur. Please see page 29, lines 758-766, for this added discussion.

Similarly, the interactions between neural variables of interest and learning session needed to strongly show a significant consolidation-related effect in the brain were sometimes tenuous. There was no reliable difference in neural representational pattern analysis fit to a model of neural integration between the short and long delays in the medial prefrontal cortex or lateral occipital cortex, nor was the posterior hippocampus-lateral occipital cortex post-encoding connectivity correlation with subsequent priming significantly different for recent and remote memories. While the relationship between integration model fit in the medial prefrontal cortex and subsequent priming (which was significantly different from that occurring for recent memories) was one of the stronger findings of the paper in favor of a consolidation-related effect on behavior, is it possible that lack of a behavioral priming effect for recent memories due to possible issues with the control condition could mask a correlation between neural and behavioral integration in the recent memory condition?

While we acknowledge that lack of a statistically reliable interaction between neural measures and behavioral priming in many cases, we are heartened by the reliable difference in the relationship between mPFC similarity and priming over time, which was our main planned prediction. In addition to adding caveats in the discussion about the neural measures and behavioral findings in the recent condition (see our response to R1.1 and R1.4 for more details), we have added language throughout the manuscript noting the need to interpret these data with caution.

These limitations are especially notable when one considers that priming does not classically require a period of prolonged consolidation to occur, and prominent models of systems consolidation rather pertain to explicit memory. While the authors have provided evidence that neural integration in the medial prefrontal cortex, as well as post-encoding coupling between the lateral occipital cortex and posterior hippocampus, are related to faster reaction times for primed objects of overlapping sequences compared to their control condition, more work is needed to verify that the observed findings indeed reflect consolidation dependent integration as proposed.

We agree that more work is needed to provide converging evidence for these novel findings. However, we wish to counter the notion that systems consolidation models are relevant only for explicit memories. Although models of systems consolidation often mention transformations from episodic to semantic memory, the critical mechanisms that define the models involve changes in the neural ensembles of a memory that is initially laid down in the hippocampus and is taught to cortex over time. This transformation of neural traces is not specific to explicit/declarative forms of memory. For example, implicit statistical learning initially depends on intact hippocampal function (Schapiro et al., 2014) and improves over consolidation (Durrant et al., 2011, 2013; Kóbor et al., 2017).

Second, while there are many classical findings of priming during or immediately after learning, there are several instances of priming used to measure consolidation-related changes to newly learned information. For instance, priming has been used as a measure of lexical integration, demonstrating that new word learning benefits from a night of sleep (Wang et al., 2017; Gaskell et al., 2019) or a 1-week delay (Tamminen & Gaskell, 2013). The issue is not whether priming can occur immediately, it is whether priming increases with a delay.

Finally, it is helpful to think about models of memory systems that divide memory representations not by their explicit/implicit nature, but along other important dimensions such as their neural bases, their flexibility vs rigidity, and their capacity for rapid vs slow learning (Henke, 2010). Considering this evidence, we suggest that systems consolidation models are most useful when considering how transformations in the underlying neural memory representation affects its behavioral expression, rather than focusing on the extent that the memory representation is explicit or implicit.

With all this said, we have added text to the discussion reminding the reader that there was no statistically significant difference in priming as a function of the delay (page 29, lines 764 - 766). However, we are encouraged by the fact that the relationship between priming and mPFC neural similarity was significantly stronger for remotely learned objects relative to recently learned ones, as this is directly in line with systems consolidation theories.

References

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Author Response:

Reviewer #3:

The authors modified a previously reported hybrid cytochrome bcc-aa3 supercomplex, consisting of bcc from M. tuberculosis and aa3 from M. smegmatis, (Kim et al 2015) by appending an affinity tag facilitating purification. The cryo-EM experiments are based on the authors' earlier work (Gong et al. 2018) on the structure of the bcc-aa3 supercomplex from M. smegmatis. The authors then determine the structure of the bcc part alone and in complex with Q203 and TB47.

The manuscript is well written and the obtained results are presented in a concise, clear-cut manner. In general, the data support the conclusions drawn.

We thank the reviewer for this evaluation.

To this reviewer, the following points are unclear:

1. The purified enzyme elutes from the gel filtration column as one peak, but there seems to be no information given on the subunit composition and the enzymatic activity of the purified hybrid cytochrome bcc-aa3 supercomplex.

See answers to Question 1 from the major Essential Revisions and Question 1 from the minor Essential Revisions.

"We have now shown that the purified chimeric supercomplex is a functional assembly with a (mean ± s.d., n = 4), in agreement with the previous study that shows M. tuberculosis CIII can functionally complement native M. smegmatis CIII and maintain the growth of M. smegmatis (Kim et al., 2015). The in vitro inhibitions of this enzyme by Q203 and TB47 was determined by means of an DMNQH2/oxygen oxidoreductase activity assay. In the assay, 500 nM Q203 or TB47 was chosen, which is close to the median inhibitory concentration (IC50) obtained from the menadiol-induced oxygen consumption in our previous study (Gong et al., 2018). After addition of Q203 and TB47, the values of turnover number of the hybrid supercomplex are reduced to 5.8 +/- 2.4 e-s-1 (Figure 4-figure supplement 4) and 5.1 +/- 2.9 e-s-1 (Figure 5-figure supplement 4) respectively, from 23.3 +/- 2.4 e-s-1. We have incorporated this new data into the text (lines 90-93, 187-189, 206-209)."

"The subunit composition of the purified enzyme has now been provided in Figure 2-figure supplement 1."

1. It is unclear what is the conclusion of the structure comparison (Fig 6) is regarding the affinity of Q203 for M. smegmatis.

The structural comparison indicates that Q203 should have a similar binding mechanism and a similar effect on the activity of cytochrome bcc from M. smegmatis and M. tuberculosis. This is in good agreement with previous antimycobacterial activity data and inhibition data for the bcc complexes from M. smegmatis and M. tuberculosis (Gong et al., 2018; Lu et al., 2018a). These have now been incorporated into the revised manuscript (line 223-227).

Author Response

Reviewer #1 (Public Review):

This study used a multi-day learning paradigm combined with fMRI to reveal neural changes reflecting the learning of new (arbitrary) shape-sound associations. In the scanner, the shapes and sounds are presented separately and together, both before and after learning. When they are presented together, they can be either consistent or inconsistent with the learned associations. The analyses focus on auditory and visual cortices, as well as the object-selective cortex (LOC) and anterior temporal lobe regions (temporal pole (TP) and perirhinal cortex (PRC)). Results revealed several learning-induced changes, particularly in the anterior temporal lobe regions. First, the LOC and PRC showed a reduced bias to shapes vs sounds (presented separately) after learning. Second, the TP responded more strongly to incongruent than congruent shape-sound pairs after learning. Third, the similarity of TP activity patterns to sounds and shapes (presented separately) was increased for non-matching shape-sound comparisons after learning. Fourth, when comparing the pattern similarity of individual features to combined shape-sound stimuli, the PRC showed a reduced bias towards visual features after learning. Finally, comparing patterns to combined shape-sound stimuli before and after learning revealed a reduced (and negative) similarity for incongruent combinations in PRC. These results are all interpreted as evidence for an explicit integrative code of newly learned multimodal objects, in which the whole is different from the sum of the parts.

The study has many strengths. It addresses a fundamental question that is of broad interest, the learning paradigm is well-designed and controlled, and the stimuli are real 3D stimuli that participants interact with. The manuscript is well written and the figures are very informative, clearly illustrating the analyses performed.

There are also some weaknesses. The sample size (N=17) is small for detecting the subtle effects of learning. Most of the statistical analyses are not corrected for multiple comparisons (ROIs), and the specificity of the key results to specific regions is also not tested. Furthermore, the evidence for an integrative representation is rather indirect, and alternative interpretations for these results are not considered.

We thank the reviewer for their careful reading and the positive comments on our manuscript. As suggested, we have conducted additional analyses of theoretically-motivated ROIs and have found that temporal pole and perirhinal cortex are the only regions to show the key experience-dependent transformations. We are much more cautious with respect to multiple comparisons, and have removed a series of post hoc across-ROI comparisons that were irrelevant to the key questions of the present manuscript. The revised manuscript now includes much more discussion about alternative interpretations as suggested by the reviewer (and also by the other reviewers).

Additionally, we looked into scanning more participants, but our scanner has since had a full upgrade and the sequence used in the current study is no longer supported by our scanner. However, we note that while most analyses contain 17 participants, we employed a within-subject learning design that is not typically used in fMRI experiments and increases our power to detect an effect. This is supported by the robust effect size of the behavioural data, whereby 17 out of 18 participants revealed a learning effect (Cohen’s D = 1.28) and which was replicated in a follow-up experiment with a larger sample size.

We address the other reviewer comments point-by-point in the below.

Reviewer #2 (Public Review):

Li et al. used a four-day fMRI design to investigate how unimodal feature information is combined, integrated, or abstracted to form a multimodal object representation. The experimental question is of great interest and understanding how the human brain combines featural information to form complex representations is relevant for a wide range of researchers in neuroscience, cognitive science, and AI. While most fMRI research on object representations is limited to visual information, the authors examined how visual and auditory information is integrated to form a multimodal object representation. The experimental design is elegant and clever. Three visual shapes and three auditory sounds were used as the unimodal features; the visual shapes were used to create 3D-printed objects. On Day 1, the participants interacted with the 3D objects to learn the visual features, but the objects were not paired with the auditory features, which were played separately. On Day 2, participants were scanned with fMRI while they were exposed to the unimodal visual and auditory features as well as pairs of visual-auditory cues. On Day 3, participants again interacted with the 3D objects but now each was paired with one of the three sounds that played from an internal speaker. On Day 4, participants completed the same fMRI scanning runs they completed on Day 2, except now some visual-auditory feature pairs corresponded with Congruent (learned) objects, and some with Incongruent (unlearned) objects. Using the same fMRI design on Days 2 and 4 enables a well-controlled comparison between feature- and object-evoked neural representations before and after learning. The notable results corresponded to findings in the perirhinal cortex and temporal pole. The authors report (1) that a visual bias on Day 2 for unimodal features in the perirhinal cortex was attenuated after learning on Day 4, (2) a decreased univariate response to congruent vs. incongruent visual-auditory objects in the temporal pole on Day 4, (3) decreased pattern similarity between congruent vs. incongruent pairs of visual and auditory unimodal features in the temporal pole on Day 4, (4) in the perirhinal cortex, visual unimodal features on Day 2 do not correlate with their respective visual-auditory objects on Day 4, and (5) in the perirhinal cortex, multimodal object representations across Days 2 and 4 are uncorrelated for congruent objects and anticorrelated for incongruent. The authors claim that each of these results supports the theory that multimodal objects are represented in an "explicit integrative" code separate from feature representations. While these data are valuable and the results are interesting, the authors' claims are not well supported by their findings.

We thank the reviewer for the careful reading of our manuscript and positive comments. Overall, we now stay closer to the data when describing the results and provide our interpretation of these results in the discussion section while remaining open to alternative interpretations (as also suggested by Reviewer 1).

(1) In the introduction, the authors contrast two theories: (a) multimodal objects are represented in the co-activation of unimodal features, and (b) multimodal objects are represented in an explicit integrative code such that the whole is different than the sum of its parts. However, the distinction between these two theories is not straightforward. An explanation of what is precisely meant by "explicit" and "integrative" would clarify the authors' theoretical stance. Perhaps we can assume that an "explicit" representation is a new representation that is created to represent a multimodal object. What is meant by "integrative" is more ambiguous-unimodal features could be integrated within a representation in a manner that preserves the decodability of the unimodal features, or alternatively the multimodal representation could be completely abstracted away from the constituent features such that the features are no longer decodable. Even if the object representation is "explicit" and distinct from the unimodal feature representations, it can in theory still contain featural information, though perhaps warped or transformed. The authors do not clearly commit to a degree of featural abstraction in their theory of "explicit integrative" multimodal object representations which makes it difficult to assess the validity of their claims.

Due to its ambiguity, we removed the term “explicit” and now make it clear that our central question was whether crossmodal object representations require only unimodal feature-level representations (e.g., frogs are created from only the combination of shape and sound) or whether crossmodal object representations also rely on an integrative code distinct from the unimodal features (e.g., there is something more to “frog” than its original shape and sound). We now clarify this in the revised manuscript.

“One theoretical view from the cognitive sciences suggests that crossmodal objects are built from component unimodal features represented across distributed sensory regions.8 Under this view, when a child thinks about “frog”, the visual cortex represents the appearance of the shape of the frog whereas the auditory cortex represents the croaking sound. Alternatively, other theoretical views predict that multisensory objects are not only built from their component unimodal sensory features, but that there is also a crossmodal integrative code that is different from the sum of these parts.9,10,11,12,13 These latter views propose that anterior temporal lobe structures can act as a polymodal “hub” that combines separate features into integrated wholes.9,11,14,15” – pg. 4

For this reason, we designed our paradigm to equate the unimodal representations, such that neural differences between the congruent and incongruent conditions provide evidence for a crossmodal integrative code different from the unimodal features (because the unimodal features are equated by default in the design).

“Critically, our four-day learning task allowed us to isolate any neural activity associated with integrative coding in anterior temporal lobe structures that emerges with experience and differs from the neural patterns recorded at baseline. The learned and non-learned crossmodal objects were constructed from the same set of three validated shape and sound features, ensuring that factors such as familiarity with the unimodal features, subjective similarity, and feature identity were tightly controlled (Figure 2). If the mind represented crossmodal objects entirely as the reactivation of unimodal shapes and sounds (i.e., objects are constructed from their parts), then there should be no difference between the learned and non-learned objects (because they were created from the same three shapes and sounds). By contrast, if the mind represented crossmodal objects as something over and above their component features (i.e., representations for crossmodal objects rely on integrative coding that is different from the sum of their parts), then there should be behavioral and neural differences between learned and non-learned crossmodal objects (because the only difference across the objects is the learned relationship between the parts). Furthermore, this design allowed us to determine the relationship between the object representation acquired after crossmodal learning and the unimodal feature representations acquired before crossmodal learning. That is, we could examine whether learning led to abstraction of the object representations such that it no longer resembled the unimodal feature representations.” – pg. 5

Furthermore, we agree with the reviewer that our definition and methodological design does not directly capture the structure of the integrative code. With experience, the unimodal feature representations may be completely abstracted away, warped, or changed in a nonlinear transformation. We suggest that crossmodal learning forms an integrative code that is different from the original unimodal representations in the anterior temporal lobes, however, we agree that future work is needed to more directly capture the structure of the integrative code that emerges with experience.

“In our task, participants had to differentiate congruent and incongruent objects constructed from the same three shape and sound features (Figure 2). An efficient way to solve this task would be to form distinct object-level outputs from the overlapping unimodal feature-level inputs such that congruent objects are made to be orthogonal from the representations before learning (i.e., measured as pattern similarity equal to 0 in the perirhinal cortex; Figure 5b, 6, Supplemental Figure S5), whereas non-learned incongruent objects could be made to be dissimilar from the representations before learning (i.e., anticorrelation, measured as patten similarity less than 0 in the perirhinal cortex; Figure 6). Because our paradigm could decouple neural responses to the learned object representations (on Day 4) from the original component unimodal features at baseline (on Day 2), these results could be taken as evidence of pattern separation in the human perirhinal cortex.11,12 However, our pattern of results could also be explained by other types of crossmodal integrative coding. For example, incongruent object representations may be less stable than congruent object representations, such that incongruent objects representation are warped to a greater extent than congruent objects (Figure 6).” – pg. 18

“As one solution to the crossmodal binding problem, we suggest that the temporal pole and perirhinal cortex form unique crossmodal object representations that are different from the distributed features in sensory cortex (Figure 4, 5, 6, Supplemental Figure S5). However, the nature by which the integrative code is structured and formed in the temporal pole and perirhinal cortex following crossmodal experience – such as through transformations, warping, or other factors – is an open question and an important area for future investigation.” – pg. 18

(2) After participants learned the multimodal objects, the authors report a decreased univariate response to congruent visual-auditory objects relative to incongruent objects in the temporal pole. This is claimed to support the existence of an explicit, integrative code for multimodal objects. Given the number of alternative explanations for this finding, this claim seems unwarranted. A simpler interpretation of these results is that the temporal pole is responding to the novelty of the incongruent visual-auditory objects. If there is in fact an explicit, integrative multimodal object representation in the temporal pole, it is unclear why this would manifest in a decreased univariate response.

We thank the reviewer for identifying this issue. Our behavioural design controls unimodal feature-level novelty but allows object-level novelty to differ. Thus, neural differences between the congruent and incongruent conditions reflects sensitivity to the object-level differences between the combination of shape and sound. However, we agree that there are multiple interpretations regarding the nature of how the integrative code is structured in the temporal pole and perirhinal cortex. We have removed the interpretation highlighted by the reviewer from the results. Instead, we now provide our preferred interpretation in the discussion, while acknowledging the other possibilities that the reviewer mentions.

As one possibility, these results in temporal pole may reflect “conceptual combination”. “hummingbird” – a congruent pairing – may require less neural resources than an incongruent pairing such as “bark-frog”.

“Furthermore, these distinct anterior temporal lobe structures may be involved with integrative coding in different ways. For example, the crossmodal object representations measured after learning were found to be related to the component unimodal feature representations measured before learning in the temporal pole but not the perirhinal cortex (Figure 5, 6, Supplemental Figure S5). Moreover, pattern similarity for congruent shape-sound pairs were lower than the pattern similarity for incongruent shape-sound pairs after crossmodal learning in the temporal pole but not the perirhinal cortex (Figure 4b, Supplemental Figure S3a). As one interpretation of this pattern of results, the temporal pole may represent new crossmodal objects by combining previously learned knowledge. 8,9,10,11,13,14,15,33 Specifically, research into conceptual combination has linked the anterior temporal lobes to compound object concepts such as “hummingbird”.34,35,36 For example, participants during our task may have represented the sound-based “humming” concept and visually-based “bird” concept on Day 1, forming the crossmodal “hummingbird” concept on Day 3; Figure 1, 2, which may recruit less activity in temporal pole than an incongruent pairing such as “barking-frog”. For these reasons, the temporal pole may form a crossmodal object code based on pre-existing knowledge, resulting in reduced neural activity (Figure 3d) and pattern similarity towards features associated with learned objects (Figure 4b).”– pg. 18

(3) The authors ran a neural pattern similarity analysis on the unimodal features before and after multimodal object learning. They found that the similarity between visual and auditory features that composed congruent objects decreased in the temporal pole after multimodal object learning. This was interpreted to reflect an explicit integrative code for multimodal objects, though it is not clear why. First, behavioral data show that participants reported increased similarity between the visual and auditory unimodal features within congruent objects after learning, the opposite of what was found in the temporal pole. Second, it is unclear why an analysis of the unimodal features would be interpreted to reflect the nature of the multimodal object representations. Since the same features corresponded with both congruent and incongruent objects, the nature of the feature representations cannot be interpreted to reflect the nature of the object representations per se. Third, using unimodal feature representations to make claims about object representations seems to contradict the theoretical claim that explicit, integrative object representations are distinct from unimodal features. If the learned multimodal object representation exists separately from the unimodal feature representations, there is no reason why the unimodal features themselves would be influenced by the formation of the object representation. Instead, these results seem to more strongly support the theory that multimodal object learning results in a transformation or warping of feature space.

We apologize for the lack of clarity. We have now overhauled this aspect of our manuscript in an attempt to better highlight key aspects of our experimental design. In particular, because the unimodal features composing the congruent and incongruent objects were equated, neural differences between these conditions would provide evidence for an experience-dependent crossmodal integrative code that is different from its component unimodal features.

Related to the second and third points, we were looking at the extent to which the original unimodal representations change with crossmodal learning. Before crossmodal learning, we found that the perirhinal cortex tracked the similarity between the individual visual shape features and the crossmodal objects that were composed of those visual shapes – however, there was no evidence that perirhinal cortex was tracking the unimodal sound features on those crossmodal objects. After crossmodal learning, we see that this visual shape bias in perirhinal cortex was no longer present – that is, the representation in perirhinal cortex started to look less like the visual features that comprise the objects. Thus, crossmodal learning transformed the perirhinal representations so that they were no longer predominantly grounded in a single visual modality, which may be a mechanism by which object concepts gain their abstraction. We have now tried to be clearer about this interpretation throughout the paper.

Notably, we suggest that experience may change both the crossmodal object representations, as well as the unimodal feature representations. For example, we have previously shown that unimodal visual features are influenced by experience in parallel with the representation of the conjunction (e.g., Liang et al., 2020; Cerebral Cortex). Nevertheless, we remain open to the myriad possible structures of the integrative code that might emerge with experience.

We now clarify these points throughout the manuscript. For example:

“We then examined whether the original representations would change after participants learned how the features were paired together to make specific crossmodal objects, conducting the same analysis described above after crossmodal learning had taken place (Figure 5b). With this analysis, we sought to measure the relationship between the representation for the learned crossmodal object and the original baseline representation for the unimodal features. More specifically, the voxel-wise activity for unimodal feature runs before crossmodal learning was correlated to the voxel-wise activity for crossmodal object runs after crossmodal learning (Figure 5b). Another linear mixed model which included modality as a fixed factor within each ROI revealed that the perirhinal cortex was no longer biased towards visual shape after crossmodal learning (F1,32 = 0.12, p = 0.73), whereas the temporal pole, LOC, V1, and A1 remained biased towards either visual shape or sound (F1,30-32 between 16.20 and 73.42, all p < 0.001, η2 between 0.35 and 0.70).” – pg. 14

“To investigate this effect in perirhinal cortex more specifically, we conducted a linear mixed model to directly compare the change in the visual bias of perirhinal representations from before crossmodal learning to after crossmodal learning (green regions in Figure 5a vs. 5b). Specifically, the linear mixed model included learning day (before vs. after crossmodal learning) and modality (visual feature match to crossmodal object vs. sound feature match to crossmodal object). Results revealed a significant interaction between learning day and modality in the perirhinal cortex (F1,775 = 5.56, p = 0.019, η2 = 0.071), meaning that the baseline visual shape bias observed in perirhinal cortex (green region of Figure 5a) was significantly attenuated with experience (green region of Figure 5b). After crossmodal learning, a given shape no longer invoked significant pattern similarity between objects that had the same shape but differed in terms of what they sounded like. Taken together, these results suggest that prior to learning the crossmodal objects, the perirhinal cortex had a default bias toward representing the visual shape information and was not representing sound information of the crossmodal objects. After crossmodal learning, however, the visual shape bias in perirhinal cortex was no longer present. That is, with crossmodal learning, the representations within perirhinal cortex started to look less like the visual features that comprised the crossmodal objects, providing evidence that the perirhinal representations were no longer predominantly grounded in the visual modality.” – pg. 13

“Importantly, the initial visual shape bias observed in the perirhinal cortex was attenuated by experience (Figure 5, Supplemental Figure S5), suggesting that the perirhinal representations had become abstracted and were no longer predominantly grounded in a single modality after crossmodal learning. One possibility may be that the perirhinal cortex is by default visually driven as an extension to the ventral visual stream,10,11,12 but can act as a polymodal “hub” region for additional crossmodal input following learning.” – pg. 19

(4) The most compelling evidence the authors provide for their theoretical claims is the finding that, in the perirhinal cortex, the unimodal feature representations on Day 2 do not correlate with the multimodal objects they comprise on Day 4. This suggests that the learned multimodal object representations are not combinations of their unimodal features. If unimodal features are not decodable within the congruent object representations, this would support the authors' explicit integrative hypothesis. However, the analyses provided do not go all the way in convincing the reader of this claim. First, the analyses reported do not differentiate between congruent and incongruent objects. If this result in the perirhinal cortex reflects the formation of new multimodal object representations, it should only be true for congruent objects but not incongruent objects. Since the analyses combine congruent and incongruent objects it is not possible to know whether this was the case. Second, just because feature representations on Day 2 do not correlate with multimodal object patterns on Day 4 does not mean that the object representations on Day 4 do not contain featural information. This could be directly tested by correlating feature representations on Day 4 with congruent vs. incongruent object representations on Day 4. It could be that representations in the perirhinal cortex are not stable over time and all representations-including unimodal feature representations-shift between sessions, which could explain these results yet not entail the existence of abstracted object representations.

We thank the reviewer for this suggestion and have conducted the two additional analyses. Specifically, we split the congruent and incongruent conditions and also investigated correlations between unimodal representations on Day 4 with crossmodal object representations on Day 4. There was no significant interaction between modality and congruency in any ROI across or within learning days. One possible explanation for these findings is that both congruent and incongruent crossmodal objects are represented differently from their underlying unimodal features, and all of these representations can transform with experience.

However, the new analyses also revealed that perirhinal cortex was the only region without a modality-specific bias after crossmodal learning (e.g., Day 4 Unimodal Feature runs x Day 4 Crossmodal Object runs; now shown in Supplemental Figure S5). Overall, these results are consistent with the notion of a crossmodal integrative code in perirhinal cortex that has changed with experience and is different from the component unimodal features. Nevertheless, we explore alternative interpretations for how the crossmodal code emerges with experience in the discussion.

“To examine whether these results differed by congruency (i.e., whether any modality-specific biases differed as a function of whether the object was congruent or incongruent), we conducted exploratory linear mixed models for each of the five a priori ROIs across learning days. More specifically, we correlated: 1) the voxel-wise activity for Unimodal Feature Runs before crossmodal learning to the voxel-wise activity for Crossmodal Object Runs before crossmodal learning (Day 2 vs. Day 2), 2) the voxel-wise activity for Unimodal Feature Runs before crossmodal learning to the voxel-wise activity for Crossmodal Object Runs after crossmodal learning (Day 2 vs Day 4), and 3) the voxel-wise activity for Unimodal Feature Runs after crossmodal learning to the voxel-wise activity for Crossmodal Object Runs after crossmodal learning (Day 4 vs Day 4). For each of the three analyses described, we then conducted separate linear mixed models which included modality (visual feature match to crossmodal object vs. sound feature match to crossmodal object) and congruency (congruent vs. incongruent)….There was no significant relationship between modality and congruency in any ROI between Day 2 and Day 2 (F1,346-368 between 0.00 and 1.06, p between 0.30 and 0.99), between Day 2 and Day 4 (F1,346-368 between 0.021 and 0.91, p between 0.34 and 0.89), or between Day 4 and Day 4 (F1,346-368 between 0.01 and 3.05, p between 0.082 and 0.93). However, exploratory analyses revealed that perirhinal cortex was the only region without a modality-specific bias and where the unimodal feature runs were not significantly correlated to the crossmodal object runs after crossmodal learning (Supplemental Figure S5).” – pg. 14

“Taken together, the overall pattern of results suggests that representations of the crossmodal objects in perirhinal cortex were heavily influenced by their consistent visual features before crossmodal learning. However, the crossmodal object representations were no longer influenced by the component visual features after crossmodal learning (Figure 5, Supplemental Figure S5). Additional exploratory analyses did not find evidence of experience-dependent changes in the hippocampus or inferior parietal lobes (Supplemental Figure S4c-e).” – pg. 14

“The voxel-wise matrix for Unimodal Feature runs on Day 4 were correlated to the voxel-wise matrix for Crossmodal Object runs on Day 4 (see Figure 5 in the main text for an example). We compared the average pattern similarity (z-transformed Pearson correlation) between shape (blue) and sound (orange) features specifically after crossmodal learning. Consistent with Figure 5b, perirhinal cortex was the only region without a modality-specific bias. Furthermore, perirhinal cortex was the only region where the representations of both the visual and sound features were not significantly correlated to the crossmodal objects. By contrast, every other region maintained a modality-specific bias for either the visual or sound features. These results suggest that perirhinal cortex representations were transformed with experience, such that the initial visual shape representations (Figure 5a) were no longer grounded in a single modality after crossmodal learning. Furthermore, these results suggest that crossmodal learning formed an integrative code different from the unimodal features in perirhinal cortex, as the visual and sound features were not significantly correlated with the crossmodal objects. * p < 0.05, ** p < 0.01, *** p < 0.001. Horizontal lines within brain regions indicate a significant main effect of modality. Vertical asterisks denote pattern similarity comparisons relative to 0.” – Supplemental Figure S5

“We found that the temporal pole and perirhinal cortex – two anterior temporal lobe structures – came to represent new crossmodal object concepts with learning, such that the acquired crossmodal object representations were different from the representation of the constituent unimodal features (Figure 5, 6). Intriguingly, the perirhinal cortex was by default biased towards visual shape, but that this initial visual bias was attenuated with experience (Figure 3c, 5, Supplemental Figure S5). Within the perirhinal cortex, the acquired crossmodal object concepts (measured after crossmodal learning) became less similar to their original component unimodal features (measured at baseline before crossmodal learning); Figure 5, 6, Supplemental Figure S5. This is consistent with the idea that object representations in perirhinal cortex integrate the component sensory features into a whole that is different from the sum of the component parts, which might be a mechanism by which object concepts obtain their abstraction…. As one solution to the crossmodal binding problem, we suggest that the temporal pole and perirhinal cortex form unique crossmodal object representations that are different from the distributed features in sensory cortex (Figure 4, 5, 6, Supplemental Figure S5). However, the nature by which the integrative code is structured and formed in the temporal pole and perirhinal cortex following crossmodal experience – such as through transformations, warping, or other factors – is an open question and an important area for future investigation.” – pg. 18

In sum, the authors have collected a fantastic dataset that has the potential to answer questions about the formation of multimodal object representations in the brain. A more precise delineation of different theoretical accounts and additional analyses are needed to provide convincing support for the theory that “explicit integrative” multimodal object representations are formed during learning.

We thank the reviewer for the positive comments and helpful feedback. We hope that our changes to our wording and clarifications to our methodology now more clearly supports the central goal of our study: to find evidence of crossmodal integrative coding different from the original unimodal feature parts in anterior temporal lobe structures. We furthermore agree that future research is needed to delineate the structure of the integrative code that emerges with experience in the anterior temporal lobes.

Reviewer #3 (Public Review):

This paper uses behavior and functional brain imaging to understand how neural and cognitive representations of visual and auditory stimuli change as participants learn associations among them. Prior work suggests that areas in the anterior temporal (ATL) and perirhinal cortex play an important role in learning/representing cross-modal associations, but the hypothesis has not been directly tested by evaluating behavior and functional imaging before and after learning cross- modal associations. The results show that such learning changes both the perceived similarities amongst stimuli and the neural responses generated within ATL and perirhinal regions, providing novel support for the view that cross-modal learning leads to a representational change in these regions.

This work has several strengths. It tackles an important question for current theories of object representation in the mind and brain in a novel and quite direct fashion, by studying how these representations change with cross-modal learning. As the authors note, little work has directly assessed representational change in ATL following such learning, despite the widespread view that ATL is critical for such representation. Indeed, such direct assessment poses several methodological challenges, which the authors have met with an ingenious experimental design. The experiment allows the authors to maintain tight control over both the familiarity and the perceived similarities amongst the shapes and sounds that comprise their stimuli so that the observed changes across sessions must reflect learned cross-modal associations among these. I especially appreciated the creation of physical objects that participants can explore and the approach to learning in which shapes and sounds are initially experienced independently and later in an associated fashion. In using multi-echo MRI to resolve signals in ventral ATL, the authors have minimized a key challenge facing much work in this area (namely the poor SNR yielded by standard acquisition sequences in ventral ATL). The use of both univariate and multivariate techniques was well-motivated and helpful in testing the central questions. The manuscript is, for the most part, clearly written, and nicely connects the current work to important questions in two literatures, specifically (1) the hypothesized role of the perirhinal cortex in representing/learning complex conjunctions of features and (2) the tension between purely embodied approaches to semantic representation vs the view that ATL regions encode important amodal/crossmodal structure.

There are some places in the manuscript that would benefit from further explanation and methodological detail. I also had some questions about the results themselves and what they signify about the roles of ATL and the perirhinal cortex in object representation.

We thank the reviewer for their positive feedback and address the comments in the below point-by-point responses.

(A) I found the terms "features" and "objects" to be confusing as used throughout the manuscript, and sometimes inconsistent. I think by "features" the authors mean the shape and sound stimuli in their experiment. I think by "object" the authors usually mean the conjunction of a shape with a sound---for instance, when a shape and sound are simultaneously experienced in the scanner, or when the participant presses a button on the shape and hears the sound. The confusion comes partly because shapes are often described as being composed of features, not features in and of themselves. (The same is sometimes true of sounds). So when reading "features" I kept thinking the paper referred to the elements that went together to comprise a shape. It also comes from ambiguous use of the word object, which might refer to (a) the 3D- printed item that people play with, which is an object, or (b) a visually-presented shape (for instance, the localizer involved comparing an "object" to a "phase-scrambled" stimulus---here I assume "object" refers to an intact visual stimulus and not the joint presentation of visual and auditory items). I think the design, stimuli, and results would be easier for a naive reader to follow if the authors used the terms "unimodal representation" to refer to cases where only visual or auditory input is presented, and "cross-modal" or "conjoint" representation when both are present.

We thank the reviewer for this suggestion and agree. We have replaced the terms “features” and “objects” with “unimodal” and “crossmodal” in the title, text, and figures throughout the manuscript for consistency (i.e., “crossmodal binding problem”). To simplify the terminology, we have also removed the localizer results.

(B) There are a few places where I wasn't sure what exactly was done, and where the methods lacked sufficient detail for another scientist to replicate what was done. Specifically:

(1) The behavioral study assessing perceptual similarity between visual and auditory stimuli was unclear. The procedure, stimuli, number of trials, etc, should be explained in sufficient detail in methods to allow replication. The results of the study should also minimally be reported in the supplementary information. Without an understanding of how these studies were carried out, it was very difficult to understand the observed pattern of behavioral change. For instance, I initially thought separate behavioral blocks were carried out for visual versus auditory stimuli, each presented in isolation; however, the effects contrast congruent and incongruent stimuli, which suggests these decisions must have been made for the conjoint presentation of both modalities. I'm still not sure how this worked. Additionally, the manuscript makes a brief mention that similarity judgments were made in the context of "all stimuli," but I didn't understand what that meant. Similarity ratings are hugely sensitive to the contrast set with which items appear, so clarity on these points is pretty important. A strength of the design is the contention that shape and sound stimuli were psychophysically matched, so it is important to show the reader how this was done and what the results were.

We agree and apologize for the lack of sufficient detail in the original manuscript. We now include much more detail about the similarity rating task. The methodology and results of the behavioral rating experiments are now shown in Supplemental Figure S1. In Figure S1a, the similarity ratings are visualized on a multidimensional scaling plot. The triangular geometry for shape (blue) and sound (red) indicate that the subjective similarity was equated within each unimodal feature across individual participants. Quantitatively, there was no difference in similarity between the congruent and incongruent pairings in Figure S1b and Figure S1c prior to crossmodal learning. In addition to providing more information on these methods in the Supplemental Information, we also now provide a more detailed description of the task in the manuscript itself. For convenience, we reproduce these sections below.

“Pairwise Similarity Task. Using the same task as the stimulus validation procedure (Supplemental Figure S1a), participants provided similarity ratings for all combinations of the 3 validated shapes and 3 validated sounds (each of the six features were rated in the context of every other feature in the set, with 4 repeats of the same feature, for a total of 72 trials). More specifically, three stimuli were displayed on each trial, with one at the top and two at the bottom of the screen in the same procedure as we have used previously27. The 3D shapes were visually displayed as a photo, whereas sounds were displayed on screen in a box that could be played over headphones when clicked with the mouse. The participant made an initial judgment by selecting the more similar stimulus on the bottom relative to the stimulus on the top. Afterwards, the participant made a similarity rating between each bottom stimulus with the top stimulus from 0 being no similarity to 5 being identical. This procedure ensured that ratings were made relative to all other stimuli in the set.”– pg. 28

“Pairwise similarity task and results. In the initial stimulus validation experiment, participants provided pairwise ratings for 5 sounds and 3 shapes. The shapes were equated in their subjective similarity that had been selected from a well-characterized perceptually uniform stimulus space27 and the pairwise ratings followed the same procedure as described in ref 27. Based on this initial experiment, we then selected the 3 sounds from the that were most closely equated in their subjective similarity. (a) 3D-printed shapes were displayed as images, whereas sounds were displayed in a box that could be played when clicked by the participant. Ratings were averaged to produce a similarity matrix for each participant, and then averaged to produce a group-level similarity matrix. Shown as triangular representational geometries recovered from multidimensional scaling in the above, shapes (blue) and sounds (orange) were approximately equated in their subjective similarity. These features were then used in the four-day crossmodal learning task. (b) Behavioral results from the four-day crossmodal learning task paired with multi-echo fMRI described in the main text. Before crossmodal learning, there was no difference in similarity between shape and sound features associated with congruent objects compared to incongruent objects – indicating that similarity was controlled at the unimodal feature-level. After crossmodal learning, we observed a robust shift in the magnitude of similarity. The shape and sound features associated with congruent objects were now significantly more similar than the same shape and sound features associated with incongruent objects (p < 0.001), evidence that crossmodal learning changed how participants experienced the unimodal features (observed in 17/18 participants). (c) We replicated this learning-related shift in pattern similarity with a larger sample size (n = 44; observed in 38/44 participants). *** denotes p < 0.001. Horizontal lines denote the comparison of congruent vs. incongruent conditions. – Supplemental Figure S1

(2) The experiences through which participants learned/experienced the shapes and sounds were unclear. The methods mention that they had one minute to explore/palpate each shape and that these experiences were interleaved with other tasks, but it is not clear what the other tasks were, how many such exploration experiences occurred, or how long the total learning time was. The manuscript also mentions that participants learn the shape-sound associations with 100% accuracy but it isn't clear how that was assessed. These details are important partly b/c it seems like very minimal experience to change neural representations in the cortex.

We apologize for the lack of detail and agree with the reviewer’s suggestions – we now include much more information in the methods section. Each behavioral day required about 1 hour of total time to complete, and indeed, participants rapidly learned their associations with minimal experience. For example:

“Behavioral Tasks. On each behavioral day (Day 1 and Day 3; Figure 2), participants completed the following tasks, in this order: Exploration Phase, one Unimodal Feature 1-back run (26 trials), Exploration Phase, one Crossmodal 1-back run (26 trials), Exploration Phase, Pairwise Similarity Task (24 trials), Exploration Phase, Pairwise Similarity Task (24 trials), Exploration Phase, Pairwise Similarity Task (24 trials), and finally, Exploration Phase. To verify learning on Day 3, participants also additionally completed a Learning Verification Task at the end of the session. – pg. 27

“The overall procedure ensured that participants extensively explored the unimodal features on Day 1 and the crossmodal objects on Day 3. The Unimodal Feature and the Crossmodal Object 1-back runs administered on Day 1 and Day 3 served as practice for the neuroimaging sessions on Day 2 and Day 4, during which these 1-back tasks were completed. Each behavioral session required less than 1 hour of total time to complete.” – pg. 27

“Learning Verification Task (Day 3 only). As the final task on Day 3, participants completed a task to ensure that participants successfully formed their crossmodal pairing. All three shapes and sounds were randomly displayed in 6 boxes on a display. Photos of the 3D shapes were shown, and sounds were played by clicking the box with the mouse cursor. The participant was cued with either a shape or sound, and then selected the corresponding paired feature. At the end of Day 3, we found that all participants reached 100% accuracy on this task (10 trials).” – pg. 29

(3) I didn't understand the similarity metric used in the multivariate imaging analyses. The manuscript mentions Z-scored Pearson's r, but I didn't know if this meant (a) many Pearson coefficients were computed and these were then Z-scored, so that 0 indicates a value equal to the mean Pearson correlation and 1 is equal to the standard deviation of the correlations, or (b) whether a Fisher Z transform was applied to each r (so that 0 means r was also around 0). From the interpretation of some results, I think the latter is the approach taken, but in general, it would be helpful to see, in Methods or Supplementary information, exactly how similarity scores were computed, and why that approach was adopted. This is particularly important since it is hard to understand the direction of some key effects.

The reviewer is correct that the Fisher Z transform was applied to each individual r before averaging the correlations. This approach is generally recommended when averaging correlations (see Corey, Dunlap, & Burke, 1998). We are now clearer on this point in the manuscript:

“The z-transformed Pearson’s correlation coefficient was used as the distance metric for all pattern similarity analyses. More specifically, each individual Pearson correlation was Fisher z-transformed and then averaged (see 61).” – pg. 32

(C) From Figure 3D, the temporal pole mask appears to exclude the anterior fusiform cortex (or the ventral surface of the ATL generally). If so, this is a shame, since that appears to be the locus most important to cross-modal integration in the "hub and spokes" model of semantic representation in the brain. The observation in the paper that the perirhinal cortex seems initially biased toward visual structure while more superior ATL is biased toward auditory structure appears generally consistent with the "graded hub" view expressed, for instance, in our group's 2017 review paper (Lambon Ralph et al., Nature Reviews Neuroscience). The balance of visual- versus auditory-sensitivity in that work appears balanced in the anterior fusiform, just a little lateral to the anterior perirhinal cortex. It would be helpful to know if the same pattern is observed for this area specifically in the current dataset.

We thank the reviewer for this suggestion. After close inspection of Lambon Ralph et al. (2017), we believe that our perirhinal cortex mask appears to be overlapping with the ventral ATL/anterior fusiform region that the reviewer mentions. See Author response image 1 for a visual comparison:

Author response image 1.

The top four figures are sampled from Lambon Ralph et al (2017), whereas the bottom two figures visualize our perirhinal cortex mask (white) and temporal pole mask (dark green) relative to the fusiform cortex. The ROIs visualized were defined from the Harvard-Oxford atlas.

We now mention this area of overlap in our manuscript and link it to the hub and spokes model:

“Notably, our perirhinal cortex mask overlaps with a key region of the ventral anterior temporal lobe thought to be the central locus of crossmodal integration in the “hub and spokes” model of semantic representations.9,50 – pg. 20

(D) While most effects seem robust from the information presented, I'm not so sure about the analysis of the perirhinal cortex shown in Figure 5. This compares (I think) the neural similarity evoked by a unimodal stimulus ("feature") to that evoked by the same stimulus when paired with its congruent stimulus in the other modality ("object"). These similarities show an interaction with modality prior to cross-modal association, but no interaction afterward, leading the authors to suggest that the perirhinal cortex has become less biased toward visual structure following learning. But the plots in Figures 4a and b are shown against different scales on the y-axes, obscuring the fact that all of the similarities are smaller in the after-learning comparison. Since the perirhinal interaction was already the smallest effect in the pre-learning analysis, it isn't really surprising that it drops below significance when all the effects diminish in the second comparison. A more rigorous test would assess the reliability of the interaction of comparison (pre- or post-learning) with modality. The possibility that perirhinal representations become less "visual" following cross-modal learning is potentially important so a post hoc contrast of that kind would be helpful.

We apologize for the lack of clarity. We conducted a linear mixed model to assess the interaction between modality and crossmodal learning day (before and after crossmodal learning) in the perirhinal cortex as described by the reviewer. The critical interaction was significant, which is now clarified in the text as well as in the rescaled figure plots.

“To investigate this effect in perirhinal cortex more specifically, we conducted a linear mixed model to directly compare the change in the visual bias of perirhinal representations from before crossmodal learning to after crossmodal learning (green regions in Figure 5a vs. 5b). Specifically, the linear mixed model included learning day (before vs. after crossmodal learning) and modality (visual feature match to crossmodal object vs. sound feature match to crossmodal object). Results revealed a significant interaction between learning day and modality in the perirhinal cortex (F1,775 = 5.56, p = 0.019, η2 = 0.071), meaning that the baseline visual shape bias observed in perirhinal cortex (green region of Figure 5a) was significantly attenuated with experience (green region of Figure 5b). After crossmodal learning, a given shape no longer invoked significant pattern similarity between objects that had the same shape but differed in terms of what they sounded like. Taken together, these results suggest that prior to learning the crossmodal objects, the perirhinal cortex had a default bias toward representing the visual shape information and was not representing sound information of the crossmodal objects. After crossmodal learning, however, the visual shape bias in perirhinal cortex was no longer present. That is, with crossmodal learning, the representations within perirhinal cortex started to look less like the visual features that comprised the crossmodal objects, providing evidence that the perirhinal representations were no longer predominantly grounded in the visual modality.” – pg. 13

We note that not all effects drop in Figure 5b (even in regions with a similar numerical pattern similarity to PRC, like the hippocampus – also see Supplemental Figure S5 for a comparison for patterns only on Day 4), suggesting that the change in visual bias in PRC is not simply due to noise.

“Importantly, the change in pattern similarity in the perirhinal cortex across learning days (Figure 5) is unlikely to be driven by noise, poor alignment of patterns across sessions, or generally reduced responses. Other regions with numerically similar pattern similarity to perirhinal cortex did not change across learning days (e.g., visual features x crossmodal objects in A1 in Figure 5; the exploratory ROI hippocampus with numerically similar pattern similarity to perirhinal cortex also did not change in Supplemental Figure S4c-d).” – pg. 14

(E) Is there a reason the authors did not look at representation and change in the hippocampus? As a rapid-learning, widely-connected feature-binding mechanism, and given the fairly minimal amount of learning experience, it seems like the hippocampus would be a key area of potential import for the cross-modal association. It also looks as though the hippocampus is implicated in the localizer scan (Figure 3c).

We thank the reviewer for this suggestion and now include additional analyses for the hippocampus. We found no evidence of crossmodal integrative coding different from the unimodal features. Rather, the hippocampus seems to represent the convergence of unimodal features, as evidenced by …[can you give some pithy description for what is meant by “convergence” vs “integration”?]. We provide these results in the Supplemental Information and describe them in the main text:

“Analyses for the hippocampus (HPC) and inferior parietal lobe (IPL). (a) In the visual vs. auditory univariate analysis, there was no visual or sound bias in HPC, but there was a bias towards sounds that increased numerically after crossmodal learning in the IPL. (b) Pattern similarity analyses between unimodal features associated with congruent objects and incongruent objects. Similar to Supplemental Figure S3, there was no main effect of congruency in either region. (c) When we looked at the pattern similarity between Unimodal Feature runs on Day 2 to Crossmodal Object runs on Day 2, we found that there was significant pattern similarity when there was a match between the unimodal feature and the crossmodal object (e.g., pattern similarity > 0). This pattern of results held when (d) correlating the Unimodal Feature runs on Day 2 to Crossmodal Object runs on Day 4, and (e) correlating the Unimodal Feature runs on Day 4 to Crossmodal Object runs on Day 4. Finally, (f) there was no significant pattern similarity between Crossmodal Object runs before learning correlated to Crossmodal Object after learning in HPC, but there was significant pattern similarity in IPL (p < 0.001). Taken together, these results suggest that both HPC and IPL are sensitive to visual and sound content, as the (c, d, e) unimodal feature-level representations were correlated to the crossmodal object representations irrespective of learning day. However, there was no difference between congruent and incongruent pairings in any analysis, suggesting that HPC and IPL did not represent crossmodal objects differently from the component unimodal features. For these reasons, HPC and IPL may represent the convergence of unimodal feature representations (i.e., because HPC and IPL were sensitive to both visual and sound features), but our results do not seem to support these regions in forming crossmodal integrative coding distinct from the unimodal features (i.e., because representations in HPC and IPL did not differentiate the congruent and incongruent conditions and did not change with experience). * p < 0.05, ** p < 0.01, *** p < 0.001. Asterisks above or below bars indicate a significant difference from zero. Horizontal lines within brain regions in (a) reflect an interaction between modality and learning day, whereas horizontal lines within brain regions in reflect main effects of (b) learning day, (c-e) modality, or (f) congruency.” – Supplemental Figure S4.

“Notably, our perirhinal cortex mask overlaps with a key region of the ventral anterior temporal lobe thought to be the central locus of crossmodal integration in the “hub and spokes” model of semantic representations.9,50 However, additional work has also linked other brain regions to the convergence of unimodal representations, such as the hippocampus51,52,53 and inferior parietal lobes.54,55 This past work on the hippocampus and inferior parietal lobe does not necessarily address the crossmodal binding problem that was the main focus of our present study, as previous findings often do not differentiate between crossmodal integrative coding and the convergence of unimodal feature representations per se. Furthermore, previous studies in the literature typically do not control for stimulus-based factors such as experience with unimodal features, subjective similarity, or feature identity that may complicate the interpretation of results when determining regions important for crossmodal integration. Indeed, we found evidence consistent with the convergence of unimodal feature-based representations in both the hippocampus and inferior parietal lobes (Supplemental Figure S4), but no evidence of crossmodal integrative coding different from the unimodal features. The hippocampus and inferior parietal lobes were both sensitive to visual and sound features before and after crossmodal learning (see Supplemental Figure S4c-e). Yet the hippocampus and inferior parietal lobes did not differentiate between the congruent and incongruent conditions or change with experience (see Supplemental Figure S4).” – pg. 20

(F) The direction of the neural effects was difficult to track and understand. I think the key observation is that TP and PRh both show changes related to cross-modal congruency - but still it would be helpful if the authors could articulate, perhaps via a schematic illustration, how they think representations in each key area are changing with the cross-modal association. Why does the temporal pole come to activate less for congruent than incongruent stimuli (Figure 3)? And why do TP responses grow less similar to one another for congruent relative to incongruent stimuli after learning (Figure 4)? Why are incongruent stimulus similarities anticorrelated in their perirhinal responses following cross-modal learning (Figure 6)?

We thank the author for identifying this issue, which was also raised by the other reviewers. The reviewer is correct that the key observation is that the TP and PRC both show changes related to crossmodal congruency (given that the unimodal features were equated in the methodological design). However, the structure of the integrative code is less clear, which we now emphasize in the main text. Our findings provide evidence of a crossmodal integrative code that is different from the unimodal features, and future studies are needed to better understand the structure of how such a code might emerge. We now more clearly highlight this distinction throughout the paper:

“By contrast, perirhinal cortex may be involved in pattern separation following crossmodal experience. In our task, participants had to differentiate congruent and incongruent objects constructed from the same three shape and sound features (Figure 2). An efficient way to solve this task would be to form distinct object-level outputs from the overlapping unimodal feature-level inputs such that congruent objects are made to be orthogonal from the representations before learning (i.e., measured as pattern similarity equal to 0 in the perirhinal cortex; Figure 5b, 6, Supplemental Figure S5), whereas non-learned incongruent objects could be made to be dissimilar from the representations before learning (i.e., anticorrelation, measured as patten similarity less than 0 in the perirhinal cortex; Figure 6). Because our paradigm could decouple neural responses to the learned object representations (on Day 4) from the original component unimodal features at baseline (on Day 2), these results could be taken as evidence of pattern separation in the human perirhinal cortex.11,12 However, our pattern of results could also be explained by other types of crossmodal integrative coding. For example, incongruent object representations may be less stable than congruent object representations, such that incongruent objects representation are warped to a greater extent than congruent objects (Figure 6).” – pg. 18

“As one solution to the crossmodal binding problem, we suggest that the temporal pole and perirhinal cortex form unique crossmodal object representations that are different from the distributed features in sensory cortex (Figure 4, 5, 6, Supplemental Figure S5). However, the nature by which the integrative code is structured and formed in the temporal pole and perirhinal cortex following crossmodal experience – such as through transformations, warping, or other factors – is an open question and an important area for future investigation. Furthermore, these anterior temporal lobe structures may be involved with integrative coding in different ways. For example, the crossmodal object representations measured after learning were found to be related to the component unimodal feature representations measured before learning in the temporal pole but not the perirhinal cortex (Figure 5, 6, Supplemental Figure S5). Moreover, pattern similarity for congruent shape-sound pairs were lower than the pattern similarity for incongruent shape-sound pairs after crossmodal learning in the temporal pole but not the perirhinal cortex (Figure 4b, Supplemental Figure S3a). As one interpretation of this pattern of results, the temporal pole may represent new crossmodal objects by combining previously learned knowledge. 8,9,10,11,13,14,15,33 Specifically, research into conceptual combination has linked the anterior temporal lobes to compound object concepts such as “hummingbird”.34,35,36 For example, participants during our task may have represented the sound-based “humming” concept and visually-based “bird” concept on Day 1, forming the crossmodal “hummingbird” concept on Day 3; Figure 1, 2, which may recruit less activity in temporal pole than an incongruent pairing such as “barking-frog”. For these reasons, the temporal pole may form a crossmodal object code based on pre-existing knowledge, resulting in reduced neural activity (Figure 3d) and pattern similarity towards features associated with learned objects (Figure 4b).” – pg. 18

This work represents a key step in our advancing understanding of object representations in the brain. The experimental design provides a useful template for studying neural change related to the cross-modal association that may prove useful to others in the field. Given the broad variety of open questions and potential alternative analyses, an open dataset from this study would also likely be a considerable contribution to the field.

Author Response

Reviewer #3 (Public Review):

Gavanetto et al. propose an interesting method to identify membrane proteins based on the analysis of single-molecule AFM (smAFM) force-extension traces obtained from native plasma membranes. In the proposed pipeline, the authors use smAFM to non-specifically probe isolated plasma membranes by recording a large number (millions) of force-extension traces. While, as expected, most of them lack any binding or represent spurious events, the authors use an unsupervised clustering algorithm to identify groups of force-extension curves with a similar mechanical pattern, suggesting that each cluster corresponds to a unique protein species that can be fingerprinted by its specific force-extension pattern. By implementing a Bayesian framework, the authors contrast the identified groups with proteomics databases, which provide the most likely proteins that correspond to the identified force-extension clusters. A set of control experiments complements the manuscript to validate the proposed methodology, such as the application of their pipeline using purified samples or overexpressing a specific protein species to enrich its population.

The primary strength of the manuscript is its originality, as it proposes a novel application of smAFM as a protein-detection method that can be applied in native samples. This methodology combines ingredients from conventional mass spectrometry and cryoEM; the contour length released upon extending a protein is a direct measure of its sequence extension (related to its mass), but the force pattern contains insightful information about the protein's structure. In this sense, the authors' proposal is very smart. However, the relationship between protein structure and mechanics is far from straightforward, and here perhaps lies one of the main limitations of the proposed method. This is particularly true for the case of membrane proteins, where we cannot talk about protein unfolding in its classical sense but rather about pullout events which is likely what each peak corresponds to (indeed, the authors speak throughout the paper about unfolding events, which I believe is not the correct term).

We fully agree with the semantics concern of reviewer #3 about the term unfolding. A membrane protein when pulled with the tip of the AFM is pulled out of the membrane (see 2 in the image below) and, simultaneously, the segment that is pulled out unfolds (see 3). To our knowledge, force peaks corresponding to a contour length equal to 2 where not consistently observed or reported (when e.g. a transmembrane alpha helix is out of the membrane but folded).

Since the field evolved with the practice of using the term ‘unfolding’ even for membrane proteins (see for instance (Kessler and Gaub, 2006; Oesterhelt et al., 2000; Yu et al., 2017) and many others), we would prefer to stick with this term.

In the context of membrane proteins the term unfolding therefore refers to at least the tertiary structure of the protein, because it is not clear when and at which timescale the secondary structures really unfolds.

We pointed this out in Line 131 (and following Lines).

Author Response

Reviewer #1 (Public Review):

This is a well performed study to demonstrate the antiviral function and viral antagonism of the dynein activating adapter NINL. The results are clearly presented to support the conclusions.

This reviewer has only one minor suggestion to improve the manuscript.

Add a discussion (1) why the folds of reduction among VSV, SinV and CVB3 were different in the NINL KO cells and (2) why the folds of reduction of VSV in the NINL KO A549 and U-2 OS cells.

Thank you for this suggestion. We have amended the results section to include additional information about these observations and possible explanations for these results.

Reviewer #2 (Public Review):

This manuscript is of interest to readers for host-viral co-evolution. This study has identified a novel human-virus interaction point NINL-viral 3C protease, where NINL is actively evolving upon the selection pressure against viral infect and viral 3Cpro cleavage. This study demonstrates that the viral 3Cpros-mediated cleavage of host NINL disrupts its adaptor function in dynein motor-mediated cargo transportation to the centrosome, and this disruption is both host- and virus-specific. In addition, this paper indicates the role of NINL in the IFN signaling pathway. Data shown in this manuscript support the major claims.

In this paper, the authors have identified a novel host-viral interaction, where viral 3C proteases (3Cpro) cleave at specific sites on a host activating adaptor of dynein intracellular transportation machinery, ninein-like protein (NINL or NLP in short) and inhibit its role in the antiviral innate immune response.

The authors firstly found that, unlike other activating adaptors of dynein intracellular transportation machinery, NINL (or NLP) is rapidly evolving. Thus, the authors hypothesized that this rapid evolution of NINL was caused by its interaction with viral infection. The authors found that viruses replicated higher in NINL knock-out (KO) cells than in wild-type (WT) cells and the replication level was not attenuated upon IFNa treatment in NINL KO cells, unlike in WT cells. Next, the authors investigated the role of NINL in type I IFN-mediated immune response and found that the induction of Janus kinase/signal transducer and activation of transcription (JAK/STAT) genes were attenuated in NINL KO cells upon IFNa treatment. The author further showed that the reduction of replication IFNa sensitive Vaccinia virus mutant upon IFNa treatment was decreased in NINL KO A549 cells compared to WT cells. The authors further showed that the virus antagonized NINL function by cleaving it with viral 3Cpro at its specific cleavage sites. NINL-peroxisome ligation-based cargo trafficking visualization assay showed that the redistribution of immobile membrane-bound peroxisome was disrupted by cleavage of NINL or viral infection.

This paper has revealed a novel host-virus interaction, and an antiviral function of a rapidly evolving activating adaptor of dynein intracellular transportation machinery, NINL. The major conclusions of this paper are well supported by data, but several aspects can be improved.

1) It would be necessary to include a couple of other pathways involved in innate immune response besides JAK/STAT pathway.

We are very interested in this question as well. Our RNAseq data (Supplementary file 4 and Figure 3 – Figure supplement 4) suggest that there are several transcriptional changes that result from NINL KO. Our goal in this manuscript was to focus on IFN signaling in order to understand this specific effect of NINL KO since it might have wide-ranging consequences on viral replication. While we agree that broadening our studies to other signaling pathways, including other pathways involved in innate immune response, is a good idea, we feel that those experiments would take longer than two months to perform and therefore fall outside of the scope of this paper.

2) The in-cell cleavages of NINL by viral 3Cpros were well demonstrated and supported by data of high quality. A direct biochemical demonstration of the cleavage is needed with purified proteins.

We agree with the reviewer that a direct biochemical cleavage assay would further demonstrate that viral 3Cpros cleave NINL specifically. However, our attempts to purify full-length NINL have been unsuccessful due to solubility issues (see example gel below), which is not surprising given that NINL is a >150 kDa human protein that has multiple surfaces that bind to other human proteins. As such, we focused our efforts on in-cell cleavage assays using specificity controls for cleavage. Specifically, we used catalytically inactive CVB3 3Cpro to show a dependence on protease catalytic activity and a variety of NINL constructs in which the glutamine in the P1 position is replaced by an arginine to show site specificity of cleavage. Notably, the cleavage sites in NINL that we mapped using this mutagenesis were predicted bioinformatically from known sites of 3Cpro cleavage in viral polyproteins, further indicating that cleavage is 3Cpro-dependent. We believe these results thus demonstrate that cleavage of NINL is dependent on viral protease activity and occurs in a sequence-specific manner. In light of the difficulty of purifying full-length NINL that would make biochemical experiments very challenging and likely take longer than two months to perform, we believe that our in cell data should be sufficient to demonstrate activity-dependent site-specific cleavage of NINL by viral 3Cpros.

Sypro stained SDS-PAGE gel showing supernatant (S) and insoluble pellet (P) fractions across multiple purifications with altered buffer conditions.

3) The author used different cell types in different assays. Explain the rationale with a sentence for each assay.

Throughout this work, we choose to use a variety of cell lines for specific purposes. A549 cells were chosen as our main cell line as they are widely used in virology, are susceptible to the viruses we used, are responsive to interferon, and express both NINL and our control NIN at moderate levels. In the case of our virology and ISG expression data, we performed the same experiments with NINL KOs in other cell lines confirm that the phenotypes we observed in A549 cells could be attributed to the absence of NINL rather than off-target CRISPR perturbations or cell-line specific effects. All cleavage experiments were performed in HEK293T for their ease of transfection and protein expression. The inducible peroxisome trafficking assays were performed in U-2 OS cells as their morphology is ideal for observing the spatial organization of peroxisomes via confocal microscopy, and based on the fact that we had recapitulated the virology results and ISG expression results in those cells. At the suggestion of the reviewer, we have amended the text to include rationales where appropriate.

4) While cell-based assays well support the conclusions in this paper, further demonstration in vivo would be helpful to provide an implication on the pathogenicity impact of NINL.

We agree. However, we believe that examining the impact of the loss of or antagonism of NINL on the pathogenesis of infectious diseases in an in vivo model is outside the scope of this study.

In summary, this manuscript contributes to a novel antiviral target. In addition, it is important to understand the host-virus co-evolution. The use of the evolution signatures to identify the "conflict point" between host and virus is novel.

Author Response

Reviewer #1 (Public Review):

Cui and colleagues have performed a longitudinal analysis of blood cell counts in a cohort of ALS patients. The major findings include increases in neutrophils and monocytes that negatively correlated with ALSFRS-R score, but not disease progression rate. Increases in NK and central memory TH2 T cells correlated with a lower risk of death, while increased CD4 CD45RA effector memory and CD8 T cells were correlated with a higher risk of death.

Strengths of the study include the sample size and effort to broadly include data.

Thank you for the positive comment.

Limitations of the study include indication bias, as the authors acknowledge, because the timing of the blood draws is not predefined. The specific review for possibility of infection does not, in this reviewer's opinion, sufficiently address this potential for bias. Also concerning is the fact that half the subjects have only a single measurement, and how well the findings generalize to more or late measurements is not clear. Similarly, the number of later measurements driving some of the main findings is much lower, further raising concern about the potential bias. Given these issues, one really would want to see disease controls, and how the different cell counts change in another disease. Finally, there is not discussion about how or whether treatments, or changes in treatment, could influence observed counts.

We agree with the reviewer regarding indication bias and that is precisely why we performed the sensitivity analyses including 1) restricting the analysis to the first cell measure of each patient and 2) excluding cell measures with signs of ongoing infection at the time of blood draw. Reassuringly, both analyses provided rather similar results as those of the main analysis. We also agree with the reviewer regarding the varying numbers of measurements between patients. This is an unavoidable challenge to any longitudinal study of ALS patients, primarily due to the high mortality rate of this patient group. We have now added this limitation to the discussion:

“First, the main cohort was heterogeneous in terms of the numbers of cell measurements and the time intervals between measurements, as the timing of blood sampling was not predefined. Indication bias due to, for example, ongoing infections might therefore be a concern. The sensitivity analysis excluding all samples taken at the time of infections provided however rather similar results. Further, the longitudinal analysis of cell counts should be interpreted with caution because not all patients contributed repeated cell measurements. This is however an unavoidable problem for any longitudinal study of ALS patients, given the high mortality rate of this patient group. Regardless, when focusing on the first cell measures, we obtained similar results as in the main analysis.”

We further agree with the reviewer regarding the use of disease control. We have access to a cohort of patients with relapsing-remitting MS (RRMS) treated by rituximab (n=34), who had been measured with all the studied cell populations at the start of treatment and the 6-month follow-up. These cell measurements were processed during the same time-period using the identical setup at Karolinska University Hospital as the ones studied in the present study. In brief, we found different longitudinal changes of the studied immune cell populations between RRMS patients and ALS patients (please see below figure for details). The declining B cells are most likely due to rituximab treatment.

Given the largely different disease mechanisms, phenotypes, and treatments between RRMS and ALS, we are not confident that RRMS would be a good disease control for the present study. We are certainly willing to reconsider our position if the reviewer and editors would disagree with us. We have regardless now added discussion about this in the manuscript:

“It would therefore be interesting to compare ALS with other diseases, especially other neurodegenerative diseases, regarding the studied cell counts, in terms of both their longitudinal trajectories during disease course and their prognostic values in predicting patient outcome.”

Finally, we agree that it is interesting to consider treatment in the analysis of cell counts. Among the ALS patients of the main cohort, majority (89.6%) were treated with Riluzole. We have now added a supplementary figure to demonstrate the leukocyte counts before and after start of Riluzole treatment. The corresponding analysis is however not possible for the FlowC cohort as majority of the patients started Riluzole treatment around time of diagnosis and almost all measurements were taken after Riluzole treatment. Th17 of CD4+ CM cells CD4+ EMRA cells CD8+ T cells Naïve CD8+ T cells CD8+ EM cells CD8+ CM cells CD8+ EMRA cells CD4+ HLA-DR+ CD38- cells CD4+ HLA-DR+ CD38+ cells CD8+ HLA-DR+ CD38- cells CD8+ HLA-DR+ CD38+ cells.

We have now added this analysis to Methods and Results, including a new Figure 1—figure supplement 2.

“To evaluate whether ALS treatment would influence the cell counts, we further visualized the temporal patterns of differential leukocyte counts before and after Riluzole treatment.”

“The levels of leukocytes, neutrophils and monocytes increased, whereas the levels of lymphocytes decreased, after Riluzole treatment, compared with before such treatment (Figure 1—figure supplement 2).”

Reviewer #2 (Public Review):

Cui et al. investigated the correlation of immune profiles in ALS patients to functional status (by ALSFRS-R score), disease progression (rate of ALSFRS-R decline) and/or risk of death (or invasive ventilation use). The study longitudinally assessed basic immune profiles from a large cohort of ALS patients (n=288). Additionally, they deeply immunophenotyped a subset of ALS patients (n=92) to examine immune cell subtypes on ALS status, progression rate, and survival. The longitudinal design, deep immunophenotyping, and large cohort are significant strengths. Using various statistical models, the authors found leukocyte, neutrophil, and monocyte counts increased gradually over time as ALSFRS-R score declined. Within lymphocyte subpopulations, increasing natural killer cells and Th2-diffrentiated CD4+ central memory T cell counts correlated with a lower risk of death. Increasing CD4+ effector memory cells re-expressing CD45RA T cell and CD8+ T cell levels associated with a higher risk of death. These findings have broad implications for ALS pathogenesis and the development of immune-based ALS therapies tailored to specific immune cell populations.

Thank you for the very positive comments.

Author Response:

Reviewer #1:

In this manuscript Hill et al, analyze immune responses to vaccination of adults with the seasonal influenza vaccine. They perform a detailed analysis of the hemagglutinin-specific binding antibody responses against several different strains of influenza, and antigen-specific CD4+ T cells/T follicular cells, and cytokines in the plasma. Their analysis reveals that: (i) tetramer positive, HA-specific T follicular cells induced 7 days post vaccination correlate with the binding Ab response measured 42 days later; (ii) the HA-specific T fh have a diverse TCR repertoire; (iii) Impaired differentiation of HA-specific T fh in the elderly; and (iv) identification of an "inflammatory" gene signature within T fh in the elderly, which is associated with the impaired development of HA-specific Tfh.

The paper addresses a topic of considerable interest in the fields of human immunology and vaccinology. In general the experiments appear well performed, and support the conclusions. However, the following points should be addressed to enhance the clarity of the paper, and add support to the key conclusions drawn.

We thank the reviewer for their supportive evaluation of the manuscript, and have provided the details of how we have addressed each the points raised below.

1) Abstract: "(cTfh) cells are the best predictor of high titre antibody responses.." Since the authors have not done any blind prediction using machine learning tools with independent cohort, the sentence should be rephrased thus: "cTfh) cells are were associated with high titre antibody responses."

We agree that this phrasing better reflects the presented data. The sentence in the abstract (page 2) now reads “we show that formation of circulating T follicular helper (cTfh) cells was associated with high titre antibody responses.”

2) Figure 1A: Please indicate the age range of the subjects.

Figure 1 has been updated to include the age range of the subjects.

3) Almost all the data in the paper shows binding Ab titers. Yet, typically HAI titers of MN titers are used to assess Ab responses to influenza. Fig 1C shows HAI titers against the H1N1 Cal 09 strain. Can the authors show HAI titers for Cal 09 and the other A and B strains contained in the 2 vaccine cohorts? Do such HAI titers correlate with the tetramer positive cells, similar to the correlations show in Fig 2e.

In this manuscript we have deliberately focussed on the immune response to the H1N1 Cal09 strain, as it is the only influenza strain in the vaccine common to both cohorts. The HAI titre for this strain is now shown as supplementary figure 4. In addition, the class II tetramers were specifically selected to recognise unique epitopes in the Cal 09 strain (J. Yang, {..} W. W. Kwok, CD4+ T cells recognize unique and conserved 2009 H1N1 influenza hemagglutinin epitopes after natural infection and vaccination. Int Immunol 25, 447-457, 2013) because of this we do not think it is appropriate to correlate HAI titres for the non-Cal 09 strains with tetramer positive cells. We agree that showing the correlation of cTfh and other immune parameters with the HAI titres for Cal 09 is important and have included this as supplementary figure 7. The new data and text are presented below:

Figure 1-figure supplement 4: HAI responses before and after vaccination A) Log2 HAI titres at baseline (d0), d7 and d42 for cohort 1 (n=16) and B) cohort 2 (n = 21). C) Correlation between HAI and A.Cali09 IgG as measured by Luminex assay for cohort 1 and 2 combined. p-values determined using paired Wilcoxon signed rank-test, and Pearson’s correlation.

Text changes. Page 4. “The increase in anti-HA antibody titre was coupled with an increase in hemagglutination inhibitory antibodies to A.Cali09, the one influenza A strain contained in the TIVs that was shared across the two cohorts and showed a positive correlation with the A.Cali09 IgG titres measured by Luminex assay (Fig. 1C, Figure 1-figure supplement 4).”

Figure 2-figure supplement 1: Correlations between HAI assay titres and selected immune parameters. Correlation between vaccine-induced A.Cali09 HAI titres at d42 with selected immune parameters in both Cohort 1 and Cohort 2 (n=37). Dot color corresponds to the cohort (black = Cohort 1, grey = Cohort 2). Coefficient (Rho) and p-value determined using Spearman’s correlation, and line represents linear regression fit.

Results text Changes: Page 5. “Similar trends were seen when these immune parameters were correlated to HAI titres against A/Cali09 (Fig Figure 2-figure supplement 1).”

4) Fig 2d to i: what % of all bulk activated Tfh at day 7 are tetramer positive? The tetramer positive T cells constitute roughly 0.094% of all CD4 T cells (Fig 2d), of which 1/3rd are CXCR5+, PD1+ (i.e. ~0.03% of CD4 T cells). What fraction of all activated Tfh is this subset of tetramer positive cells? Presumably, there will also be Tfh generated against other viral proteins in the vaccine, and these will constitute a significant fraction of all activated Tfh.

This is an important point, as the tetramers only recognise one peptide epitope of the Cal.09 HA protein, so there will be many other influenza reactive CD4+ T cells that are responding to other Cal 09 epitopes as well as other proteins in the vaccine. The analysis suggested by the reviewer shows that the frequency of Tet+ cells amongst bulk cTfh cells ranges from 0.14%-1.52% in cohort 1, and from 0.022-2.7% in cohort 2. These data have been included as Figure Figure 1-figure supplement 6C, D in the revised manuscript. In addition, Tet+ cells as a percentage of bulk cTfh cells were reduced in older people compared to younger adults. This data has been included in Figure 5-figure supplement 1C in the revised manuscript.

Figure 1-figure supplement 6: Percentage of cTfh cells that are Tet+ and CXCR3 and CCR6 expression on HA-specific CD4+ T cells. A) Representative flow cytometry gating strategy for CXCR5+PD-1+ cTfh cells on CD4+CD45RA- T cells, and the proportion of HA-specific Tet+ cells within the CXCR5+PD-1+ cTfh cell gate. B) Percentage Tet+ cells within the CXCR5+PD-1+ cTfh cell population. Within-cohort age group differences were determined using the Mann-Whitney U test.

Results text, page 4: These antigen-specific T cells had upregulated ICOS after immunisation, indicating that they have been activated by vaccination (Fig. 1F, G). In addition, a median of one third of HA-specific T cells upregulated the Tfh markers CXCR5 and PD1 on d7 after immunisation (Fig. 1H, I). The tetramer binding cells represented between 0.022-2.7% of the total CXCR5+PD-1+ bulk population (Fig Figure 1-figure supplement 6A, B).

Figure 5-figure supplement 1C: Age-related differences in cytokines and HA-specific CD4+ T cell parameters. C) Percentage Tet+ cells within the CXCR5+PD-1+ cTfh cell population. Within-cohort age group differences were determined using the Mann-Whitney U test.

Results text, page 8: Across both cohorts, the only CD4+ T cell parameters consistently reduced in older individuals at d7 were the frequency of polyclonal cTfh cells and HA-specific Tet+ cTfh cells, with the strongest effect within the antigen-specific cTfh cell compartment (Fig. 5H-J, Figure 5-figure supplement 1C).

Reviewer #2:

Hill and colleagues present a comprehensive dataset describing the recall and expansion of HA-specific cTFH cells following influenza immunisation in two cohorts. Using class II tetramers, IgG titres against a large panel of HA antigens, and quantification of plasma cytokines, they find that activated and HA-specific cTFH cells were a strong predictor of the IgG response against the vaccine after 6 weeks. Using RNAseq and TCR clonotype analysis, they find that, in 10/15 individuals, the HA-specific cTFH response at day 7 post-vaccination is recalled from the available CD4 T cell memory pool present prior to vaccination. Post-vaccination HA-specific cTFH cells exhibited a transcriptional profile consistent with lymph node-derived GC TFH, as well as evidence of downregulation of IL-2 signaling pathways relative to pre-vaccine CD4 memory cells.

The authors then apply these findings to a comparison of vaccine immunogenicity between younger (18-36) and older (>65) adults. As expected, they found lower levels of vaccine-specific IgG responses among the older cohort. Analysis of HA-specific T cell responses indicated that tet+ cTFH fail to properly develop in the older cohort following vaccination. Further analysis suggests that development of HA-specific cTFH in older individuals is not caused by a lack of TCR diversity, but is associated with higher expression of inflammation-associated transcripts in tet+ cTFH.

Overall this is an impressive study that provides clarity around the recall of HA-specific CD4 T cell memory, and the burst of HA-specific cTFH cells observed 7 days post-vaccination. The association between defective cTFH recall and lower IgG titres post-vaccination in older individuals provides new targets for improving influenza vaccine efficacy in this age group. However, as currently presented, the model of impaired cTFH differentiation in the older cohort and the link to inflammation is somewhat unclear. There are several issues that could be clarified to improve the manuscript in its current form:

We thank the reviewer for their supportive and comprehensive summary of our work. We agree that the link between impaired inflammation and cTfh differentiation is correlative, we have added new data to address this, including mechanistic data to support chronic IL-2 signalling as antagonistic to cTfh development, as well as providing new analyses to address the other points raised.

1) It is somewhat unclear the extent to which the reduction in HA-specific cTFH in the older cohort is also related to an overall reduction in T cell expansion - cohort 1 shows a significant reduction in total tet+ CD4 T cells post-vaccination as well as in the cTFH compartment, and while this difference may not reach statistical significance, a similar trend is shown for cohort 2.

We agree that a possible interpretation is a global failure in T cell expansion in the older individuals. To determine whether there is a relationship between the degree of Tet+ CD4+ T cell expansion and cTfh cell differentiation with age, we performed correlation analyses. There is no correlation between the expansion of Tet+ cells and the frequency of cTfh cells formed seven days after immunisation in either age group. This suggests that the impaired cTfh cell differentiation in older persons is most likely caused by factors other than the capacity of CD4+ T cells to expand after vaccination. These data have been added as Figure 5-figure supplement 1D, and included in the results text on page 8.

Figure 5-figure supplement 1D: Age-related differences in cytokines and HA-specific CD4+ T cell parameters. D) Correlation between Tet+ cells (d7-d0, % of CD4+) and cTfh (d7-d0, % of TET+) in both cohorts for each age-group (18- 36 y.o n=37, 65+ y.o. n= 39). Dot color corresponds to the cohort (black = Cohort 1, grey = Cohort 2). Coefficient (Rho) and p-value determined using Spearman’s correlation, and line represents linear regression fit.

Text changes, Page 8: There was no consistent difference in the total d7 Tet+ HA-specific T cell population with age for both cohorts (Fig. 5H) and we observed no age-related correlation between the ability of an individual to differentiate Tet+ cells into a cTfh cell and the overall expansion of Tet+ HA-specific T cell population (Figure 5-figure supplement 1D). Thus, our data suggests that the poor vaccine antibody responses in older individuals is impacted by impaired cTfh cell differentiation (Fig. 5J) rather than size of the vaccine-specific CD4+ T cell pool.

2) Transcriptomic analysis indicates that HA-specific cTFH in the older cohort show impaired downregulation of inflammation, TNF and IL-2-related signaling pathways. The authors therefore conclude that excess inflammation can limit the response to vaccination. In its current presentation, the data does not necessarily support this conclusion. While it is clear that downregulation of TNF and IL-2 signalling pathways occur during cTFH/TFH differentiation, there is no evidence presented to support the idea that (a) vaccination results in increased pro-inflammatory cytokine production in lymphoid organs in older individuals or that (b) these pro-inflammatory cytokines actively promote CXCR5-, rather than cTFH, differentiation of existing memory T cells.

We agree with the reviewer that the data presented in figure 7 are correlative, rather than causative. Unfortunately, we do not have access to secondary lymphoid tissues from younger and older people after vaccination to test point (a) above. In order to test the hypothesis that increased inflammatory cytokine production in lymphoid organs limits Tfh cell differentiation we have used Il2cre/+; Rosa26stop-flox-Il2/+ transgenic mice. In this mouse model, IL-2-dependent cre- recombinase activity facilitates the expression of low levels of IL-2 in cells that have previously expressed IL-2. This creates a scenario in which cells that physiologically express IL-2 cannot turn its expression off therefore increasing expression IL-2 after antigenic stimulation (mice reported in Whyte et al., bioRxiv, 2020, doi: https://doi.org/10.1101/2020.12.18.423431).

Twelve days after influenza A infection, Il2cre/+; Rosa26stop-flox-Il2/+ transgenic mice have fewer Tfh cells in the draining mediastinal lymph node and in the spleen (Fig. 8A-C), this is accompanied by a reduction in the magnitude of the GC B cell response (Fig. 8D-E). These data provide a proof of concept that sustained IL-2 production limit the formation of Tfh cells, consistent with the negative correlation of an IL-2 signalling gene signature and cTfh cell formation in humans (Figure 7). These new data support the conclusion that excess IL-2 signalling can limit the Tfh cell response. These data are presented in Figure 8, and are discussed on page 12 in the results, and pages 12-13 in the discussion.

Figure 8: Increased IL-2 production impairs Tfh cell formation and the germinal centre response. Assessment of the Tfh cell and germinal centre response in Il2cre/+; Rosa26stop-flox-Il2/+ transgenic mice that do not switch off IL-2 production, and Il2cre/+; Rosa26+/+ control mice 12 days after influenza A infection. Flow cytometric contour plots (A) and quantification of the percentage of CXCR5highPD-1highFoxp3-CD4+ Tfh cells in the mediastinal lymph node (B) and spleen (C). Flow cytometric contour plots (D) and quantification of the percentage of Bcl6+Ki67+B220+ germinal centre B cells in the mediastinal lymph node (E) and spleen (F). The height of the bars indicates the median, each symbol represents one mouse, data are pooled from two independent experiments. P-values calculated between genotype-groups by Mann Whitney U test.

Results text, page 12: Sustained IL-2 production inhibits Tfh cell frequency and the germinal centre response. To test the hypothesis that cytokine signalling needs to be curtailed to facilitate Tfh cell differentiation turned to a genetically modified mouse model in which cells that have initiated IL-2 production cannot switch it off, Il2cre/+; Rosa26stop-flox-Il2/+ mice (37). Twelve days after influenza infection Il2cre/+; Rosa26stop-flox-Il2/+ mice have fewer Tfh cells in the draining lymph node and spleen (Fig. 8A-C), which is associated with a reduced frequency of germinal center B cells (Fig. 8D-F). This provides a proof of concept that proinflammatory cytokine production needs to be limited to enable full Tfh cell differentiation in secondary lymphoid organs.

Discussion text, pages 12, 13: These enhanced inflammatory signatures associated with poor antibody titre in an independent cohort of influenza vaccinees. The dampening of Tfh cell formation by enhanced cytokine production was confirmed by the use of genetically modified mice where IL-2 production is restricted to the appropriate anatomical and cellular compartments, but once initiated cannot be inactivated. Together, this suggests that formation of antigen-specific Tfh cells is essential for high titre antibody responses, and that excessive inflammatory factors can contribute to poor cTfh cell responses.

Author Response

Reviewer #1 (Public Review):

In the article "Neuroendocrinology of the lung revealed by single cell RNA sequencing", Kuo et. al. described various aspects of pulmonary neuroendocrine cells (PNECs) including the scRNA-seq profile of one human lung carcinoid sample. Overall, although this manuscript does not have any specific storyline, it is informative and would be an asset for researchers exploring various new roles of PNECs.

Thank you for appreciating the significance of the data presented. Our storyline focuses on the newly uncovered molecular diversity of PNECs and the extraordinary repertoire of peptidergic signals they express and cell types these signals can directly target in (and outside) the lung, in mice and human, and in health and disease (human carcinoid tumor).

Major comments:

The major concern about the work is most results are preliminary, and at a descriptive level, conclusions or sub-conclusions are derived from scRNA-seq analysis only, lacking in-depth functional analysis and validation in other methods or systems. There are many open-end results that have been predicted by the authors based on their scRNA-seq data analysis without functional validation. In order to give them a constructive roadmap, it would be better to investigate literature and put them in a potential or probable hypothesis by citing the available literature. This should be done in each section of the result part. The paper lacks a main theme or specific biology question to address. In addition, the description about the human lung carcinoid by scRNA-seq is somehow disconnected from the main study line. Also, these results are derived from the study on only one single patient, lacking statistical power.

We agree that much of the data and analysis presented in the paper is descriptive and hypothesis-generating for PNECs, however we do not consider it preliminary. We focused on validating two key conclusions from the scRNA-seq analysis: PNECs are extraordinarily diverse molecularly (as validated by multiplex in situ hybridization and immunostaining) and they express many different combinations of peptidergic signals (and appear to package them in separate vesicles). From the lung expression profiles of the cognate receptors, we also predicted the direct lung targets of the dozens of new PNEC peptidergic signals we uncovered, and validated the cell target (PSN4, a recently identified subtype of pulmonary sensory neuron) of one of the newly identified PNEC signals (the classic hormone angiotensin) by confirming expression of the cognate receptor gene in PSN4 neurons that innervate PNECs and showing that the hormone can directly activate PSN4 neurons. The characterized human carcinoid provided evidence that during tumorigenesis, the amplified PNECs retain a memory (albeit imperfect) of the molecular subtype of PNEC from which they originated. As suggested by the Reviewer, we have provided more background in Results by adding additional citations from the literature to clarify the rationale for each analysis and what was known prior to the analysis. We feel that our paper provides a broad foundation for exploring the diversity and signaling functions of PNECs, and although each molecular type of PNEC and new PNEC peptidergic signal we uncovered and potential target cell in (and outside) the lung warrants follow up (as do the sensory and other properties of PNECs we inferred from their expression profiles), such studies will require the effort of many individuals in many labs studying both normal and disease physiology in mouse and human, and exploiting the data, hypotheses, approaches, and framework we provide.

Reviewer #2 (Public Review):

Pulmonary neuroendocrine cells (PNECs) are known to monitor oxygen levels in the airway and can serve as stem cells that repair the lung epithelium after injury. Due to their rarity, however, their functions are still poorly understood. To identify potential sensory functions of PNECs, the authors have used single-cell RNA-sequencing (scRNA-seq) to profile hundreds of mouse and human PNECs. They report that PNECs express over 40 distinct peptidergic genes, and over 150 distinct combinations of these genes can be detected. Receptors for these neuropeptides and peptide hormones are expressed in a wide range of lung cell types, suggesting that PNECs may have mechanical, thermal, acid, and oxygen sensory roles, among others. However, since some of these cognate receptors are not expressed in the lung, PNECs may also have systemic endocrine functions. Although these data are largely descriptive, the results represent a significant resource for understanding the potential roles of PNECs in normal biology as well as in pulmonary diseases and cancer and are likely to be relevant for understanding neuroendocrine cells in other tissue contexts.

However, there are several aspects of the data analysis that are unclear and require clarification, most notably the definition of a neuroendocrine cell (points #1 and #2 below).

1) Figure S1 shows the sorting strategy used for isolation of putative PNECs from Ascl1CreER/+; Rosa26ZsGreen/+ mice, and distinguishes neuroendocrine cells defined as ZsGreen+ EpCAM+ and "neural" cells defined as ZsGreen+ EpCAM-; the figure legend also refers to the ZsGreen+ EpCAM- cells as "control" cells. However, the table shown in panel D indicates that the NE population combines 112 ZsGreen+ EpCAM+ cells together with 64 ZsGreen+ EpCAM- cells to generate the 176 cells used for subsequent analyses. Why are these ZsGreen+ EpCAM- cells initially labeled as neural or control, but are then defined as neuroendocrine? If these do not express an epithelial marker, can they be rigorously considered as neuroendocrine?

As explained above in the response to Essential Revision point 1, we define pulmonary neuroendocrine cells (PNECs) throughout the paper by their transcriptomic clustering and signatures, which includes the dozens of newly identified PNEC markers as well as the few extant marker genes available before this study (listed in Table S2). The confusion here arises from the two previously known markers (Ascl1 lineage marker ZsGreen, EpCAM) we used for flow sorting to enrich for these rare cells for transcriptomic profiling (Fig. S1). Although most of the cells with PNEC transcriptomic profiles were from the ZsGreenhi EpCAMhi sorted population (as expected), some were from the ZsGreenhi EpCAMlo sorted population. The latter resulted from the high EpCAM gating threshold we used during flow sorting, which excluded some PNECs with intermediate levels of surface EpCAM. Indeed, nearly all PNECs (> 95%) expressed EpCAM by scRNAseq, and there was no difference in EpCAM transcript levels or transcriptomic clustering of PNECs that were from the ZsGreenhi EpCAMhi vs. ZsGreenhi EpCAMlo sorted populations, as we now show in the new panels (C', C'') added to Fig S1C. This point is now clarified in the legend to Fig. S1C, and it nicely demonstrates that transcriptomic profiling is a more robust method of identifying PNECs than flow sorting based on two classical markers.

2) Similarly, in the human scRNA-seq analysis, how were PNECs defined? The methods description states that these cells were identified by their expression of CALCA and ASCL1, but does not indicate whether they also expressed epithelial markers.

Human PNECs were identified in the single cell transcriptomic analysis by the same strategy described above for mouse PNECs: by their transcriptomic clustering and signatures, which includes the dozens of newly identified PNEC markers as well as the few extant marker genes available before this study (listed in Table S2). In addition to expression of classic and new markers, the human PNEC cluster defined by scRNA-seq indeed showed the expected expressed of epithelial markers (e.g, EPCAM, see dotplot below), like other epithelial cells.

3) The presentation of sensitivity and specificity in Figure 1 is confusing and potentially misleading. According to Figure 1B, Psck1 and Nov are two of the top-ranked differentially expressed genes in PNECs with respect to both sensitivity and specificity. However, the specificity of these two genes appears to be lower than that of Scg5, Chgb, and several other genes, as suggested in Figure 1C and Figure S1E. In contrast, Chgb appears to have higher specificity and sensitivity than Psck1 in Figures 1C and E but is not shown in the list of markers in Figure 1B.

As explained above in the response to Essential Revision point 2, because different marker features are important for different applications, we have provided several different graphical formats (Figs. 1B,C, Fig. S1E) and a table (Table S1) to aid in selection of the optimal markers for each application. Fig. 1B shows the most sensitive and specific PNEC markers identified by ratio of the natural logs of the average expression of the marker in PNECs vs. non-PNEC epithelial cells (Table S1), and we have added a two-dimensional plot of this sensitivity and specificity for a large set of PNEC markers (new panel E of Fig. S1). The violin plots in Fig. 1C allow visual comparison of expression of selected markers across PNECs and 40 other lung cell types including non-epithelial cells (from our extensive mouse lung atlas in Travaglini, Nabhan et al, Nature 2020). Pcsk1 and Nov score high in the analysis of Fig. 1B because they are highly sensitive and specific markers within the pulmonary epithelium, and they are also valuable markers because they are highly expressed in PNECs. However, they appear slightly less specific in the violon plots of Fig. 1C (Pcsk1) and Fig. S1F (Nov) because of expression (though at much lower levels) in individual lung cell types outside the epithelium: Pcsk1 is expressed also at low levels in some Alox5+ lymphocytes, and Nov is expressed at low levels in some smooth muscle cells. Chgb is a new PNEC marker that did not make the cutoff for the list in Fig. 1B because it is expressed in a slightly higher percentage of non-PNEC epithelial cells than the markers shown, which ranked slightly above it by this metric (see Table S1).

4) The expression of serotonin biosynthetic genes in mouse versus human PNECs deserves some comment. The authors fail to detect the expression of Tph1 and Tph2 in any of the mouse PNECs analyzed, but TPH1 is expressed in 76% of the human PNECs (Table S8). Is it possible that Tph1 and Tph2 are not detected in the mouse scRNA-seq data due to gene drop-out? If serotonin signaling by mouse PNECs is due to protein reuptake, as implied on p. 5, is there a discrepancy between serotonin expression as detected by smFISH versus immunostaining?

It is always possible that the failure to detect expression of Tph1 and Tph2 in the mouse scRNA-seq dataset is due to technical dropout, however when we analyzed this in our other mouse PNEC scRNA-seq dataset obtained using a microfluidic platform and also deeply-sequenced (Ouadah et al, Cell 2019), we found similar values as in the previously analyzed dataset: no Tph2 expression was detected and only 3% (3 of 92) of PNECs had detected Tph1 expression, whereas 24% (22 of 92) had detected expression of serotonin re-uptake transporter Slc6a4. Because our mouse and human scRNA-seq datasets were prepared similarly and sequenced to a similar depth (105 to 106 reads/cell), the difference observed in Tph1/TPH1 expression between mouse (0-3% PNECs) and human (76% PNECs) is more likely a true biological difference. We also analyzed serotonin levels in mouse PNECs by immunohistochemistry (not shown) and detected serotonin in nearly all (~90%) embryonic PNECs but only ~10% of adult PNECs. Systematic follow up studies will be necessary to resolve the mechanism of serotonin biogenesis and uptake in PNECs, and the potential stage and species-specific differences in these processes suggested by this initial data.

5) The smFISH and immunostaining analyses are often presented without any indication of the number of independent replicate samples analyzed (e.g., Figure 2B, Figure 3F, G).

The number of samples analyzed have been added (the values for Fig. 2B are given in legend to Fig. 2C, the quantification of Fig. 2B).

6) It would be helpful to provide a statistical analysis of the similarities and differences shown in the graphs in Figures 1E and G.

We added a statistical analysis (Fisher's exact test, two-sided) of Fig. 1E comparing expression of each examined gene in the two scRNA-seq datasets (Table S4). We added a similar statistical analysis of Fig. 1G comparing the expression values of each examined gene by scRNA-seq vs smFISH (see Fig. 1G legend).

Author Responses

Reviewer #1 (Public Review):

This study uses a nice longitudinal dataset and performs relatively thorough methodological comparisons. I also appreciate the systematic literature review presented in the introduction. The discussion of confound control is interesting and it is great that a leave-one-site-out test was included. However, the prediction accuracy drops in these important leave-one-site-out analyses, which should be assessed and discussed further.

Furthermore, I think there is a missed opportunity to test longitudinal prediction using only pre-onset individuals to gain clearer causal insights. Please find specific comments below, approximately in order of importance.

We thank the reviewers for their positive remarks and for providing important suggestions to improve the analysis. Please see our detailed comments below.

1) The leave-one-site-out results fail to achieve significant prediction accuracy for any of the phenotypes. This reveals a lack of cross-site generalizability of all results in this work. The authors discuss that this variance could be caused by distributed sample sizes across sites resulting in uneven folds or site-specific variance. It should be possible to test these hypotheses by looking at the relative performance across CV folds. The site-specific variance hypothesis may be likely because for the other results confounds are addressed using oversampling (i.e., sampling with replacement) which creates a large sample with lower variance than a random sample of the same size. This is an important null finding that may have important implications, so I do not think that it is cause for rejection. However, it is a key element of this paper and I think it should be assessed further and discussed more widely in the abstract and conclusion.

We thank the reviewer for raising this point and providing specific suggestions. As mentioned by the reviewer, the leave-one-site-out results showed high-variance across sites, that is, across cross validation (CV) folds. Therefore, as suggested by the reviewer, we further investigated the source of this variance by observing how the model accuracies correlates with each site and its sample sizes, ratio of AAM-to-controls, and the sex distribution in each site. We ranked the sites from low to high accuracy and observed different performance metrics such as sensitivity and specificity:

As shown, the models performed close-to-chance for sites ‘Dublin’, ‘Paris’ and ‘Berlin’ (<60% mean balanced accuracy) in the leave-one-site-out experiment, across all time-points and metrics. Notably, the order of the performance at each site does not correspond to the sample sizes (please refer to the ‘counts’ column in the above figure). It also does not correspond to the ratio of AAM-to-controls, or to the sex distribution.

To further investigate this, we performed another additional leave-one-site-out experiment with all 8 sites. Here, we repeated the ML (Machine Learning) exploration by using the entire data, including the data from the Nottingham site that was kept aside as the holdout. Since there are 8 sites now, we used a 8-fold cross validation and observed how the model accuracy varied across each site:

The results were comparable to the original leave-one-site-out experiment. Along with ‘Dublin’ and Berlin’, the models additionally performed poorly on the ‘Nottingham’ site. Results on ‘London’ and ‘Paris’ also fell below 60% mean balanced accuracy.

Finally, we compared the above two results to the main experiment from the paper where the test samples were randomly sampled across all sites. The performance on test subjects from each site was compared:

As seen, the models struggled with subjects from ‘Dublin’ followed by ‘Nottingham’ ‘London’ and ‘Berlin’ respectively, and performed well on subjects from ‘Dresden’, ‘Mannheim’, ‘Hamburg’ and ‘Paris’.

Across all the three results discussed above, the models consistently struggle to generalize to subjects particularly from ‘Dublin’ and ‘Nottingham’. As already pointed out by the reviewer, the variance in the main experiment in the manuscript is lower because of the random sampling of the test set across all sites. Since these results have important implications, we have included them in the manuscript and also provided these figures in the Appendix.

2) The authors state that "83.3% of subjects reported having no or just one binge drinking experience until age 14". To gain clearer insights into the causality, I recommend repeating the MRIage14 → AAMage22 prediction using only these 83% of subjects.

We thank the reviewer for this valuable comment. As suggested by the reviewer, we now repeated the MRIage14 → AAMage22 analysis by including (a) only the subjects who had no binge drinking experiences (n=477) by age 14 and (b) subjects who had one or less binge drinking experiences (n=565). The results are shown below. The balanced accuracy on the holdout set were 72.9 +/- 2% and 71.1 +/- 2.3% respectively, which is comparable to the main result of 73.1 +/- 2%.

These results provide further evidence that certain form of cerebral predisposition might be preceding the observed alcohol misuse behavior in the IMAGEN dataset. We discuss these results now in the Results section and the 2nd paragraph of Discussion.

3) The feature importance results for brain regions are quite inconsistent across time points. As such, the study doesn't really address one of the main challenges with previous work discussed in the introduction: "brain regions reported were not consistent between these studies either and do not tell a coherent story". This would be worth looking into further, for example by looking at other indices of feature importance such as permutation-based measures and/or investigating the stability of feature importance across bootstrapped CV folds.

The feature importance results shown in Figure 9 is intended to be illustrative and show where the most informative structural features are mainly clustered around in the brain, for each time point. We would like to acknowledge that this figure could be a bit confusing. Hence, we have now provided an exhaustive table in the Appendix, consisting of all important features and their respective SHAP scores obtained across the seven repeated runs. In addition, we address the inconsistencies across time points in the 3rd paragraph in the Discussion chapter and contrast our findings with previous studies. These claims can now be verified from the table of features provided in the Appendix.

Addressing the reviewer's suggestions, we would like to point out that SHAP is itself a type of permutation-based measure of feature importance. Since it derives from the theoretically-sound shapley values, is model agnostic, and has been already applied for biomedical applications, we believe that running another permutation-based analysis would not be beneficial. We have also investigated the stability of our feature importance scores by repeating the SHAP estimation with different random permutations. This process is explained in the Methods section Model Interpretation.

Additionally now, the SHAP scores across the seven repetitions are also provided in the Appendix table 6 for verification.

Author Response

Reviewer #1 (Public Review):

This paper tests the hypothesis that 1/f exponent of LFP power spectrum reflects E-I balance in a rodent model and Parkinson's patients. The authors suggest that their findings fit with this hypothesis, but there are concerns about confirmation bias (elaborated on below) and potential methodological issues, despite the strength of incorporating data from both animal model and neurological patients.

First, the frequency band used to fit the 1/f exponent varies between experiments and analyses, inviting concerns about potentially cherry-picking the data to fit with the prior hypothesis. The frequency band used for fitting the exponent was 30-100 Hz in Experiment 1 (rodent model), 40-90 Hz in Experiment 2 (PD, levodopa), and 10-50 Hz in Experiment 3 (PD, DBS). Ad-hoc reasons were given to justify these choices, such as " to avoid a spectral plateau starting > 50 Hz" in Experiment 3. However, at least in Experiment 3 (Fig. 3), if the frequency range was shifted to 1-10 Hz, the authors would have uncovered the opposite effect, where the exponent is smaller for DBS-on condition.

We agree that parameter choice is crucial, in particular, choice of the fitting range. In addition to the 40-90 Hz range (Figure 2C), we have performed aperiodic fitting for five other frequency ranges to test to what extent the reported results are sensitive to the selected frequency range (Figure S2A). This analysis showed that the results are robust when a broad frequency range from 30 to 95 Hz was chosen, which is consistent with what has been suggested by Gao et al., 2017 to make inferences on the E/I ratio.

Accordingly, we have now repeated the analyses for the animal data with the same fitting range used for the ON-OFF medication comparison in humans. Along with Figure S2A where different frequency ranges were tested for data used in Figure 2, this shows that the results in Figure 1 and 2 hold up with higher aperiodic exponents when STN spiking is low and vice versa. Therefore, a broad fitting range from 30 to 90 Hz (excluding harmonics of mains interference) generates consistent results for both human and animal data.

We opted against a fitting range from 1-10 Hz because of two restraints highlighted in Gerster et al., 2022. First, a fitting range starting at 1 Hz could have a larger y-intercept due to the presence of low-frequency oscillations. This could lead to a larger aperiodic exponent and could be misinterpreted as stronger neural inhibition. Therefore, the lower fitting bound should be chosen to best avoid known oscillations in the delta/theta range (Gerster et al., 2022). Second, frequencies should be chosen to avoid oscillations crossing fitting range limits. In Figure 3A, oscillations in the theta/alpha band both ON and OFF stimulation would complicate parameterisation and would likely result in spurious fits.

We also tested the effect of changing the peak threshold, peak width limits and the aperiodic fitting mode on FOOOF parameterisation. Increasing and decreasing the peak threshold from its default value (at 2 standard deviations) did not change results (Figure S2B). Similarly, adapting the peak width limits did not affect the exponent difference between medication states (Figure S2C). Finally, choosing the ‘knee’ mode instead of ‘fixed’ resulted in fundamentally different aperiodic fits that did not differ anymore with medication (Figure S2D). This is most likely a consequence of the near linear PSD in log-log space from 40 to 90 Hz (Figure 2B). If there is no bend in the PSD, the FOOOF algorithm will be forced to assign a ‘random’ knee and the aperiodic fit will then mostly reflect the slope of the spectrum above the knee point.

Second, there are important, fine-grained features in the spectra that are ignored in the analyses, which confounds the interpretation.

One salient example of this is Fig. 2, where based on the plots in B, one would expect that the power of beta-band oscillations to be higher in the Med-On condition, as the oscillatory peaks rise higher above the 1/f floor and reach the same amplitude level as the Med-OFF condition (in other words, similar total power is subtracted by a smaller 1/f power in the Med-ON condition). But this impression is opposite to the model-fitting results in C, where beta power is lower in the Med-ON condition.

We agree that PSDs over a broad frequency range (e.g. 5-90 Hz) typically do not have a single 1/f property. Instead, there can be multiple oscillatory peaks and ‘knees/bends’ in the aperiodic component. For these cases, fitting should be performed using the knee mode. To extract periodic beta power, we parameterise the PSD between 5 and 90 Hz and select the largest oscillatory component between 8 and 35 Hz (this range was extended to include the large oscillatory peaks in hemispheres 27 and 28 at ~ 10 Hz, see Figure R1). We now use the knee mode, to model the aperiodic component between 5 and 90 Hz when periodic beta power is calculated (see our previous comments). Figure R1 provides an overview of all PSDs ON and OFF medication, the aperiodic fits (5-90 Hz (knee) and 40-90 Hz (fixed)) and the detected beta peaks. In spite of this modification in our pipeline, periodic beta power is still larger OFF medication (Figure 2C), in keeping with previous studies (Kim et al., 2022; Kühn et al., 2006; Neumann et al., 2017; Ray et al., 2008). We acknowledge the reviewer’s point that the average spectra in Figure 2B are misleading in that respect and for clarity provide here all 30 spectra in both conditions. Note that the calculation of aperiodic exponents between 40 and 90 Hz is not affected by this change in our pipeline. Figures 2B, D+E were revised accordingly.

We have repeated the analysis of our animal data using the ‘knee mode’ with a fitting range from 30 to 100 Hz. However, using the knee mode did not improve the goodness of fit or fitting error and, in fact, made them slightly worse (Figure S5). Based on this, we think the fixed mode would provide a more holistic model for the PSDs used in this analysis. We have now added this comparison in Figure S5 to justify the choice of the fixed mode.

Figure R1. PSDs from all 30 hemispheres ON and OFF medication. Aperiodic fits are shown between 5-90 Hz (knee mode), which was used to calculate the power of beta peaks, and between 40-90 Hz (fixed mode), which was used to estimate the aperiodic exponent of the spectrum.

Another example is Fig. 1C, where the spectra for high and low STN spiking epochs are identical between 10 and 20 Hz, and the difference in higher frequency range could be well-explained by an overall increase of broadband gamma power (e.g. as observed in Manning et al., J Neurosci 2012, Ray & Maunsell PLoS Biol 2011). This increase of broadband gamma power is trivially expected, as broadband gamma power is tightly coupled with population spiking rate, which was used to define the two conditions.

We agree with the reviewer that in Figure 1C, high and low STN spiking states could well be separated by average gamma power (Figure 1E), too. However, the difference of aperiodic exponents is more prominent between both conditions (Figure 1D+E, based on p-values). What is more, in human LFP data recorded from clinical macroelectrodes, medication states can be reasonably well distinguished using the aperiodic exponent between 40-90 Hz (Figure 2C), but average gamma power does not separate both states (Figure S3A). This suggests that the aperiodic exponent reflects more than just power differences in the high gamma regions. In addition, power changes do not inevitably change the aperiodic exponent and vice versa as elaborated in (Donoghue et al., 2020).

Manning et al., 2009 show that the power spectrum is shifted to higher power values at all observed frequencies (2-150 Hz) as firing rates increase. As the reviewer points out, power spectra of our data are almost identical between 10-20 Hz (despite the marked spiking differences) and only drift apart from > 20 Hz (Figure 1C). This is a relevant difference between our study and Manning et al., 2009 and suggests that power differences in the gamma range are not solely explained by differences in spiking. This is confirmed when cortical activity at different spikes/sec is modelled (Miller et al., 2009). The entire spectrum is shifted to higher power values if spiking rates increase.

Ray & Maunsell, 2011 reported low (30-80 Hz) and high (> 80 Hz) gamma activity in the macaque visual cortex, with a positive correlation between spiking activity and high gamma activity. However, activities in the low gamma range (30-80 Hz), which largely overlaps with the frequency range in our study, does not necessarily correlate with firing rates.

In conclusion, the link between gamma power and spiking activity is not as strong as alluded. Even if the change in spiking activities can lead to changes of both gamma power and the aperiodic exponent, the aperiodic exponent would still constitute a measure to separate E/I levels and medication states.

The above consideration also speaks to a major weakness of the general approach of considering the 1/f spectrum a monolithic spectrum that can be captured by a single exponent. As the authors' Fig. 1C shows, there are distinct frequency regions within the 1/f spectrum that have different slopes. Indeed, this tripartite shape of the 1/f spectrum, including a "knee" feature around 40-70 Hz which is well visible here, was described in multiple previous papers (Miller et al., PLoS Comput Biol 2009; He et al., Neuron 2010), and have been successfully modeled with a neural network model using biologically plausible mechanisms (Chaudhuri et al., Cereb Cortex, 2017). The neglect of these fine-grained features confounds the authors' model fitting, because an overall increase in the broadband gamma power - which can be explained straightforwardly by the change in population firing rates - can result in the exponent, fit over a larger spectral frequency region, to decrease. However, this is not due to the exponent actually changing, but the overall increase of power in a specific sub-frequency-region of the broadband 1/f activity.

We have now used the knee mode for aperiodic fits between 5 and 90 Hz when periodic beta power is calculated. We agree that this broad frequency range is unlikely to have a single 1/f component.

We have also repeated the analysis of our animal data using the knee mode for aperiodic fits between 30 and 100 Hz (Figure S5). However, the goodness of fits had barely changed. In fact, the R2 and error become slightly worse. In addition, the knee parameter complicates interpretation of the aperiodic exponent and has to be considered along with the knee frequency. What is more, we do not see this bend around 40-70 Hz in all subjects. We show PSDs of representative LFP channels in Figure R2 and need to assert that the knee around 40-70 Hz is not a robust finding in our data set. Therefore, we chose the fixed mode for parameterisation within this frequency band.

Please see our answer to the previous comment regarding the link between broad gamma power and changes in population firing rates.

Figure R2. PSDs of representative PSD channels for each animal (data used in Figure 1C). The knee around 40-70 Hz is not a robust finding in all PSDs.

Author Response:

Reviewer #1:

The manuscript by Lalanne and Li aims to provide an intuitive and quantitative understanding of the expression of translation factors (TFs) from first principles. The authors first find that the steady-state solutions for translation sub-processes are largely independent at optimality. With a coarse-grained model, the authors derive the optimal expression of translation factors for all important sub-processes. The authors show that intuitive scaling factors can explain the differential expression of translation factors.

The results are impressive. However, as detailed in the major comments, the choice of some important parameters is not sufficiently justified in the current version. In particular, it is not clear to what extent parameter choice and rescaling was biased toward achieving a good agreement with the experimental data.

Major comments:

1) The work assumes that reaction times per TF are constant. That may be true at the highest growth rates, but it might not hold for conditions with lower growth rates. The data of Schmidt et al. (Nat. Biotechnol. 34, 104 (2016)) would allow to compare the predictions to proteome partitioning in E. coli across growth rates. It is ok to restrict the present work to maximal growth rates, but then this caveat should be made explicit. This last point also concerns ignoring the offset in the bacterial growth laws, which is only permissible at fast growth; that also should be stated more prominently in the manuscript; see also the legend of Fig. 1, "Our framework of flux optimization under proteome allocation constraint addresses what ribosome and translation factor abundances maximize growth rate".

We see two distinct but related points made by the reviewer, which we address in turn.

First, we thank the reviewer for highlighting the important and interesting point of the growth rate dependence of expression in components of the translational machinery, which encouraged us to investigate this aspect further. Leveraging other existing ribosome profiling datasets (which provide better quantitation than mass spectrometry data, see response to minor point #6 below) across multiple growth conditions and species, we compared the predicted optimal translation factor abundance in these conditions (using same formula for the optima). The new conditions and species now include E. coli at much slower growth rates, C. crescentus in two different media, and others. We found similar degrees of agreement between predicted and observed levels (shown in Figure 4-Figure supplement 1 ). One exception is aaRS in C. crescentus, and the discrepancy likely arises from a lack of quantification of tRNA abundance which is a parameter we use to predict the optimal aaRS levels.

These additional data also provided another way to examine the model predictions. Specifically, we assessed the predicted square-root scaling of translation factor abundance with growth rate. While the expression stoichiometry remains constant across growth rates (see response to minor point #6 below), the overall abundance decreases following our predicted scaling (Figure 4-Figure supplement 2B). We now describe these new analyses and results in the main text (p. 7, line 216):

"Analysis of tlF expression across slower growth conditions supports the derived square root dependence (Figure 4-Figure supplement 2)."

The second point made by the reviewer pertains to the “offset in bacterial growth law” that corresponds to inactive ribosomes, which make up a substantial fraction of ribosomes at very slow growth rates. We note that the derivation of the optimality condition, equation 5, does not rely on all ribosomes being active. What is necessary is that that there is a direct proteomic trade-off between ribosomes and translation factors (see response to minor point 1 below). To rigorously place our work in the context of previous literature, we have replaced mention of ribosome with “active ribosome” (as well as in equation 1 and Figure 1), which we define as those functionally engaged in the translation cycle. We also formally include the proteome fraction of inactive ribosome in equations 2 and 3 leading to the optimality condition.

2) The diffusion-limited regime considers only the free and idle reactants. For some translation factors, the free state only accounts for a small fraction of its total concentration. In this case, the diffusion-limited regime only explains a small fraction of the TFs. For example, most of EF-Ts may not be in its free state: in simulations with in vitro kinetics, free EF-Ts accounts for 6%-48% of its total concentration (Supplementary Data 3 in [21]). Can the authors use in vitro parameters (or other ways) to provide a rough estimate of the fraction of free TFs? Including this might allow to make quantitative statements about some of the deviations seen in Fig. 4, as most of the TFs are underestimated.

We thank the reviewer for the suggestion that deviations between the diffusion-limited prediction and the observed abundance might be quantitatively explained by the finite catalytic activity of the respective factors. However, to do so requires accurate values of kcat, which are often not available. In the Supplement of the initial submission, we provided an example of the in vitro kcat being not compatible with the protein synthesis rates in vivo, which we have now moved to the main text (reproduced below).

Another experimental approach that can feasibly be used to infer the bound fraction of translation factors in live cell is fluorescence microscopy of tagged proteins. Indeed, by quantifying the diffusive states of a tagged EF-Tu protein, Volkov et al (1) could estimate that <10% of EF-Tu was in its bound state, which is consistent with the agreement between our diffusion-limited prediction and observed abundance for that factor.

We now discuss these possibilities and the facts about EF-Ts in a paragraph in the Discussion (p. 13, line 471):

"Our optimization model can also be solved analytically in the non-diffusion-limited regime (Table 2), with the finite catalytic rate leading to an additional contribution of the form ∝ l 𝜆*/kcat. Recent detailed modeling of the EF-Ts cycle (Hu et al., 2020) estimated that a minor fraction (6 to 48%) of its abundance was in the free form in the cell, consistent with the large deviation we observe for this factor from our diffusion only prediction. However, the numerical values for these solutions are in general difficult to obtain because measurements of catalytic rates are sparse and often inconsistent with estimates of kinetics in live cells. As an example, the catalytic rates for aaRSs (Jeske et al., 2019) measured in vitro is ≈3 s-1 (median across different aaRSs), which is well below the minimal value of 15 s-1 required to sustain translation flux at the measured translation elongation rate (Appendix 5), suggesting substantial deviation between in vitro and in vivo kinetics. Although technically demanding, the fraction of free vs. bound factors can in principle be determined through live cell microscopy of tagged factors based on the partitioning the diffusive states of enzymes. Using that approach, (Volkov et al., 2018) estimated that EF-Tu was in its bound state <10% of the time (consistent with the agreement between our diffusion-limited prediction and the observed value for this factor)."

3) "A factor-independent time τ_ind (e.g., peptidyl transfer), which does not come into play in our optimization framework, was added to account for additional steps making up the full elongation cycle." - what happened to this time? I couldn't find it anywhere else in the paper. What value was chosen, and by what rationale?

We thank the reviewer for pointing out a lack of clarity in our presentation. The factor-independent time τind in fact did not appear in our optimization procedure at all (by virtue of obeying dτind/d𝜙TFi = 0 by definition), and was only included for generality to account for steps such as peptidyl transferase (extremely fast (2)). In line with the parsimony of our model, and to avoid any confusion, we have now removed this factor from our model and description altogether.

4) Fig. 4: The agreement is very impressive, especially given the simplifying assumptions. However, there are some questions relating the choice of parameters.

a) Were any parameters fitted? Which, how? What about τ_ind, for example (see above)?

Our approach does not include any fitted parameter. We instead rely on biophysically measured quantities such as diffusion constants, protein sizes, tRNA abundances, cell doubling times (growth rates), and in vivo kinetic estimates. (In the line of Major Comment #3 above, we have removed τind for clarity.) We now include all quantities needed to predict the optimal translation factor abundances (using the formula listed in section “Summary of optimal solutions”, Table 2) in Appendix 5-Tables 1-3, including new Appendix 5-Tables 2-3, reproduced below.

b) The "predicted" value for ribosomes is calculated from observed data (in a way described on p. S34 that I found incomprehensible, and would likely look very similar regardless of the predicted values for the TFs). According to the section "Equipartition between TF and corresponding ribosomes", the corresponding ribosomes can be quantified in the authors' scheme, too, by the method used for deriving optimal TF concentrations in equation 5. Why didn't the authors directly use the sum of these estimations as the optimal ribosome concentration in Fig. 4? In the current state, it does not seem fair to include the ribosome with the other predictions.

We agree that the nature of the prediction for ribosomes was different than for other translation factors in our original manuscript in a way that might have lacked clarity. We now exclude ribosomes from Fig. 4 to avoid any possible confusion.

It is interesting to directly estimate ribosome abundance using the equipartition principle. This estimation is however limited by the fact that the equipartition principle only accounts for ribosomes that are waiting for factor- dependent binding steps. Substantial fractions of ribosomes may be engaged at factor-free steps (e.g., peptidyl transfer catalyzed by ribosome itself) and factor-dependent catalytic steps after binding. Although the latter could be estimated using the observed tlF concentrations (by considering that the tlF in excess to the binding-limited predictions is sequestered in catalytic steps), the former is not estimated in our model. Furthermore, some other ribosomes may not be fully assembled yet or are inactive (3). Indeed, the predicted factor-dependent ribosome abundance using the equipartition principle with observed tlF abundances constitute a fraction (40%) of the measured total ribosome abundance.

c) Predictions are for a specific growth rate (doubling time 21min). Was this growth rate also averaged over the three organisms? What were the individual values? These points would need to be discussed in the main text.

The reviewer is correct. In the initial submission, we used the average growth rate of E. coli (doubling time 21.5±0.4 min), B. subtilis (doubling time 21±1 min), and V. natriegens (doubling time 19±1 min). A note has been added in the main text (p. 11, line 448):

"We take the growth rate 𝜆* to be the average of the fast-growing species considered, corresponding to a doubling time of 21±1 min (E. coli: 21.5±1 min, B. subtilis: 21±1 min, V. natriegens: 19±1 min)."

In addition, we now include predictions for different growth rates and compared them with several bacterial species grown in a wide range of conditions (Figure 4-Figure supplement 1) (see response to Major Comment #1 and to reviewer 2’s third request). These predictions and data are now included in Supplementary Files 1-4.

5) In the same vein, in a footnote (!) to Table S4: "#For the ternary complex, the total mass of tRNA+EF-Tu was converted to an equivalent amino acid length." - I can see that this is important to get reasonable results, but it constitutes a major deviation from the strategy proclaimed throughout the main text: that the predicted effects result from a competition for fractions of the limited proteome. That rationale has to be changed (and explained in the main text), or the predictions in Fig. 4 should be based on calculations using only the protein part of TCs (i.e., EF-Tu).

We are sorry for the confusion. The procedure of converting tRNA size to protein size was only used to estimate diffusion coefficients for the ternary complex (described in Appendix 5 Table 2), and not for the competition within the proteome. For factors for which no direct experimental estimates exist for in vivo diffusion coefficient, we used the relationship DA = (lTC/lA)1/3 DTC. The resulting estimated diffusion coefficients were then used to rescale the association rate inferred from in vivo measurements for the ternary complex (see response to point 6 below as well) to obtain association rates for other factors.

6) S9: "we anchored our association rates to the estimated in vivo association rate for the ternary complex, 𝑘^𝑇𝐶 = 6.4 μM−1s−1 [13], and rescale the association rate by diffusion of related components" - in comparison, the diffusion limited k^TC is >100. If I understand this correctly, you simply rescale ALL on-rates by 100/6.4 = 15.6. If that is (qualitatively) correct, you would need to discuss this point (and the derivation of the scaling factor) explicitly in the main text.

The reviewer is correct in his interpretation of our approach, and we are grateful for his remark as this led us to spot a mistake in our choice of parameter (capture radius R). Indeed, while the ternary complex as a largest physical dimension of about 10 nm (from structural data (4)), the appropriate capture radius is closer to 2 nm (size of the portion binding to the ribosome) (5). Correcting for the appropriate capture radius alone brings the estimate to 45 μM-1s-1 , which is however still several-fold higher than the measured value of 6.4 μM-1s-1. Whereas a part of this could be due to systematic overestimation of the diffusion coefficient, a large portion of the discrepancy is assuredly due to the many simplifying assumptions underlying the Smoluchowski estimate which serve to place an absolute upper bound on the reaction rate (perfectly/instantaneously absorbing spheres, and hence no notion of specific reaction position or molecular orientation).

The estimate for capture radius R has been corrected (p. 47, line 1605) and a new sentence has now been included in the main text (p. 11, line 441):

"Importantly, the absolute values of the optimal concentrations can be anchored by the association rate constant between TC and the ribosome obtained from translation elongation kinetic measurements in vivo (Dai et al., 2016). The latter was found to be several-fold smaller than the simplest and absolute upper bound of a Smoluchowski estimate of perfectly absorbing spheres (section Estimation of optimal abundances), and we assume that the rescaling factor is the same for all reactions."

Author Response

Reviewer #1 (Public Review):

Iyer et al. address the problem of how cells exposed to a graded but noisy morphogen concentration are able to infer their position reliably, in other words how the positional information of a realistic morphogen gradient is decoded through cell-autonomous ligand processing. The authors introduce a model of a ligand processing network involving multiple ”branches” (receptor types) and ”tiers” (compartments where ligand-bound receptors can be located). Receptor levels are allowed to vary with distance from the source independently of the morphogen concentration. All rates, except for the ligand binding and unbinding rates, are potentially under feedback control. The authors assume that the cells can infer their position from the output of the signalling network in an optimal way. The resulting parameter space is then explored to identify optimal ”network architectures” and parameters, i.e. those that maximise the fidelity of the positional inference. The analysis shows how the presence of both specific and non-specific receptors, graded receptor expression and feedback loops can contribute to improving positional inference. These results are compared with known features of the Wnt signalling system in Drosophila wing imaginal disc.

The authors are doing an interesting study of how feedback control of the signalling network reading a morphogen gradient can influence the precision of the read-out. The main strength of this work is the attention to the development of the mathematical framework. While the family of network architectures introduced here is not completely generic, there is enough flexibility to explore various features of realistic signalling systems. It is exciting to find that some network topologies are particularly efficient at reducing the noise in the morphogen gradient. The comparison with the Wnt system in Drosophila is also promising.

Major comments:

1) The authors assume that the cell estimates its position through the maximum a posteriori estimate, Eq.(5), which is a well-defined mathematical object; it seems to us however that whether the cell is actually capable of performing this measurement is uncertain (it is an optimal measurement in some sense, but there is no guarantee that the cell is optimal in that respect). Notably, this entails evaluating p(theta), which is a probability distribution over the entire tissue, so this estimate can not be done with purely local measurements. Can the authors comment on this and how the conclusions would change if a different position measurement was performed?

This is indeed an important question. Our viewpoint is that if the cells were to use a maximum a posteriori (MAP) estimate (Eq. 5) to decode their positions, then what features of the channel architecture would lead to small errors in positional inference. Whether the maximum a posteriori estimate is employed by the cell, or some other estimate, is an important but difficult question to address. Our choice has been motivated by how this estimate has allowed the precise determination of developmental fates in the context of gap gene expression in Drosophila embryo [1, 2, 3]. We had earlier computed the inference error with a different estimate i.e.

which computes the mean squared deviations of the inferred positions from the true position for each x, taking into account the entire distribution p(x∗|x). While the qualitative results are the same, the inference errors showed spurious jitters from outliers in sampling the noisy morphogen input distribution. This consistency might suggest that our qualitative results are insensitive to the choice of the estimate.

Further, when evaluating the MAP estimate, the term p(θ) in the denominator serves as a normalisation factor to ensure p(x|θ) is a probability density. This is not strictly necessary for MAP estimation. Since p(θ) does not depend on x, the MAP estimate can be written as follows

without the need for evaluating p(θ). In the case of a uniform prior, it would be equivalent to maximum likelihood estimate (MLE) i.e.

2) One of the features of the signalling networks studied in the manuscript is the ability of the system to form a complex (termed a conjugated state, Q) made of two ligands L, one receptor and one nonsignalling receptor. While there are clear examples of a single ligand binding to two signalling receptors (e.g. Bmps), are there also known situations where such a complex with two ligands, one receptor, and one non-signalling receptor can form? In the Wnt example (Fig. 10a), it is not clear what this complex would be? In general, it would be great to have a more extended discussion of how the model hypothesis for the signalling networks could relate to real systems.

This is a good suggestion. We have now added a discussion on the various possible realisations of the “conjugate state” Q in Section 3.6. We have also explored the various states in the context of different signalling contexts such as Dpp, Hh, Fgf in the Discussion section.

The conjugated state ‘Q’ represents a combination of the readings from the two branches i.e. receptor types. This could be realised through processes like ligand exchange or complex formation, both in a shared spatial location such as a compartment. As discussed in the original manuscript (Section 3.6 of the revised manuscript), the ligand Wg in the Wg signalling pathway is internalised through two separate endocytic pathways associated with the receptor types - signalling receptor Frizzled (via Clathrin-mediated endocytosis (CME)) and non-signalling receptor HSPGs (via the CLIC/GEEC pathway (CLIC - (clathrin-independent carriers, GEEC - GPI-anchored protein-enriched early endosomal compartments)). Both pathways meet in a common early endosomal compartment where the ligands may be exchanged between the two receptors [4]. In a previous work by Hemalatha et al [4], we had shown that there are more Wg-DFz2 interactions in the endosomal compartment (measured through FRET) than on the cell surface. Therefore, the non-signalling receptors directing Wg through the CLIC/GEEC pathway titrate the amount of Wg interaction with the signalling receptor, DFz2.

As mentioned in the original manuscript (Section 3.3 and subsection 4.2 of the Discussion in the revised manuscript), apart from Wg signalling, non-signalling receptors such as the HSPGs have also been proposed to act as co-receptors for Dpp, Hh, FGF (reviewed in [5, 6]). Although some ligands bind to the core protein of HSPG, the majority of the ligands bind to the negatively charged HS chains [7, 8]. Here, the coreceptors HSPGs aid in capturing diffusible ligands and presenting the same to signalling receptors (either on the cell surface or within endosomes).

3) The authors consider feedback on reaction rates - it would seem natural to also consider feedback on the total number of receptors; notably, since there are known examples of receptors transcriptionally down-regulated by their ligands (e.g. Dpp/Tkv)? Also it is not clear in insets such as in Fig. 7b, if the concentration plotted corresponds to the concentration of receptors bound to ligands?

As mentioned in the original manuscript (Section 2.2 of the revised manuscript), we have indeed considered control on reaction rates and receptors, although the control on the latter is done with the constraint of receptor profiles being monotonic. Further, while the control on reaction rates is considered via feedbacks explicitly, the control on receptors is done via an approach akin to the openloop control used in control theory. In reality, cellular control on receptors will involve transcriptional up- or down-regulation of receptor and thus warrant a feedback control approach – however, the timescales involved in such a control are different from the binding-unbinding and signalling timescales.

Therefore, in the current work, we take the morphogen profile to be given i.e. independent of receptor concentrations, and we ask for the receptor concentrations that would help reduce the inference errors.

Our predictions of increasing signalling receptor and decreasing non-signalling receptors in a twobranch channel architecture are consistent with the known transcriptional up-regulation of Dally/Dlp and down-regulation of Fz by Wg signalling [9].

In a future work, we will extend the control on receptors to include feedbacks explicitly. Furthermore, the explicit feedback control on receptors may need to be considered concomitantly with the effect of receptors on morphogen dynamics (i.e. morphogen sculpting by receptors) along with the possibility of spatial correlations in receptor concentrations through neighbouring cell-cell interactions.

As mentioned in the original manuscript (Section 2.2 of the revised manuscript), the variables ψ and φ stand for the total (bound + unbound) surface receptor concentrations of the signalling and the non-signalling receptors respectively. Therefore, the insets showing receptor profiles such as in Fig. 6b, 7b, and Appendix H Fig.8b,e correspond to the total surface receptor concentrations.

4) The authors are clear about the fact that they consider the morphogen gradient to be fixed independently of the reaction network; however, that seems like a very strong assumption; in the Dpp morphogen gradient for instance over expression of the Tkv receptor leads to gradient shortening. Can the authors comment on this?

This point is related to the earlier question 4. As discussed in the Discussion of the original manuscript (subsection 4.3 of the revised manuscript), we focus on finding the optimal receptor concentration profiles and reaction networks that enable precision and robustness in positional information from a given noisy morphogen profile. The framework and the optimisation scheme within it will prescribe different receptor profiles and reaction networks for different monotonically behaving, noisy morphogen profiles. It is possible that cells may achieve the optimal receptor concentrations via feedback control on production of the receptors.

Broadly, morphogen dynamics depends on cell surface receptors, which could participate in both the inference and the sculpting of the morphogen profile, and factors independent of them such as extracellular degradation, transport and production, etc. In our present work, we have taken the receptors involved in sculpting and inference as being independent.

In a more general case, feedback control on receptors will change the receptor concentrations as well as the morphogen profile. We are currently working on realising such a feedback control on receptors within the same broader information theoretic framework proposed in the current work.

5) Fig. 10f is showing an exciting result on the change in endocytic gradient CV in the WT and in DN mutant of Garz. Can the authors check that the Wg morphogen gradient is not changing in these two conditions? And can they also show the original gradient, and not only its CV?

The reviewer raises a legitimate concern – could the observed changes in CV upon perturbation of endocytic machinery be attributed to a systematic change in the mean levels of the endocytosed Wg alone? In the original manuscript (Appendix O Fig.17b,c of the revised manuscript), we show the normalised profiles of endocytic Wg in control and myr-Garz-DN cases. Here, in Fig.1 below, we show a comparison between the mean Wg concentrations (measured as fluorescence intensity) in control wing discs and discs wherein CLIC/GEEC endocytic pathway is removed using UAS-myr-Garz-DN. For clarity, we show the discs with largest and smallest fluorescence intensities from the control and myr-Garz-DN discs. It is hard to conclude that the mean concentrations are significantly different in the two cases.

Reviewer #2 (Public Review):

The work of Iyer et al. uses a computational approach to investigate how cells using multiple tiers of processing and multiple parallel receptor types allow more accurate reading of position from a noisy signal. Authors find that combining signaling and non-signaling types of receptors together with additional feedback increases the accuracy of positional readout against extrinsic noise that is conveyed in the morphogen signal. Further, extending the number of layers of signal processing counteracts the intrinsic stochasticity of the signal reading and processing steps. The mathematical formulation of the model is general but comprehensive in the way it handles the difference between branches and tiers for the processing of channels with feedbacks. The results of the model are presented from simple one-branch and one-tier architecture to two-branch and two-tier architecture with feedbacks. Interestingly authors find that adding more tiers results in only very small improvements in the accuracy of positional readout. The model is tested against a perturbation experiment that impairs one of the signaling branches in the Drosophila wing disc, but the comparison is only qualitative as further experiment-oriented work is planned in a separate paper.

Strengths

There is a clear statement of objectives, model, and how the model is evaluated. In particular, the objective is to find what number of receptor types and their concentrations for a given number of tiers and feedback types is resulting in the most accurate positional readout. The employed optimization procedure is capable to find signalling architectures that result in one cell diameter positional precision for most of the tissue with 3-4 cells at the tissue end that is most distant to the morphogen source. This demonstrates that employing additional complexity in signal processing results in a very accurate positional readout, which is comparable with estimates of positional precision obtained in other developmental systems (Petkova et al., Cell 2019, Zagorski et al., Science 2017).

The optimal signalling architectures indicate that both signalling (specific) and non-signalling (nonspecific) receptors affect the precision of positional readout, but the contributions of each type of these receptors are qualitatively different. Even slight perturbation of signalling receptors drives the system out of optimum, resulting in a decrease in positional precision. In contrast, the non-signalling receptors could accommodate much larger perturbations. This observation could provide a biophysical explanation for how cross-talk between different morphogen species could be realized in a way that positional precision is kept at the optimum when morphogen signaling undergoes extrinsic and intrinsic perturbations.

Last, the model formulation allows to specifically address perturbations of signalling and feedbacks, that could be explored to validate model predictions experimentally in Drosophila wing disc, but also in other developmental tissues. The authors present a proof-of-concept by obtaining consistent results of variation of output profiles in two-tier two-branch architectures with non-signaling branch removed and intensity profiles of Wg in wing disc where the CLIC/GEEC endocytic pathway was perturbed.

Weaknesses

The list of model parameters is long including more than 20 entries for two-tier two-branch architectures. This is expected, as the aim of the model is to describe the sophisticated signalling architecture mimicking the biological system. However, this also makes it very challenging or impossible to provide guiding principles or understanding of the system behaviour for the complete space of signalling architectures that optimize positional readout. Although, the employed optimization procedure finds solutions that exhibit very high positional accuracy, there is only very limited notion how these solutions depend on variation of different parameters. The authors do not address the following question, whether these solutions correspond to broad global optima in the space of all solutions, or were rather fine-tuned by the optimization procedure and are quite rare.

It is unclear how contributions from the intrinsic noise affect the system behaviour compared to contributions from extrinsic noise. In principle, the two-branch one-tier architecture results in an already very accurate positional readout across the tissue. The adding of another tier seems to provide only a very weak improvement over a one-tier solution. It is possible that contributions from intrinsic noise for the investigated signalling architectures are only mildly affecting the system compared with contributions from extrinsic noise. Hence, it is difficult to assess whether the claim of reducing intrinsic noise by adding another tier is supported by the presented data, as the contributions from intrinsic noise could overall very weakly affect the positional readout.

The optimal response of the channel to extrinsic and intrinsic noises is very distinct. As noted correctly by the reviewer, an additional tier provides only a marginal improvement in inference error due extrinsic noise (compare Fig.7 and Fig.8 in the revised manuscript). However, as shown in Fig.9c of the revised manuscript (same as in the original manuscript), adding an extra tier provides a substantial improvement in inference errors due to intrinsic noise.

References

[1] Gasper Tkacik, Julien O Dubuis, Mariela D Petkova, and Thomas Gregor. Positional information, positional error, and readout precision in morphogenesis: a mathematical framework. Genetics, 199:39– 59, 2015.

[2] Mariela D Petkova, Gasper Tkacik, William Bialek, Eric F Wieschaus, and Thomas Gregor. Optimal decoding of cellular identities in a genetic network. Cell, 176:844–855, 2019.

[3] Julien O Dubuis, Gaˇsper Tkaˇcik, Eric F Wieschaus, Thomas Gregor, and William Bialek. Positional information, in bits. Proceedings of the National Academy of Sciences, 110:16301–16308, 2013.

[4] Anupama Hemalatha, Chaitra Prabhakara, and Satyajit Mayor. Endocytosis of wingless via a dynaminindependent pathway is necessary for signaling in drosophila wing discs. Proceedings of the National Academy of Sciences, 113:E6993–E7002, 2016.

[5] Xinhua Lin. Functions of heparan sulfate proteoglycans in cell signaling during development. Development, 131:6009–6021, 2004.

[6] Stephane Sarrazin, William C Lamanna, and Jeffrey D Esko. Heparan sulfate proteoglycans. Cold Spring Harbor perspectives in biology, 3(7):a004952, 2011.

[7] Catherine A Kirkpatrick, Sarah M Knox, William D Staatz, Bethany Fox, Daniel M Lercher, and Scott B Selleck. The function of a drosophila glypican does not depend entirely on heparan sulfate modification. Developmental biology, 300(2):570–582, 2006.

[8] Mariana I Capurro, Ping Xu, Wen Shi, Fuchuan Li, Angela Jia, and Jorge Filmus. Glypican-3 inhibits hedgehog signaling during development by competing with patched for hedgehog binding. Developmental cell, 14(5):700–711, 2008.

[9] Kenneth M Cadigan, Matthew P Fish, Eric J Rulifson, and Roel Nusse. Wingless repression of drosophila frizzled 2 expression shapes the wingless morphogen gradient in the wing. Cell, 93(5):767–777, 1998.

Author Response

Reviewer #1 (Public Review):

Strength: The study is summarizing a large cohort of human samples of blood, nasal swabs and nasopharyngeal aspirates. This is very uncommon as most of the time studies focus on the blood and serum of patients. Within the study, 3 monocyte and 3 DC subsets have been followed in healthy and Influenza A virus-infected persons. The study also includes functional data on the responsiveness of Influenza A virus-infected DC and monocyte populations. The authors achieved their aims in that they were able to show that the tissue microenvironment is important to understand subset specific migration and activation behavior in Influenza A virus infection and in addition that it matters with which kind of agent a person is infected. Thus, this study also impacts a better understanding of vaccine design for respiratory viruses.

We thank Reviewer 1 for highlighting what we believe to be the greatest strengths of our study. The key feature of this study was to generate a comprehensive description of monocytes and dendritic cells (DC) in the human nasopharynx during influenza A virus infection, and to provide a comparison with healthy and convalescent individuals. Further, we wished to emphasize the value of studying the nasopharynx during respiratory viral infections, particularly in light of the ongoing COVID-19 pandemic. We describe a non-invasive method to (longitudinally) sample this anatomical compartment that allows retrieval of intact immune cells as well as mucosal fluid for soluble marker analysis. We also believe that the addition of proteomic profiles in the different compartments (new Figure 7) further highlights the importance of the tissue microenvironment.

Weakness: In the described study, the authors used a different nomenclature to introduce the DC subsets. This is confusing and the authors should stick to the nomenclature introduced by Guilliams et al., 2014 (doi.org/10.1038/nri3712) and commented in Ginhoux et al., 2022 (DOI: 10.1038/s41577-022-00675-7 ) or at least should introduce the alternative names (cDC1, cDC2, expression markers XCR1, CD172a/Sirpa). Further, Segura et al., 2013 (doi: 10.1084/jem.20121103) showed that all three DC subpopulations were able to perform cross-presentation when directly isolated. Overall, a more up-to-date introduction would be useful.

Reviewer 1 commented on the DC nomenclature used in the manuscript. We agree that our manuscript would benefit from appropriately updating the DC nomenclature. We therefore revised the text, and now we refer to the subsets previously described as CD1c+ and CD141+ myeloid DCs (MDC) as cDC2 and CDC1 subsets, respectively. We have also modified the text in the Introduction of the revised manuscript to reflect the same and give a more up-to-date introduction of DC subsets (marked-up version lines 75-81).

As the data of this was already obtained in 2016-2018 it is clear that the FACS panel was not developed to study DC3. If possible, the authors might be able to speculate about the role of this subset in their data set. Moreover, there were other studies on SARS-CoV-2 infection and DC subset analyses in blood (line 87, and line 489) e.g. Winheim et al., (DOI: 10.1371/journal.ppat.1009742 ), which the authors should introduce and discuss in regard to their own data.

As reviewer 1 accurately pointed out, the flow cytometry panel used in this study was indeed not developed to study the DC3 subset. The data was obtained in 2016-2018, and lack the typical markers used to identify the DC3 subset, such as CD163, BTLA and CD5 (Cytlak et al, https://doi.org/10.1016/j.immuni.2020.07.003, Villani et al, https://doi.org/10.1126/science.aah4573). Due to the constraints of the panel, we would not be able to accurately identify DC3s. However, in an attempt to dig deeper into the data that is available, we re-analyzed the data to identify CD14+CD1c+ cells among the lineage–HLADR+CD16–CD14+ cells, here collectively called “mo-DC”. This population is likely a combination of monocytes upregulating CD1c and bona fide DC3 expressing CD14. Accordingly, the gating strategy was updated in Supplementary figure 1 (marked-up version lines 192-194), and new data plot in Figure 2H (marked-up version lines 208-220) summarizes the changes observed in mo-DC numbers in IAV patients between blood and the nasopharynx. Parallel to the pattern seen in other DC subsets, mo-DC frequencies are reduced in blood and we observed an increase (not significant) in the nasopharynx.

As CD88 was not included in the original panel, it was not possible to discriminate between bona fide monocytes and DC3s. We performed a staining of PBMCs (buffy coat) with CD88 (FITC) added to the original flow panel used in the study, to assess if CD88 can be helpful for future studies (Reviewer figure 1). The staining showed that some cells in the mo-DC population are CD88 positive, indicating a bona fide monocyte origin, whereas some are negative, indicating that they are bona fide DC3 expressing CD14. (Bourdely et al, https://doi.org/10.1016/j.immuni.2020.06.002).

Reviewer figure 1. Expression of CD88 in the “mo-DC” population. Cells from a buffy coat were stained with the flow cytometry panel used in the manuscript, with the addition of CD88 (FITC). Within the CD14+CD1c+ population, the “mo-DC” population, we identified both CD88+ and CD88- cells.

Reviewer 1 also suggested citing Winheim et al (https://doi.org/10.1371/journal.ppat.1009742), and we thank them for their suggestion. We have now cited Winheim et al, and two additional reports (Kvedaraite et al, https://doi.org/10.1073/pnas.2018587118 and Affandi et al, https://doi.org/10.3389/fimmu.2021.697840) describing a depletion of DC3s (and other DC subsets) from circulation, and functional impairment of DCs following SARS-CoV-2 infection. Further, Winheim et al observed an increased frequency of a CD163+CD14+ subpopulation within the DC3s, which correlated with systemic inflammatory responses in SARS-CoV-2 infection. We speculate that perhaps in IAV infection too, DC3s may follow the trend of other DC subsets and be found in increased numbers in the nasopharynx (marked-up version lines 75-81 and 543-552).

Taken together, although the data are very important and very interesting, my overall impression of the manuscript is that in the era of RNA seq and scRNA seq analyses the study lacks a bit of comprehensiveness.

The final comment from reviewer 1 is well taken, in that our study does not include RNA-seq analyses. Again, we ask Reviewer 1 to take into consideration the challenging material we worked with in our study in combination with the COVID-19 pandemic that subsequently has excluded recruitment of new influenza patients to the study. The cell numbers and viability in the nasopharyngeal aspirates limit what experimental approaches can be done simultaneously, and flow cytometry seemed to be the best approach for the study. However, we agree that in future studies, both our own and those of others in the field, will greatly benefit from single cell analysis of nasopharyngeal immune cells, and from generating transcriptomic or epigenetic profiles of these cells. Unfortunately, it is a limitation that we are currently unable to overcome within the scope of this revision. Despite this weakness, we agree with Reviewer 1 that the methods we developed and the data we generated are important and interesting.

Moreover, we have added additional proteomics data from both NPA and plasma from influenza and COVID-19 patients, using the SomaScan platform (new Figure 7) (marked-up version lines 472-511, 738-755 and 768-792). We also included a supplementary table listing enriched pathway data from gProfiler. Briefly, our data showed sizeable changes within the blood and nasopharyngeal proteome during respiratory virus infection (IAV or SARS-CoV-2), as compared to healthy controls. Importantly, we found several differentially expressed proteins unique to the nasopharynx that were not seen in blood, and pathway analysis highlighted “host immune responses” and “innate immunity” pathways, containing TNF, IL-6, ISG15, IL-18R, CCL7, CXCL10 (IP-10), CXCL11, GZMB, SEMA4A, S100A8, S100A9. These findings are in line with our flow cytometry data, and support our hypothesis that the immunological response to viral infection in the upper airways differ from that in matching plasma samples. One of the main messages in this manuscript is the importance of looking at the site of infection, and not only at systemic immune responses to better understand respiratory viral infections in humans. We believe that the addition of the proteomics data serves to further highlight this point.

Reviewer #2 (Public Review):

This study aims to describe the distribution and functional status of monocytes and dendritic cells in the blood and nasopharyngeal aspirate (NPA) after respiratory viral infection in more than 50 patients affected by influenza A, B, RSV and SARS-CoV2. The authors use flow cytometry to define HLA-DR+ lineage negative cells, and within this gate, classical, intermediate and non-classical monocytes and CD1c+, CD141+, and CD123+ dendritic cells (DC). They show a large increase in classical monocytes in NPA and an increase in intermediate monocytes in blood and NPA, with more subtle changes in non-classical monocytes. Changes in intermediate monocytes were age-dependent and resolution was seen with convalescence. While blood monocytes tended to increase in blood and NPA, DC frequency was reduced in blood but also increased in NPA. There were signs of maturation in monocytes and DC in NPA compared with blood as judged by expression of HLA-DR and CD86. Cytokine levels in NPA were increased in infection in association with enrichment of cytokine-producing cells. Various patterns were observed in different viral infections suggesting some specificity of pathogen response. The work did not fully document the diversity of human myeloid cells that have arisen from single-cell transcriptomics over the last 5 years, notably the classification of monocytes which shows only two distinct subsets (intermediate cannot be distinguished from classical), distinct populations of DC1, DC2 and DC3 (DC2 and 3 both having CD1c, but different levels of monocyte antigens), and the lack of distinction provided by CD123 which also includes a precursor population of AXL+SIGLEC6+ myeloid cells in addition to plasmacytoid DC. Furthermore, some greater precision of the gating could have been achieved for the subsets presented. Specifically, CD34+ cells were not excluded from the HLA-DR+ lineage- gate, and the threshold of CD11c may have excluded some DC1 owing to the low expression of this antigen. Overall, the work shows that interesting results can be obtained by comparing myeloid populations of blood and NPA during viral infection and that lineage, viral and age-specific patterns are observed. However, the mechanistic insights for host defense provided by these observations remain relatively modest.

We thank Reviewer 2 for their assessment of our manuscript and summarizing our key findings in their public review. As reviewer 2 noted, our study describes changes in frequencies of monocytes and DCs during acute IAV infection, in blood and in the nasopharynx. Additionally, we also demonstrate pathogen-specific changes in both compartments. Reviewer 2 also highlighted a drawback of our study- that the approach did not fully capture the breadth of monocyte and DC diversity as it currently stands. Despite this, the findings we presented here laid the groundwork for continued research and led to significant progress, including mechanistic insights (Falck-Jones et al, https://doi.org/10.1172/JCI144734 and Cagigi et al, https://doi.org/10.1172/jci.insight.151463, Havervall et al. https://doi.org/10.1056/nejmc2209651 and Marking et al. Lancet Infectious Diseases in press), in understanding the role of myeloid cells in the human airways during viral infections.

Author Response

Reviewer #1 (Public Review):

In the article "Whole transcriptome-sequencing and network analysis of CD1c+ human dendritic cells identifies cytokine-secreting subsets linked to type I IFN-negative autoimmunity to the eye," Hiddingh, Pandit, Verhagen, et al., analyze peripheral antigen presenting cells from patients with active uveitis and control patients, and find several differentially expressed transcription factors and surface markers. In addition, they find a subset of antigen presenting cells that is decreased in frequency in patients with uveitis that in previous publications was shown to be increased in the eye of patients with active uveitis. The greatest strength of this paper is the ability to obtain such a large number of samples from active uveitis patients that are not currently on systemic therapy. While the validation experiments have methodologic flaws that decrease their usefulness, this study will still serve as a valuable resource in generating hypotheses about the pathogenesis of uveitis that can be tested in future projects.

We thank the reviewer for the constructive comments and effort to review our work in detail.

Since all CD36+CX3CR1+ cells are CD14+ (Figure 4D), how CX3CR1 ended up being differentially regulated in a similar way despite this population was excluded from 2nd bulk RNAseq data set should be commented on by the authors.

We agree with reviewer that the CD14 surface expression in relation to the black-gene module and CD36+CX3CR1+ DC3s requires more detailed analysis. As described in the results section, genes in this module are linked to both CD1c+ DCs and inflammatory CD14+ monocytes, which we cannot distinguish by bulk RNA seq analysis. Therefore, we aimed to use an approach to demonstrate that the black module is a bona fide CD1c+ DC gene signature not dependent on CD14 surface expression: We showed that there was not difference in CD14+ cell fractions in the samples for RNA-seq between patient and control samples (see Fig. 1F). We now further investigated this by additional data and experiments. We now show in Figure 2 Supplement 2A that CD14 – as expected - does not correlate with the black module. To confirm this experimentally, we purified CD14+CD1c+ and CD14- CD1c+ DCs from 6 donors and subjected these to qPCR analysis to evaluate the expression of key genes from the black module (see revised Figure 2A). As illustrated in revised Figure 2 panel B, we show that the expression levels of genes, including CD36 and CX3CR1, are not significantly altered between CD14+/- CD1c+ DCs which supports that the identified gene module is also not dependent on CD14 surface expression by CD1c+ DCs. To assess if the expression of the black module was also independent of CD14 in inflammatory disease, we used RNA-seq data from FACS-sorted CD14+CD1c+ DCs and CD14-CD1c+ DCS from patients with SLE and Scleroderma (GSE13731) and confirm that the expression of the black module genes is independent from CD14 surface expression (see revised Figure 2 panel C). Finally, we removed CD14+ cells from the analysis in the 2nd bulk RNA-seq experiment to proof that indeed the black module could be perceived as being associated with uveitis independent of CD14+ expression which allowed attributing the black module to CD1c+ DCs by bulk RNA-seq analyses. Also, more detailed analysis by flow cytometry (Revised Figure 4) and scRNA-seq (Figure 6) confirm these findings. For example, we show that the CD36+ CX3CR1+ DC3s are in fact a subset of CD14+ CD1c+ DCs (Figure 2 – Supplement 2) and we show that eye-infiltrating CD1c+ DCs that harbor the black module gene signature show increased CD36 and CX3CR1, but not CD14 (Figure 6C). We have addressed all these experiments and data in the result section on page 12-13, 16,17, and in the discussion section on page 19. We hope the reviewer agrees that this has now been sufficiently addressed.

Line 153: "...substantiates this gene set as a core transcriptional feature of human autoimmune uveitis." It would be difficult to argue that when only 137 of the 1236 DEGs from the first module are repeated in a validation data set that this is the core transcriptions set that defines the population in any uveitis. Further concerns include that the validation data set is not the same population, but rather a subset not containing CD14.

We agree with the reviewer and have changed this in the result section to “substantiates this gene set as a robust and bona fide transcriptional feature of CD1c+ DCs in human non-infectious uveitis” at page 13. We agree that - as expected - the removal of CD14+ cells impacted the sensitivity of our analysis, but that this strategy was required to attribute the black module to CD1c+ DCs. Our data supports that the black module gene signature is not restricted to CD14+ CD1c+ DCs by demonstrating that its dysregulation in non-infectious uveitis can even be perceived in CD14- CD1c+ DCs. We show now that the replication of a fraction of genes of the black module is a consequence of sensitivity to detect differentially expressed genes (Figure 2 – Supplement 1C). – most likely due to lower cell number after sorting out CD14+ cells. We have outlined this in greater detail in the result section on page 13. We hope the reviewer agrees this has now been adequately described.

Line 220: Notch-dll experiments: with the experiments presented it is not possible to say that the changes are due to maintenance of CD1c+ DCs without further experiments outlining what NOTCH2 signaling changes throughout time. Is the population fully developed in the first 7 days of culture prior to adding NOTCH2 or ADAM10 inhibitors? Is there more apoptosis in this pathway? Less proliferation? It would be more accurate to say that there are fewer cDC2s after 14 days of culture without speculating the cause. In this experiment it is unclear why the gate of CD141/CD1c was chosen, as this appears to be in the middle of the population. In normal PBMCs CD141+ DCs would be CD1c negative; therefore why exclude the CD141hiCD1c+ and CD141loCD1c+ populations?

We agree with the reviewer that in the current state the additional Notch-DLL experiments are inconclusive. Based on the comments from this reviewer, we believe the most appropriate experiments would be to show changes in the surface protein expression of CD36, CX3CR1 and other key surface markers of the black module upon inhibition of NOTCH2 or ADAM10. To this end, we repeated the experiments with human CD34+ HPC-derived DCs cells to measure cell subset by flow cytometry using the same panel we used for the PBMCs. However, we experienced substantial autofluorescence of human CD34-HPC derived cultures (expected for the complex heterogeneous cellularity of these cultures and as previously reported for CD34+ cells (Donnenberg et al., Methods 2015) that introduced significant artifacts and interfere with optimal identification of CD1c+ DCs and their subsets (see example below). We were unable to control for this so far, unfortunately. Since we agree with the reviewer that in the current form the supplemental figure does not significantly contribute to the manuscript, we removed the supplemental figure entirely from the manuscript. We hope the reviewer agrees that we already provide several complementary lines of evidence that link NOTCH-RUNX3 signaling to the black module (Figure 3A-D), including RNA-seq data from NOTCH2-DLL experiments, and that the current data is sufficient to support the main conclusions of the manuscript. We hope the reviewer agrees with this proposal.

Author response figure 1: Manual gating example of human CD34-HPC derived DCs shows substantial autofluorescence.

Line 256: The hypothesis that the loss of CD36+CX3CR1+ cells was due to migration to the eye doesn't make sense based on volume and number of cells. 0.1% of all PBMC is ~1x107 cells, and distributed throughout the eye would give about 1.3x106 cells/mL of eye volume. This would make the eye turbid which is not consistent with birdshot chorioretinopathy and would be rare in HLA-B27 anterior uveitis and intermediate uveitis

We agree with the reviewer and have changed this in the manuscript section to “We speculated that the decrease in blood CD36+CX3CR1+ CD1c+ DCs was in part the result of migration of these cells to peripheral tissues (lymph nodes) and that these cells may also infiltrate the eye during active uveitis.” On page 17.

Line 267: Would have liked to see the gating of CX3CR1/CD36 cells be more consistent (there are overlapping CX3CR1+ and CX3CR1- populations in 5A, but in Figure 4 quadrants were used to define the populations when evaluating the numbers in uveitis and healthy controls. The populations in Figure 5 are more separated by CD36.

We agree with the reviewer and have added a more detailed example of the gating strategy used to sort CD36/CX3CR1 subsets in Figure 5 – Supplement 1 including the expression of CX3CR1 and CD36 in the sorted populations.

Line 269, IN VITRO stimulation: The experimental paradigm is set up to find a difference between cells but does not to test any biologically relevant scenario. By sorting on a surface marker, then stimulating with the ligand for that receptor, the result better proves that CD36 is important in TLR2 signaling than does it give any information on how these dendritic cells might behave in uveitis.

We agree with the reviewer that the connection between the cytokine expression of the CD1c+ subsets and non-infectious uveitis may benefit from additional experimental data. To this end, we profiled available eye fluid biopsies and paired plasma by Olink proteomics to measure 92 immune mediators from patients and controls from this study (and several additional samples, including aqueous humor from non-inflammatory cataract controls – see revised Figure 5 panel D). This analysis shows that cytokines produced by CD36+CX3CR1+ DCs such as TNF-alpha and IL-6 are specifically increased in eye tissue of patients, but not in blood. We hope the reviewer agrees that we have provided additional experimental data that links the functional differences in DC subsets to cytokines implicated in the pathogenesis of non-infectious uveitis.

Reviewer #3 (Public Review):

First, a note on nomenclature. The authors use the term 'auto-immune' uveitis to encapsulate three different conditions -- HLA-B27 anterior uveitis, idiopathic intermediate uveitis, and birdshot choroidopathy. While I would agree with this terminology for the third set, there is substantial controversy as to whether HLA-B27 is truly autoimmune or autoinflammatory. Indeed, one major hypothesis is that this condition is driven by changes in gut microbiome. Intermediate uveitis is even more problematic; a substantial number of cases of this condition will turn out to be associated with demyelinating disease, which has recently been linked to Epstein Barr virus disease. To my knowledge in none of these diseases has a definitive autoantigen been identified nor passive transfer via transfusion shown; I would suggest the authors abandon this terminology and simply refer to the conditions as they are called.

We would like to thank the reviewer for the constructive suggestions. We agree and have changed the term “autoimmune uveitis” to “non-infectious uveitis” throughout the manuscript.

Further, it would have been very desirable to compare the DC transcriptome for the other class of uveitic disease -- infectious -- for acute retinal necrosis or similar. As well it would have been very useful to compare profiles to other, related immune-mediated diseases such as ankylosing spondylitis.

We agree with the reviewer that comparison of DC transcriptomes is useful for interpretation of biological mechanisms involved. This is precisely the reason we use (in Figure 3) comparison of our DC transcriptomic data to well-controlled transgenic models and DC culture systems. This revealed NOTCH2-RUNX3 signaling driving the uveitis-associated CD1c+ DC signature. We have now included transcriptomic data from CD1c+ DC subsets of type I IFN diseases SLE and Systemic Sclerosis in Figure 2. Although we agree that comparison to infectious uveitis would be interesting, bulk RNA-seq data from CD1c+ DCs are – to the best of our knowledge – unfortunately not available.

Finally, it must be noted that looking for systemic signals in dendritic gene expression may be a bit of a needle in the haystack approach. Presumably, the function of the dendritic cells in uveitis is largely centered on those cells in the eye. It would have been highly desirable to examine the expression profile of intraocular DCs in at least a subset of patients who may have come to surgery (for instance, steroid implantation or vitrectomy).

We agree with the reviewer that analysis of blood requires enormous efforts and controls to dissect disease-relevant changes in gene profiles of cDC2 subsets. We therefore designed a strategy that focusses on replication of gene modules, use independent cohorts, and complementary immunophenotyping technologies to detect key changes in specific subsets of CD1c+ DCs in uveitis patients. To further extend these analyses, we have now also detailed our analysis of intraocular DCs using single-cell RNA seq of eye fluid biopsies (aqueous humor) of HLA-B27 anterior uveitis (identical to our “AU” group of patients). As shown in revised Figure 6, we detected eye-infiltrating CD1c+ DCs and were able to cluster cells positive for the uveitis-associated black module (revised Figure 6B), which showed – as expected - that “black-module+” CD1c+ DCs show higher expression for CD36, CX3CR1, and lower RUNX3, but not CD14 (revised Figure 6C)– closely corroborating our blood CD1c+ DC analyses. These DC3s were also found at higher frequency in the eye of patients with AU (Figure 6D). We hope the reviewer agrees we have sustainably improved the analysis of intraocular DCs and that this has now been sufficiently addressed.

It is also problematic that no effort has been made to assess the severity of uveitis. Flares of disease can range from extremely mild to debilitating. Similarly, intermediate uveitis and BSCR can range greatly in severity. Without normalizing for disease severity it is difficult to fully understand the range of transcriptional changes between cases.

In our view, a key limitation in determination of uveitis severity for molecular analysis is the fact that objective biomarkers that assess disease severity across uveitis entities are lacking. Currently, disease severity is dependent an array of clinical features (i.e, SUN criteria) which cannot be applied consistently to anterior, intermediate and posterior uveitis. For example, the severity of anterior uveitis is in part assessed by grading of inflammation in the anterior chamber, while the anterior chamber is (typically) not involved in Birdshot Uveitis (BU in this study). However, to allow the study of patients with high disease activity, we exclusively used systemic treatment-free patients that all had active uveitis at sampling at our academic institute, making the results highly relevant for understanding the pathophysiology of non-infectious uveitis. For this reviewer’s convenience, we have conducted additional analysis that includes key clinical parameters (anterior chamber cells, vitreous cells, and macular thickness for patients from cohort I). These data showed no clear clustering of patients based on any of the clinical parameters (revised Figure 1 -Supplement 2). We hope the reviewer agrees this has been addressed in sufficient detail.

The use of principal component analysis for clustering may be underpowered; I would suggest the authors apply UMAP to determine if higher dimensional component analyses correlate with disease type.

Upon request of the reviewer, we have conducted UMAP (with different tuning of hyperparameters) on the DEGs (cohort I, see image below). We believe that UMAP analysis did not provide additional insights or correlates with disease type. We hope the reviewer agrees.

The false-discovery rate in large transcriptomic projects is challenging. While the authors are to be commended for employing a validation set, it would be useful to employ a Monte Carlo simulation in which groups are arbitrarily relabeled to determine the number of expected false discoveries within this data set (i.e. akin to Significance Analysis of Microarray techniques).

We determined the adjusted P values via the DESeq2 package (for false-discovery rate of 5% and Benjamini-Hochberg Procedure). The results are shown in Supplemental File 1K-1M and analysis in Figure 1A.

I do not fully understand the significance of the mouse CD11c-Runx3delta mice. It appears these data were derived from previous datasets or from bone marrow stromal line cultures. Did the authors attempt to generate autoimmune uveitis (i.e. EAU) in these animals? Without this the relevance for uveitis is unclear.

We did not attempt to induce experimental autoimmune uveitis in CD11c-Runx3delta mice. We used transcriptomic data from dendritic cells purified from this model to show that loss of RUNX3 induces a gene signature highly reminiscent of the gene module identified in non-infectious uveitis patients. Using enrichment analysis, we show that the transcriptome of patients is highly enriched for this signature which indicates that the decreased RUNX3 observed in patients underlies the upregulation of CD36, CX3CR1 and other surface genes. In other words, we used data from transgenic models to dissect which of the altered transcription factors were driving this gene module and we identified the RUNX3-NOTCH2 axis as an important contributor.

Author Response

We thank the reviewers for their positive feedback and thoughtful suggestions that will improve our manuscript. Here we summarise our plan for immediate action. We will resubmit our manuscript once additional experiments have been performed to clarify all the major and minor concerns of the reviewers and the manuscript has been revised. At that point, we will respond to all reviewer’s points and highlight the changes made in the text.

Reviewer #1 (Public Review):

The authors have tried to correlate changes in the cellular environment by means of altering temperature, the expression of key cellular factors involved in the viral replication cycle, and small molecules known to affect key viral protein-protein interactions with some physical properties of the liquid condensates of viral origin. The ideas and experiments are extremely interesting as they provide a framework to study viral replication and assembly from a thermodynamic point of view in live cells.

The major strengths of this article are the extremely thoughtful and detailed experimental approach; although this data collection and analysis are most likely extremely time-consuming, the techniques used here are so simple that the main goal and idea of the article become elegant. A second major strength is that in other to understand some of the physicochemical properties of the viral liquid inclusion, they used stimuli that have been very well studied, and thus one can really focus on a relatively easy interpretation of most of the data presented here.

There are three major weaknesses in this article. The way it is written, especially at the beginning, is extremely confusing. First, I would suggest authors should check and review extensively for improvements to the use of English. In particular, the abstract and introduction are extremely hard to understand. Second, in the abstract and introduction, the authors use terms such as "hardening", "perturbing the type/strength of interactions", "stabilization", and "material properties", for just citing some terms. It is clear that the authors do know exactly what they are referring to, but the definitions come so late in the text that it all becomes confusing. The second major weakness is that there is a lack of deep discussion of the physical meaning of some of the measured parameters like "C dense vs inclusion", and "nuclear density and supersaturation". There is a need to explain further the physical consequences of all the graphs. Most of them are discussed in a very superficial manner. The third major weakness is a lack of analysis of phase separations. Some of their data suggest phase transition and/or phase separation, thus, a more in-deep analysis is required. For example, could they calculate the change of entropy and enthalpy of some of these processes? Could they find some boundaries for these transitions between the "hard" (whatever that means) and the liquid?

The authors have achieved almost all their goals, with the caveat of the third weakness I mentioned before. Their work presented in this article is of significant interest and can become extremely important if a more detailed analysis of the thermodynamics parameters is assessed and a better description of the physical phenomenon is provided.

We thank reviewer 1 for the comments and, in particular, for being so positive regarding the strengths of our manuscript and for raising concerns that will surely improve the manuscript. At this point, we propose the following actions to address the concerns of Reviewer 1:

1) We will extensively revise the use of English, particularly, in the abstract and introduction, defining key terms as they come along in the text to make the argument clearer.

2) We acknowledge the importance of discussing our data in more detail and we propose the following. We will discuss the graphs and what they mean as exemplified in the paragraph below.

Regarding Figure 3 - As the concentration of vRNPs increases, we observe an increase in supersaturation until 12hpi. This means that contrary to what is observed in a binary mixture, in which the Cdilute is constant (Klosin et al., 2020), the Cdilute in our system increases with concentration. It has been reported that Cdilute increases in a multi-component system with bulk concentration (Riback et al., 2020). Our findings have important implications for how we think about the condensates formed during influenza infection. As the 8 different genomic vRNPs have a similar overall structure, they could, in theory, behave as a binary system between units of vRNPs and Rab11a. However, a change in Cdilute with concentration shows that our system behaves as a multi-component system. This means that the differences in length, RNA sequence and valency that each vRNP have are key for the integrity of condensates.

3) The reviewer calls our attention to the lack of analysis of phase separations. We think that phase separation (or percolation coupled to phase separation) governs the formation of influenza A virus condensates. However, we think we ought to exert caution at this point as the condensates we are working with are very complex and that the physics of our system in cells may not be sufficient to claim phase separation without an in vitro reconstitution system. In fact, IAV inclusions contain cellular membranes, different vRNPs and Rab11a. So far, we can only speculate that the liquid character of IAV inclusions may arise from a network of interacting vRNPs that bridge several cognate vRNP-Rab11 units on flexible membranes, similarly to what happens in phase separated vesicles in neurological synapses. However, the speculative model for our system, although being supported by correlative light and electron microscopy, currently lacks formal experimental validation.

For this reason, we thought of developing the current work as an alternative to explore the importance of the liquid material properties of IAV inclusions. By finding an efficient method to alter the material properties of IAV inclusions, we provide proof of principle that it is possible to impose controlled phase transitions that reduce the dynamics of vRNPs in cells and negatively impact progeny virion production. Despite having discussed these issues in the limitations of the study, we will make our point clearer.

We are currently establishing an in vitro reconstitution system to formally demonstrate, in an independent publication, that IAV inclusions are formed by phase separation. For this future work, we teamed up with Pablo Sartori, a theorical physicist to derive in- depth analysis of the thermodynamics of the viral liquid condensates. Collectively, we think that cells have too many variables to derive meaningful physics parameters (such as entropy and enthalpy) as well as models and need to be complemented by in vitro systems. For example, increasing the concentration inside a cell is not a simple endeavour as it relies on cellular pathways to deliver material to a specific place. At the same time, the 8 vRNPs, as mentioned above, have different size, valency and RNA sequence and can behave very differently in the formation of condensates and maintenance of their material properties. Ideally, they should be analysed individually or in selected combinations. For the future, we will combine data from in vitro reconstitution systems and cells to address this very important point raised by the reviewer.

From the paper on the section Limitations of the study: “Understanding condensate biology in living cells is physiologically relevant but complex because the systems are heterotypic and away from equilibria. This is especially challenging for influenza A liquid inclusions that are formed by 8 different vRNP complexes, which although sharing the same structure, vary in length, valency, and RNA sequence. In addition, liquid inclusions result from an incompletely understood interactome where vRNPs engage in multiple and distinct intersegment interactions bridging cognate vRNP-Rab11 units on flexible membranes (Chou et al., 2013; Gavazzi et al., 2013; Haralampiev et al., 2020; Le Sage et al., 2020; Shafiuddin & Boon, 2019; Sugita, Sagara, Noda, & Kawaoka, 2013). At present, we lack an in vitro reconstitution system to understand the underlying mechanism governing demixing of vRNP-Rab11a-host membranes from the cytosol. This in vitro system would be useful to explore how the different segments independently modulate the material properties of inclusions, explore if condensates are sites of IAV genome assembly, determine thermodynamic values, thresholds accurately, perform rheological measurements for viscosity and elasticity and validate our findings”.

Reviewer #2 (Public Review):

During Influenza virus infection, newly synthesized viral ribonucleoproteins (vRNPs) form cytosolic condensates, postulated as viral genome assembly sites and having liquid properties. vRNP accumulation in liquid viral inclusions requires its association with the cellular protein Rab11a directly via the viral polymerase subunit PB2. Etibor et al. investigate and compare the contributions of entropy, concentration, and valency/strength/type of interactions, on the properties of the vRNP condensates. For this, they subjected infected cells to the following perturbations: temperature variation (4, 37, and 42{degree sign}C), the concentration of viral inclusion drivers (vRNPs and Rab11a), and the number or strength of interactions between vRNPs using nucleozin a well-characterized vRNP sticker. Lowering the temperature (i.e. decreasing the entropic contribution) leads to a mild growth of condensates that does not significantly impact their stability. Altering the concentration of drivers of IAV inclusions impact their size but not their material properties. The most spectacular effect on condensates was observed using nucleozin. The drug dramatically stabilizes vRNP inclusions acting as a condensate hardener. Using a mouse model of influenza infection, the authors provide evidence that the activity of nucleozin is retained in vivo. Finally, using a mass spectrometry approach, they show that the drug affects vRNP solubility in a Rab11a-dependent manner without altering the host proteome profile.

The data are compelling and support the idea that drugs that affect the material properties of viral condensates could constitute a new family of antiviral molecules as already described for the respiratory syncytial virus (Risso Ballester et al. Nature. 2021).

Nevertheless, there are some limitations in the study. Several of them are mentioned in a dedicated paragraph at the end of a discussion. This includes the heterogeneity of the system (vRNP of different sizes, interactions between viral and cellular partners far from being understood), which is far from equilibrium, and the absence of minimal in vitro systems that would be useful to further characterize the thermodynamic and the material properties of the condensates.

We thank reviewer 2 for highlighting specific details that need improving and raising such interesting questions to validate our findings. We will address all the minor comments of Reviewer 2. To address the comments of Reviewer 2, we propose the actions described in blue below each point raised that is written in italics.

1) The concentrations are mostly evaluated using antibodies. This may be correct for Cdilute. However, measurement of Cdense should be viewed with caution as the antibodies may have some difficulty accessing the inner of the condensates (as already shown in other systems), and this access may depend on some condensate properties (which may evolve along the infection). This might induce artifactual trends in some graphs (as seen in panel 2c), which could, in turn, affect the calculation of some thermodynamic parameters.

The concern of using antibodies to calculate Cdense is valid. We will address this concern by validating our results using a fluorescent tagged virus that has mNeon Green fused to the viral polymerase PA (PA-mNeonGreen PR8 virus). Like NP, PA is a component of vRNPs and labels viral inclusions, colocalising with Rab11 when vRNPs are in the cytosol without the need of using antibodies.

This virus would be the best to evaluate inclusion thermodynamics, where it not an attenuated virus (Figure 1A below) with a delayed infection as demonstrated by the reduced levels of viral proteins (Figure 1B below). Consistently, it shows differences in the accumulation of vRNPs in the cytosol and viral inclusions form later in infection. After their emergence, inclusions behave as in the wild-type virus (PR8-WT), fusing and dividing (Figure 1C below) and displaying liquid properties. The differences in concentration may shift or alter thermodynamic parameters such as time of nucleation, nucleation density, inclusion maturation rate, Cdense, Cdilute. This is the reason why we performed the thermodynamics profiling using antibodies upon PR8-WT infection. For validating our results, and taking into account a possible delayed kinetics, and differenced that may occur because of reduced vRNP accumulation in the cytosol, this virus will be useful and therefore we will repeat the thermodynamics using it.

As a side note, vRNPs are composed of viral RNA coated with several molecules of NP and each vRNP also contains 1 copy of the trimeric RNA dependent RNA polymerase formed by PA, PB1 and PB2. It is well documented that in the cytosol the vast majority of PA (and other components of the polymerase) is in the form of vRNPs (Avilov, Moisy, Munier, et al., 2012; Avilov, Moisy, Naffakh, & Cusack, 2012; Bhagwat et al., 2020; Lakdawala et al., 2014), and thus we can use this virus to label vRNPs on condensates to corroborate our studies using antibodies.

Figure 1 – The PA- mNeonGreen virus is attenuated in comparison to the WT virus. A. Cells (A549) were infected or mock-infected with PR8 WT or PA- mNeonGreen (PA-mNG) viruses, at a multiplicity of infection (MOI) of 3, for the indicated times. Viral production was determined by plaque assay and plotted as plaque forming units (PFU) per milliliter (mL) ± standard error of the mean (SEM). Data are a pool from 2 independent experiments. B. The levels of viral PA, NP and M2 proteins and actin in cell lysates at the indicated time points were determined by western blotting. C. Cells (A549) were transfected with a plasmid encoding mCherry-NP and co-infected with PA-mNeonGreen virus for 16h, at an MOI of 10. Cells were imaged under time-lapse conditions starting at 16 hpi. White boxes highlight vRNPs/viral inclusions in the cytoplasm in the individual frames. The dashed white and yellow lines mark the cell nucleus and the cell periphery, respectively. The yellow arrows indicate the fission/fusion events and movement of vRNPs/ viral inclusions. Bar = 10 µm. Bar in insets = 2 µm.

2) Although the authors have demonstrated that vRNP condensates exhibit several key characteristics of liquid condensates (they fuse and divide, they dissolve upon hypotonic shock or upon incubation with 1,6-hexanediol, FRAP experiments are consistent with a liquid nature), their aspect ratio (with a median above 1.4) is much higher than the aspect ratio observed for other cellular or viral liquid compartments. This is intriguing and might be discussed.

IAV inclusions have been shown to interact with microtubules and the endoplasmic reticulum, that confers movement, and also undergo fusion and fission events. We propose that these interactions and movement impose strength and deform inclusions making them less spherical. To validate this assumption, we compared the aspect ratio of viral inclusions in the absence and presence of nocodazole (that abrogates microtubule-based movement). The data in figure 2 shows that in the presence of nocodazole, the aspect ratio decreases from 1.42±0.36 to 1.26 ±0.17, supporting our assumption.

Figure 2 – Treatment with nocodazole reduces the aspect ratio of influenza A virus inclusions. Cells (A549) were infected PR8 WT and treated with nocodazole (10 µg/mL) for 2h time after which the movement of influenza A virus inclusions was captured by live cell imaging. Viral inclusions were segmented, and the aspect ratio measured by imageJ, analysed and plotted in R.

3) Similarly, the fusion event presented at the bottom of figure 3I is dubious. It might as well be an aggregation of condensates without fusion.

We will change this, thank you for the suggestion.

4) The authors could have more systematically performed FRAP/FLAPh experiments on cells expressing fluorescent versions of both NP and Rab11a to investigate the influence of condensate size, time after infection, or global concentrations of Rab11a in the cell (using the total fluorescence of overexpressed GFP-Rab11a as a proxy) on condensate properties.

We will try our best to be able to comply with this suggestion as we think it is important.

Reviewer #3 (Public Review):

This study aims to define the factors that regulate the material properties of the viral inclusion bodies of influenza A virus (IAV). In a cellular model, it shows that the material properties were not affected by lowering the temperature nor by altering the concentration of the factors that drive their formation. Impressively, the study shows that IAV inclusions may be hardened by targeting vRNP interactions via the known pharmacological modulator (also an IAV antiviral), nucleozin, both in vitro and in vivo. The study employs current state-of-the-art methodology in both influenza virology and condensate biology, and the conclusions are well-supported by data and proper data analysis. This study is an important starting point for understanding how to pharmacologically modulate the material properties of IAV viral inclusion bodies.

We thank this reviewer for all the positive comments. We will address the minor issues brought to our attention entirely, including changing the tittle of the manuscript and we will investigate the formation and material properties of IAV inclusions in the presence and absence of nucleozin for the nucleozin escape mutant NP-Y289H.

References

Avilov, S. V., Moisy, D., Munier, S., Schraidt, O., Naffakh, N., & Cusack, S. (2012). Replication- competent influenza A virus that encodes a split-green fluorescent protein-tagged PB2 polymerase subunit allows live-cell imaging of the virus life cycle. J Virol, 86(3), 1433- 1448. doi:10.1128/JVI.05820-11

Avilov, S. V., Moisy, D., Naffakh, N., & Cusack, S. (2012). Influenza A virus progeny vRNP trafficking in live infected cells studied with the virus-encoded fluorescently tagged PB2 protein. Vaccine, 30(51), 7411-7417. doi:10.1016/j.vaccine.2012.09.077

Bhagwat, A. R., Le Sage, V., Nturibi, E., Kulej, K., Jones, J., Guo, M., . . . Lakdawala, S. S. (2020). Quantitative live cell imaging reveals influenza virus manipulation of Rab11A transport through reduced dynein association. Nat Commun, 11(1), 23. doi:10.1038/s41467-019-13838-3

Chou, Y. Y., Heaton, N. S., Gao, Q., Palese, P., Singer, R. H., & Lionnet, T. (2013). Colocalization of different influenza viral RNA segments in the cytoplasm before viral budding as shown by single-molecule sensitivity FISH analysis. PLoS Pathog, 9(5), e1003358. doi:10.1371/journal.ppat.1003358

Gavazzi, C., Yver, M., Isel, C., Smyth, R. P., Rosa-Calatrava, M., Lina, B., . . . Marquet, R. (2013). A functional sequence-specific interaction between influenza A virus genomic RNA segments. Proc Natl Acad Sci U S A, 110(41), 16604-16609. doi:10.1073/pnas.1314419110

Haralampiev, I., Prisner, S., Nitzan, M., Schade, M., Jolmes, F., Schreiber, M., . . . Herrmann, A. (2020). Selective flexible packaging pathways of the segmented genome of influenza A virus. Nat Commun, 11(1), 4355. doi:10.1038/s41467-020-18108-1

Klosin, A., Oltsch, F., Harmon, T., Honigmann, A., Julicher, F., Hyman, A. A., & Zechner, C. (2020). Phase separation provides a mechanism to reduce noise in cells. Science, 367(6476), 464-468. doi:10.1126/science.aav6691

Lakdawala, S. S., Wu, Y., Wawrzusin, P., Kabat, J., Broadbent, A. J., Lamirande, E. W., . . . Subbarao, K. (2014). Influenza a virus assembly intermediates fuse in the cytoplasm. PLoS Pathog, 10(3), e1003971. doi:10.1371/journal.ppat.1003971

Le Sage, V., Kanarek, J. P., Snyder, D. J., Cooper, V. S., Lakdawala, S. S., & Lee, N. (2020). Mapping of Influenza Virus RNA-RNA Interactions Reveals a Flexible Network. Cell Rep, 31(13), 107823. doi:10.1016/j.celrep.2020.107823

Riback, J. A., Zhu, L., Ferrolino, M. C., Tolbert, M., Mitrea, D. M., Sanders, D. W., . . . Brangwynne, C. P. (2020). Composition-dependent thermodynamics of intracellular phase separation. Nature, 581(7807), 209-214. doi:10.1038/s41586-020-2256-2

Shafiuddin, M., & Boon, A. C. M. (2019). RNA Sequence Features Are at the Core of Influenza a Virus Genome Packaging. J Mol Biol. doi:10.1016/j.jmb.2019.03.018

Sugita, Y., Sagara, H., Noda, T., & Kawaoka, Y. (2013). Configuration of viral ribonucleoprotein complexes within the influenza A virion. J Virol, 87(23), 12879- 12884. doi:10.1128/JVI.02096-13

Author Response

Reviewer #1 (Public Review):

The authors have tried to correlate changes in the cellular environment by means of altering temperature, the expression of key cellular factors involved in the viral replication cycle, and small molecules known to affect key viral protein-protein interactions with some physical properties of the liquid condensates of viral origin. The ideas and experiments are extremely interesting as they provide a framework to study viral replication and assembly from a thermodynamic point of view in live cells.

The major strengths of this article are the extremely thoughtful and detailed experimental approach; although this data collection and analysis are most likely extremely time-consuming, the techniques used here are so simple that the main goal and idea of the article become elegant. A second major strength is that in other to understand some of the physicochemical properties of the viral liquid inclusion, they used stimuli that have been very well studied, and thus one can really focus on a relatively easy interpretation of most of the data presented here.

There are three major weaknesses in this article. The way it is written, especially at the beginning, is extremely confusing. First, I would suggest authors should check and review extensively for improvements to the use of English. In particular, the abstract and introduction are extremely hard to understand. Second, in the abstract and introduction, the authors use terms such as "hardening", "perturbing the type/strength of interactions", "stabilization", and "material properties", for just citing some terms. It is clear that the authors do know exactly what they are referring to, but the definitions come so late in the text that it all becomes confusing. The second major weakness is that there is a lack of deep discussion of the physical meaning of some of the measured parameters like "C dense vs inclusion", and "nuclear density and supersaturation". There is a need to explain further the physical consequences of all the graphs. Most of them are discussed in a very superficial manner. The third major weakness is a lack of analysis of phase separations. Some of their data suggest phase transition and/or phase separation, thus, a more in-deep analysis is required. For example, could they calculate the change of entropy and enthalpy of some of these processes? Could they find some boundaries for these transitions between the "hard" (whatever that means) and the liquid?

The authors have achieved almost all their goals, with the caveat of the third weakness I mentioned before. Their work presented in this article is of significant interest and can become extremely important if a more detailed analysis of the thermodynamics parameters is assessed and a better description of the physical phenomenon is provided.

We thank you for the comments and, in particular, for being so positive regarding the strengths of our manuscript and for raising concerns that will surely improve it. We have taken the following actions to address your concerns:

1) Extensive revisions have been made to the use of English, particularly in the abstract and introduction. Key terms are defined as they are introduced in the text to enhance the clarity of the argument. This is a significant revision that is highlighted within the text, but it is too extensive to detail here.

2) In the results section, we improved and extended the discussion of our graphs to the extent possible. However, we found that attempting to explain the graphs' meanings more thoroughly would detract from our manuscript's main focus: identifying thermodynamic changes that could potentially lead to alterations in material properties, specifically aspect ratio, size, and Gibbs free energy. As a result, we introduced the type of information we could obtain from our analyses in the introduction (Lines 112-125) and briefly commented on it in the ‘results’ section (Lines 304-306, sentences below).

From introduction – lines 112-125:

“In addition, other parameters like nucleation density determine how many viral condensates are formed per area of cytosol. Overall, the data will inform us if changing one parameter, e.g. the concentration, drives the system towards larger condensates with the same or more stable properties, or more abundant condensates that are forced to maintain the initial or a different size on account of available nucleation centres (Riback et al., 2020:Snead, 2022 #1152). It will also inform us if liquid viral inclusions behave like a binary or a multi-component system. In a binary mixture, Cdilute is constant (Klosin et al., 2020). However, in multi-component systems, Cdilute increases with bulk concentration (Riback et al., 2020). This type of information could have direct implications about the condensates formed during influenza infection. As the 8 different genomic vRNPs have a similar overall structure, they could, in theory, behave as a binary system between units of vRNPs and Rab11a. However, a change in Cdilute with concentration would mean that the system behaves as a multi-component system. This could raise the hypothesis that the differences in length, RNA sequence and valency that each vRNP has may be relevant for the integrity and behaviour of condensates.”.

From results lines 304-306:

This indicates that the liquid inclusions behave as a multi-component system and allow us to speculate that the differences in length, RNA sequence and valency that each vRNP may be key for the integrity and behaviour of condensates.

3) The reviewer has drawn our attention to the absence of phase separation analysis in our study. We believe that the formation of influenza A virus condensates is governed by phase separation (or percolation coupled to phase separation). However, we must exercise caution at this point because the condensates we are studying are highly complex, and the physics of our cellular system may not be adequate to claim phase separation without being validated by an in vitro reconstitution system. IAV inclusions contain a variety of cellular membranes, different vRNPs, and Rab11a. While we have robust data to propose a model in which the liquid-like properties of IAV inclusions arise from a network of interacting vRNPs that bridge multiple cognate vRNP-Rab11 units on flexible membranes, similar to what occurs in phase-separated vesicles in neurological synapses, our model for this system still lacks formal experimental validation. As a note, the data supporting our model includes: the demonstration of the liquid properties of our liquid inclusions (Alenquer et al. 2019, Nature Communications, 10, 1629); and impairment of recycling endocytic activity during IAV infection Bhagwat et al. 2020, Nat Commun, 11, 23; Kawaguchi et al. 2012, J Virol, 86, 11086-95; Vale-costa et al. 2016, J Cell Sci, 129, 1697-710. This leads to aggregated vesicles seen by correlative light and electron microscopy (Vale-Costa et al., 2016 JCS, 129, 1697-710) and by immunofluorescence and FISH (Amorim et al. 2011,. J Virol 85, 4143-4156; Avilov et al. 2012, Vaccine 30, 7411-7417; Chou et al. 2013, PLoS Pathog 9, e1003358; Eisfeld et al. 2011, J Virol 85, 6117-6126 and Lakdawala et al. 2014, PLoS Pathog 10, e1003971.

To be able to explore the significance of the liquid material properties of IAV inclusions, we used the strategy described in this current work. By developing an effective method to manipulate the material properties of IAV inclusions, we provide evidence that controlled phase transitions can be induced, resulting in decreased vRNP dynamics in cells and a negative impact on progeny virion production. This suggests that the liquid character of liquid inclusions is important for their function in IAV infection. We have improved our explanation addressing this concern in the limitations of our study (as outlined below in the box and in manuscript in lines 857-872).

We are currently establishing an in vitro reconstitution system to formally demonstrate, in an independent publication, that IAV inclusions are formed by phase separation (or percolation coupled to phase separation). For this future work, we teamed up with Pablo Sartori, a theorical physicist to derive in-depth analysis of the thermodynamics of the viral liquid condensates in the in vitro reconstituted system and compare it to results obtained in the cell. This will provide means to establish comparisons. We think that cells have too many variables to derive meaningful physics parameters (such as entropy and enthalpy) and models that need to be complemented by in vitro systems. For example, increasing the concentration inside a cell is not a simple endeavour as it relies on cellular pathways to deliver material to a specific place. At the same time, the 8 vRNPs, as mentioned above, have different size, valency and RNA sequence and can behave very differently in the formation of condensates and maintenance of their material properties. Ideally, they should be analysed individually or in selected combinations. For the future, we will combine data from in vitro reconstitution systems and cells to address this very important point raised by the reviewer.

From the paper on the section ‘Limitations of the study’:

“Understanding condensate biology in living cells is physiological relevant but complex because the systems are heterotypic and away from equilibria. This is especially challenging for influenza A liquid inclusions that are formed by 8 different vRNP complexes, which although sharing the same structure, vary in length, valency, and RNA sequence. In addition, liquid inclusions result from an incompletely understood interactome where vRNPs engage in multiple and distinct intersegment interactions bridging cognate vRNP-Rab11 units on flexible membranes (Chou et al., 2013, Gavazzi et al., 2013, Sugita et al., 2013, Shafiuddin and Boon, 2019, Haralampiev et al., 2020, Le Sage et al., 2020). At present, we lack an in vitro reconstitution system to understand the underlying mechanism governing demixing of vRNP-Rab11a-host membranes from the cytosol. This in vitro system would be useful to explore how the different segments independently modulate the material properties of inclusions, explore if condensates are sites of IAV genome assembly, determine thermodynamic values, thresholds accurately, perform rheological measurements for viscosity and elasticity and validate our findings. The results could be compared to those obtained in cell systems to derive thermodynamic principles happening in a complex system away from equilibrium. Using cells to map how liquid inclusions respond to different perturbations provide the answer of how the system adapts in vivo, but has limitations.

Reviewer #2 (Public Review):

During Influenza virus infection, newly synthesized viral ribonucleoproteins (vRNPs) form cytosolic condensates, postulated as viral genome assembly sites and having liquid properties. vRNP accumulation in liquid viral inclusions requires its association with the cellular protein Rab11a directly via the viral polymerase subunit PB2. Etibor et al. investigate and compare the contributions of entropy, concentration, and valency/strength/type of interactions, on the properties of the vRNP condensates. For this, they subjected infected cells to the following perturbations: temperature variation (4, 37, and 42{degree sign}C), the concentration of viral inclusion drivers (vRNPs and Rab11a), and the number or strength of interactions between vRNPs using nucleozin a well-characterized vRNP sticker. Lowering the temperature (i.e. decreasing the entropic contribution) leads to a mild growth of condensates that does not significantly impact their stability. Altering the concentration of drivers of IAV inclusions impact their size but not their material properties. The most spectacular effect on condensates was observed using nucleozin. The drug dramatically stabilizes vRNP inclusions acting as a condensate hardener. Using a mouse model of influenza infection, the authors provide evidence that the activity of nucleozin is retained in vivo. Finally, using a mass spectrometry approach, they show that the drug affects vRNP solubility in a Rab11a-dependent manner without altering the host proteome profile

The data are compelling and support the idea that drugs that affect the material properties of viral condensates could constitute a new family of antiviral molecules as already described for the respiratory syncytial virus (Risso Ballester et al. Nature. 2021)

Nevertheless, there are some limitations in the study. Several of them are mentioned in a dedicated paragraph at the end of a discussion. This includes the heterogeneity of the system (vRNP of different sizes, interactions between viral and cellular partners far from being understood), which is far from equilibrium, and the absence of minimal in vitro systems that would be useful to further characterize the thermodynamic and the material properties of the condensates.

There are other ones.

We thank reviewer 2 for highlighting specific details that need improving and raising such interesting questions to validate our findings. We have addressed the comments of Reviewer 2, we performed the experiments as described (in blue) below each point raised.

1) The concentrations are mostly evaluated using antibodies. This may be correct for Cdilute. However, measurement of Cdense should be viewed with caution as the antibodies may have some difficulty accessing the inner of the condensates (as already shown in other systems), and this access may depend on some condensate properties (which may evolve along the infection). This might induce artifactual trends in some graphs (as seen in panel 2c), which could, in turn, affect the calculation of some thermodynamic parameters.

The concern of using antibodies to calculate Cdense is valid, and we thought it was very important. We addressed this concern by performing the same analyses using a fluorescent tagged virus that has mNeon Green fused to the viral polymerase PA (PA-mNeonGreen PR8 virus). Like NP, PA is a component of vRNPs and labels viral inclusions, colocalising with Rab11 when vRNPs are in the cytosol. However, per vRNP there is only one molecule of PA, whilst of NP there are 37-96 depending on the size of vRNPs. As predicted, we did observe changes in the Cdilute, Cdense and nucleation density. However, the measurements and values obtained for Gibbs free energy, size, aspect ratio detecting viral inclusions with fluorescently tagged vRNPs or antibody staining followed the same trend and allow us to validate our conclusion that major changes in Gibbs free energy occur solely when there is a change in the valency/strength of interactions but not in temperature or concentration (Figure 1 below). Given the extent of these data, we show here the results but, in the manuscript, we will describe the limitations of using antibodies in our study within the section ‘Limitations of the study’ from lines 881-894. Given the importance of the question regarding the pros and cons of the different systems for analysing thermodynamic parameters, we have decided to systematically assess and explore these differences in detail in a future manuscript.

For more information. This reviewer may be asking why we did not use the PA-fluorescent virus in the first place to evaluate inclusion thermodynamics and avoid problems in accessibility that antibodies may have to get deep into large inclusions. Our answer is that no system is perfect. In the case of the PA-fluorescent virus, the caveats revolve around the fact that the virus is attenuated (Figure 1a below), exhibiting a delayed infection as demonstrated by reduced levels of viral proteins (Figure 1b below). Consistently, it shows differences in the accumulation of vRNPs in the cytosol and viral inclusions form later in infection and the amount of vRNPs in the cytosol does not reach the levels observed in PR8-WT virus. After their emergence, inclusions behave as in the wild-type virus (PR8-WT), fusing and dividing (Figure 1c below) and displaying liquid properties.

As the overarching goal of this manuscript is to evaluate the best strategies to harden liquid IAV inclusions and given that one of the parameters we were testing is concentration, we reasoned that using PR8-WT virus for our analyses would be reasonable.

In conclusions, both systems have caveats that are important to systematically assess, and these differences may shift or alter thermodynamic parameters such as nucleation density, inclusion maturation rate, Cdense, Cdilute in particular by varying the total concentration. As a note, to validate all our results using the PA-mNeonGreen PR8 virus, we considered the delayed kinetics and applied our thermodynamic analyses up to 20 hpi rather than 16 hpi.

However, because of the question raised by this reviewer, on which is the best solution for mitigating errors induced by using antibodies, we re-checked all our data. Not only have we compared the data originated from attenuated fluorescently tagged virus with our data, but also made comparisons with images acquired from Z stacks (as used for concentration and for type/strength of interactions) with those acquired from 2D images. Our analysis revealed that there is a very good match using images acquired with Z-stacks and analysed as Z projections with between antibody staining and vRNP fluorescent virus. Therefore, we re-analysed all our thermodynamic data done with temperature using images acquired from Z stacks and altered entirely Figure 2. We believe that all these comparisons and analyses have greatly improved the manuscript and hence we thank all reviewers for their input.

Figure 1 – The PA-mNeonGreen virus is attenuated in comparison to the WT virus and data obtained is consistent for Gibbs free energy with analyses done with images processed with antibody fluorescent vRNPs. A. Representation of the PA-mNeonGreen virus (PA-mNG; Abbreviations: NCR: non coding region). B. Cells (A549) were transfected with a plasmid encoding mCherry-NP and co-infected with PA-mNeonGreen virus for 16h, at an MOI of 10. Cells were imaged under time-lapse conditions starting at 16 hpi. White boxes highlight vRNPs/viral inclusions in the cytoplasm in the individual frames. The dashed white and yellow lines mark the cell nucleus and the cell periphery, respectively. The yellow arrows indicate the fission/fusion events and movement of vRNPs/ viral inclusions. Bar = 10 µm. Bar in insets = 2 µm. C-D. Cells (A549) were infected or mock-infected with PR8 WT or PA-mNG viruses, at a multiplicity of infection (MOI) of 3, for the indicated times. C. Viral production was determined by plaque assay and plotted as plaque forming units (PFU) per milliliter (mL) ± standard error of the mean (SEM). Data are a pool from 2 independent experiments. D. The levels of viral PA, NP and M2 proteins and actin in cell lysates at the indicated time points were determined by western blotting. (E-G) Biophysical calculations in cells infected with the PA-mNeonGreen virus upon altering temperature (at 10 hpi, evaluating the concentration of vRNPs (over a time course) in conditions expressing native amounts of Rab11a or overexpressing low levels of Rab11a and upon altering the type/strength of vRNP interactions by adding nucleozin at 10 hpi during the indicated time periods. All data: Ccytoplasm/Cnucleus; Cdense, Cdilute, area aspect ratio and Gibbs free energy are represented as boxplots. Above each boxplot, same letters indicate no significant difference between them, while different letters indicate a statistical significance at α = 0.05 using one-way ANOVA, followed by Tukey multiple comparisons of means for parametric analysis, or Kruskal-Wallis Bonferroni treatment for non-parametric analysis.

2) Although the authors have demonstrated that vRNP condensates exhibit several key characteristics of liquid condensates (they fuse and divide, they dissolve upon hypotonic shock or upon incubation with 1,6-hexanediol, FRAP experiments are consistent with a liquid nature), their aspect ratio (with a median above 1.4) is much higher than the aspect ratio observed for other cellular or viral liquid compartments. This is intriguing and might be discussed.

IAV inclusions have been shown to interact with microtubules and the endoplasmic reticulum, that confers movement, and undergo fusion and fission events. We propose that these interactions and movement impose strength and deform inclusions making them less spherical. To validate this assumption, we compared the aspect ratio of viral inclusions in the absence and presence of nocodazole (that abrogates microtubule-based movement). The data in figure 2 shows that in the presence of nocodazole, the aspect ratio decreases from 1.42±0.36 to 1.26 ±0.17, supporting our assumption.

Figure 2 – Treatment with nocodazole reduces the aspect ratio of influenza A virus inclusions. Cells (A549) were infected with PR8 WT for 8 h and treated with nocodazole (10 µg/mL) for 2h, after which the movement of influenza A virus inclusions was captured by live cell imaging. Viral inclusions were segmented, and the aspect ratio measured by imageJ, analysed and plotted in R.

3) Similarly, the fusion event presented at the bottom of figure 3I is dubious. It might as well be an aggregation of condensates without fusion.

We have changed this (check Fig 5A and B in the manuscript), thank you for the suggestion.

4) The authors could have more systematically performed FRAP/FLAPh experiments on cells expressing fluorescent versions of both NP and Rab11a to investigate the influence of condensate size, time after infection, or global concentrations of Rab11a in the cell (using the total fluorescence of overexpressed GFP-Rab11a as a proxy) on condensate properties.

We have included a new figure, figure 5 with the suggested data.

Author Response

Reviewer #2 (Public Review):

1) The main limitation of this study is that the results are primarily descriptive in nature, and thus, do not provide mechanistic insight into how Ryr1 disease mutations lead to the muscle-specific changes observed in the EDL, soleus and EOM proteomes.

An intrinsic feature of the high-throughput proteomic analysis technology is the generation of lists of differentially expressed proteins (DEP) in different muscles from WT and mutated mice. Although the definition of mechanistic insights related to changes of dozens of proteins is very interesting, it is a difficult task to accomplish and goes beyond the goal of the high-throughput proteomic analysis presented here. Nevertheless, the analysis of DEPs may indeed provide arguments to speculate on the pathogenesis of the phenotype linked to recessive RyR1 mutations. In the unrevised manuscript, we pointed out that the fiber type I predominance observed in congenital myopathies linked to recessive Ryr1 mutation are consistent with the high expression level of heat shock proteins in slow twitch muscles. However, as suggested by Reviewer 3, we have removed "vague statements" from the text of the revised manuscript, concerning major insights into pathophysiological mechanisms, since we are aware that the mechanistic information, if any, that we can extract from the data set, cannot go over the intrinsic limitation of the high-throughput proteomic technology.

b) Results comparing fast twitch (EDL) and slow twitch (soleus) muscles from WT mice confirmed several known differences between the two muscle types. Similar analyses between EOM/EDL and EOM/soleus muscles from WT mice were not conducted.

We agree with the point raised by the Reviewer. In the revised manuscript we have changed Figure 2. The new Figure 2 shows the analysis of differentially expressed proteins in EDL, soleus and EOMs from WT mice. We have also added 2 new Tables (new Supplementary Table 2 and 3) and have inserted our findings in the revised Results section (page, 7, lines 157-176, pages 8 and 9).

c) While a reactome pathway analysis for proteins changes observed in EDL is shown in Supplemental Figure 1, the authors do not fully discuss the nature of the proteins and corresponding pathways impacted in the other two muscle groups analyzed.

We have now included in the revised manuscript a new Figure 2 which includes the Reactome pathway analysis comparing EDL with soleus, EDL with EOM and soleus with EOM (panels C, F and I, respectively). We have also inserted into the revised manuscript a brief description of the pathways showing the greatest changes in protein content (page 7 line 156-175, pages 8 and 9). We agree that the data showing changes in protein content between the 3 muscle groups of the WT mice are important also because they validate the results of the proteomic approach. Indeed, the present results confirm that many proteins including MyHCIIb, calsequestrin 1, SERCA1, parvalbumin etc are more abundantly expressed in fast twitch EDL muscles compared to soleus. Similarly, our results confirm that EOMs are enriched in MyHC-EO as well as cardiac isoforms of ECC proteins. This point has been clarified in the revised version of the manuscript (page 8, lines 198-213; page 9 lines 214-228). Nevertheless, we would like to point out that the main focus of our study is to compare the changes of protein content induced by the presence of recessive RyR1 mutations.

Reviewer #3 (Public Review):

a) it would be useful to determine whether changes in protein levels correlated with changes in mRNA levels …….

We performed qPCR analysis of Stac3 and Cacna1s in EDL, Soleus and EOM from WT mice (see Figure 1 below). The expression of transcripts encoding Cacna1s and Stac3 is approximately 9-fold higher in EDL compared to Soleus. The fold change of Stac3 and Cacna1s transcripts in EDL muscles is higher compared to the differences we observed by Mass spectrometry at the protein level between EDL and Soleus. Indeed, we found that the content of the Stac3 protein in EDL is 3-fold higher compared to that in soleus. Although there is no apparent linear correlation between mRNA and protein levels, we believe that a few plausible conclusions can be drawn, namely: (i) the expression level of both transcripts and proteins is higher EDL compared to EOM and soleus muscles, respectively, (ii) the expression level of transcripts encoding Stac3 correlate with those encoding Cacan1s and confirm proteomic data. In addition, the level of Stac3 transcript does not changes between WT and dHT, confirming our proteomic data which show that Stac3 protein content in muscles from dHT is similar to that found in WT littermates. Altogether these results support the concept that the differences in Stac3 content between EDL and soleus occur at both the protein and transcript levels, namely high Stac3 mRNA level correlates with higher protein content (EDL) and low mRNA levels correlated with low Stac3 protein content in Soleus muscles (see Figure 1 below).

Figure 2: qPCR of Cacna1s and Stac3 in muscles from WT mice. The expression levels of the transcripts encoding Cacna1s and Stac3 are the highest in EDL muscles and the lowest in soleus muscles (top panels). There are no significant changes in their relative expression levels in dHT vs WT. Each symbol represents the value from of a single mouse. * p=0.028 Mann Whitney test qPCR was performed as described in Elbaz et al., 2019 (Hum Mol Genet 28, 2987-2999).

….and whether or not the protein present was functional, and whether Stac3 was in fact stoichiometrically depleted in relation to Cacna1s.

We thought about this point but think that there are no plausible arguments to believe that Stac3 is not functional, one simple reason being that our WT mice do not have a phenotype which would be associated with the absence of Stac3 (Reinholt et al., PLoS One 8, e62760 2013, Nelson et al. Proc. Natl. Acad. Sci. USA 110:11881 2013).

b) In the abstract, the authors stated that skeletal muscle is responsible for voluntary movement. It is also responsible for non-voluntary. The abstract needs to be refocused on the mutation and on what we learn from this study. Please avoid vague statements like "we provide important insights to the pathophysiological mechanisms..." mainly when the study is descriptive and not mechanistic.

The abstract of the revised manuscript has been rewritten. In particular, we removed statements referring to important “pathophysiological mechanistic insight”.

c) The author should bring up the mutation name, location and phenotype early in the introduction.

In the revised manuscript we provide the information requested by the Reviewer (page 2 lines 36-38 and page 4, lines 98-102).

d) This reviewer also suggests that the authors refocus the introduction on the mutation location in the 3D RyR1 structure (available cryo-EM structure), if there is any nearby ligand binding site, protomers junction or any other known interacting protein partners. This will help the reader to understand how this mutation could be important for the channel's function

The residue Ala4329 is present inside the TMx (Auxiliary transmembrane helices) domain which spans from residue 4322 to 4370 and interposes structurally (des Georges A et al. 2016 Cell 167,145-57; Chen W, et al. 2020 EMBO Rep. 21, e49891). Although the structural resolution of the region has been improved (des Georges et al, 2016), parts of the domain still remain with no defined atomic coordinates, especially the region encompassing a.a. E4253 – F4540. Because of such undefined atomic coordinates of the region E4253-F4540, we are not able to determine the real orientation and the disposition of the amino acids in this region, including the A4329 residue. As reference, structure PDB: 5TAL of des Georges et al, 2016 was analyzed with UCSF Chimera (production version 1.16) (Pettersen et al. J. Comput. Chem. 25: 1605-1612. doi: 10.1002/jcc.20084).

Author Response

Reviewer #1 (Public Review):

The authors reveal dual regulatory activity of the complex nuclear receptor element (cNRE; contains hexads A+B+C) in cardiac chambers and its evolutionary origin using computational and molecular approaches. Building upon a previous observation that hexads A and B act as ventricular repressor sequences, in this study the authors identify a novel hexad C sequence with preferential atrial expression. The authors also reveal that the cNRE emerged from an endogenous viral element using comparative genomic approaches. The strength of this study is in a combination of in silico evolutionary analyses with in vivo transgenic assays in both zebrafish and mouse models. Rapid, transient expression assays in zebrafish together with assays using stable, transgenic mice demonstrate dual functionality of cNRE depending on the chamber context. This is especially intriguing given that the cNRE is present only in Galliformes and has originated likely through viral infection. Interestingly, there seem to be some species-specific differences between zebrafish and mouse models in expression response to mutations within the cNRE. Taken together, these findings bear significant implications for our understanding of dual regulatory elements in the evolutionary context of organ formation.

We thank reviewer 1 for the thorough review and are very satisfied with his favorable view of our manuscript. We also thank reviewer 1 for suggestions and opportunities to further clarify some relevant issues.

Reviewer #2 (Public Review):

Nunes Santos et al. investigated the gene regulatory activity of the promoter of the quail myosin gene, SMyHC III, that is expressed specifically in the atria of the heart in quails. To do so, they computationally identified a novel 6-bp sequence within the promoter that is putatively bound by a nuclear receptor transcription factor, and hence is a putative regulatory sequence. They tested this sequence for regulatory activity using transgenic assays in zebrafish and mice, and subjected this sequence to mutagenesis to investigate whether gene regulatory effects are abrogated. They define this sequence, together with two additional known 6-bp regulatory sequences, as a novel regulatory sequence (denoted cNRE) necessary and sufficient for driving atrial-specific expression of SMyHC III. This cNRE sequence is shared across several galliform species but appears to be absent in other avian species. The authors find that there is sequence homology between the cNRE and several virus genomes, and they conclude that this regulatory sequence arose in the quail genome by viral integration.

Strengths: The evolutionary origins of gene regulatory sequences and their impact on directing tissue-specific expression are of great interest to geneticists and evolutionary biologists. The authors of this paper attempt to bring this evolutionary perspective to the developmental biology question of how genes are differentially expressed in different chambers of the heart. The authors test for regulatory activity of the putative regulatory sequence they identified computationally in both zebrafish and mouse transgenic assays. The authors disrupt this sequence using deletions and mutagenesis, and introduce a tandem repeat of the sequence to a reporter gene to determine its consequences on chamber activity. These experiments demonstrate that the identified sequence has regulatory activity.

We appreciate the thorough review of our manuscript and are very stimulated by the reviewer’s understanding of the contents we presented. We will take the liberty to comment after the reviewer’s considerations, in the hope to better answer the relevant points.

Weaknesses: There are several decisions and assumptions that have been made by the authors, the reasons for which have not been articulated. Firstly, the rationale for the approach is not clear. The study is a follow-up to work previously performed by the authors which identified two 6-bp sequences important for controlling atrial-specific expression of the quail SMyHC III gene. This study appears to be motivated by the fact that these two sequences, bound by nuclear receptors, do not fully direct chamber-specific expression, and therefore this study aims to find additional regulatory sequences. It is assumed that any additional regulatory sequences should also be bound by nuclear receptors, and be 6-bp in length, and therefore the authors search for 6-bp sequences bound by nuclear receptors. It is not clear what the input sequence for this analysis was.

Thank you for giving us the opportunity to clarify our rational. Our approach is justified by the natural progression in the understanding of the mechanisms involved in preferential atrial expression by the SMyHC III promoter. The groundwork was solidly laid down by Wang and colleagues (see references as below). They mapped potential atrial stimulators and ventricular repressors throughout the SMyHC III promoter using atrial and ventricular cultures, respectively. Wang and colleagues pinned down the relevant regulators. First between -840 and -680 bp upstream from the transcription start site, then inside this nucleotide stretch, then in the 72-bp fragment contained between -840 and -680 bp, then identified the ventricular repressor in Hexads A and B inside the 72-bp sequence (see references below). We, in this manuscript, contributed with the identification of Hexad C (immediately downstream of Hexads A and B) as a potential nuclear receptor binding site and as a bona fide atrial activator. In summary, our work represents a logical conclusion of previous work by Wang and colleagues. We continued the process of narrowing down sequences previously proven to contain atrial activators (that were unknown before our present work) and ventricular repressors (that were already described).

Why did we use nuclear receptors as models for the putative cardiac chamber regulators binding to the cNRE? This is because previous work by Wang et al., 1996, 1998, 2001 and by Bruneau et al., 2001 showed that the 5’ portion of the cNRE (Hexads A and B) is indeed a hub for the integration of signals conveyed by nuclear receptors. Originally, Wang et al., 1996 showed that the VDR response element is a ventricular repressor acting via the 5’ portion of the cNRE. In a subsequent manuscript, Wang et al., 1998 showed that both RAR and VDR bind the 5’ portion of the cNRE. Bruneau et al., 2001 showed, by crossing IRX4 knockout mice with SMyHC III-HAP mice (Xavier-Neto et al., 1999), that IRX4 plays the role of a repressor of SMyHC III-HAP expression. Finally, Wang et al., 2001 showed that IRX4 interacts with RXR bound to the 5’ portion of the cNRE to inhibit ventricular expression.

Why was the 3’ Hexad included as a research subject? Very early on in our work it was noted that 3’ of the original VDR response element (Hexads A and B), described by Wang et al., 1996 and 1998 as a ventricular repressor, there was a sequence (Hexad C) with almost equal binding potential to nuclear receptors as Hexads A and B (as initially judged on the basis of comparisons with canonical nuclear receptor binding sequences, but later on confirmed by in silico profiling of nuclear receptor binding, see below). This discovery prompted us to design point mutants in the 3’ portion of the cNRE to investigate whether Hexad C contained relevant regulators of heart chamber expression. These analyses revealed a strong atrial activator in the mouse (the missing atrial activator from Wang et al., 1996, 1998, 2001).

Wang, G. F., Nikovits, W., Schleinitz, M., and Stockdale, F. E. (1996). Atrial chamber-specific expression of the slow myosin heavy chain 3 gene in the embryonic heart. J. Biol. Chem. 271, 19836-19845.

Wang, G. F., Nikovits, W. Jr., Schleinitz, M., and Stockdale, F. E. (1998). A positive GATA element and a negative vitamin D receptorlike element control atrial chamber-specific expression of a slow myosin heavy-chain gene during cardiac morphogenesis. Mol. Cell Biol. 18, 6023-6034.

Xavier-Neto, J., Neville, C. M., Shapiro, M. D., Houghton, L., Wang, G. F., Nikovits, W. Jr, Stockdale, F. E., and Rosenthal, N. (1999). A retinoic acid-inducible transgenic marker of sino-atrial development in the mouse heart. Development 126, 2677-2687.

Bruneau, B. G., Bao, Z. Z., Fatkin, D., Xavier-Neto, J., Georgakopoulos, D., Maguire, C. T., Berul, C. I., Kass, D. A., Kuroski-de Bold, M. L., de Bold, A. J., Conner, D. A., Rosenthal, N., Cepko, C. L., Seidman, C. E., and Seidman, J. G. (2001). Cardiomyopathy in Irx4-deficient mice is preceded by abnormal ventricular gene expression. Mol. Cell Biol. 21, 1730-1736.

Wang, G. F., Nikovits, W. Jr., Bao, Z.Z., and Stockdale, F.E. (2001). Irx4 forms an inhibitory complex with the vitamin D and retinoic X receptors to regulate cardiac chamber-specific slow MyHC3 expression. J Biol Chem. 276, 28835-28841.

The methods section mentions the cNRE sequence, but this is their newly defined regulatory sequence based on the newly identified 6-bp sequence. It is therefore unclear why Hexad C was identified to be of interest, and not the GATA binding site for example, and whether other sequences in the promoter might have stronger effects on driving atrial-specific expression.

As far as the existence of binding sites other than Hexads A, B, and C, we cannot, formally, exclude the possibility that there may be other relevant regulators of the SMyHC III gene. But we note that the sequences that we utilized were previously mapped through deletion mutant promoter approach by Wang et al., 1996 as the most powerful atrial activator(s) and ventricular repressor(s). We addressed these concerns in a new session entitled “Limitations of our work”.

Concerning GATA regulation, Wang et al., 1996, 1998 characterized a GATA-4 site that drives generalized (atrial and ventricular) cardiac expression in quail cultures. However, we were unable to identify any relevant changes in cardiac expression in mutant GATA SMyHC III-HAP transgenic mouse lines produced with the same mutated promoter sequences described by Wang et al., 1996, 1998.

Finding Hexad C as an atrial activator was an experimental finding. We identified it as such because we had two important inputs. First, in 1997, we consulted with Ralff Ribeiro, a specialist on nuclear receptors and he pointed out that downstream of the Hexad A + Hexad B VDRE/RARE (the ventricular repressor), there was a sequence with good potential for a nuclear receptor binding motif. This was exactly Hexad C. Then, we confirmed its potential for nuclear receptor binding by nuclear receptor profiling. After these two pieces of evidence, we thought that there was enough evidence to justify a mutant construct (Mut C). The experimental results we obtained in transgenic mice and zebrafish are consistent with the hypothesis that Hexad C does contain the long sought atrial activator predicted by Wang et al., 1996 in atrial cultures. This seems to be the most important atrial activator (a seven-fold activator) predicted by a deletion approach to be located between -840 and 680 bp in Wang et al., 1996.

Wang, G. F., Nikovits, W., Schleinitz, M., and Stockdale, F. E. (1996). Atrial chamber-specific expression of the slow myosin heavy chain 3 gene in the embryonic heart. J. Biol. Chem. 271, 19836-19845.

Wang, G. F., Nikovits, W. Jr., Schleinitz, M., and Stockdale, F. E. (1998). A positive GATA element and a negative vitamin D receptorlike element control atrial chamber-specific expression of a slow myosin heavy-chain gene during cardiac morphogenesis. Mol. Cell Biol. 18, 6023-6034.

Indeed, the zebrafish transgenic assays use the 32 bp cNRE, while in the mouse transgenic assays, a 72 bp region is used. This choice of sequence length is not justified.

As stated above, our rational was built as a continuation of the thorough work by Wang and colleagues in progressively narrowing down the location of relevant atrial stimulators and ventricular repressors. Throughout our work, we sought to obtain maximal coherence with previous studies (see references below) and to simultaneously probe cNRE function at an increased resolution. For that, we utilized previously described mutant SMyHC III promoter constructs (Wang et al., 1996) and introduced novel site-directed dinucleotide substitution mutants of individual Hexads in the SMyHC III promoter.

Wang, G. F., Nikovits, W., Schleinitz, M., and Stockdale, F. E. (1996). Atrial chamber-specific expression of the slow myosin heavy chain 3 gene in the embryonic heart. J. Biol. Chem. 271, 19836-19845.

Wang, G. F., Nikovits, W. Jr., Schleinitz, M., and Stockdale, F. E. (1998). A positive GATA element and a negative vitamin D receptorlike element control atrial chamber-specific expression of a slow myosin heavy-chain gene during cardiac morphogenesis. Mol. Cell Biol. 18, 6023-6034.

Xavier-Neto, J., Neville, C. M., Shapiro, M. D., Houghton, L., Wang, G. F., Nikovits, W. Jr, Stockdale, F. E., and Rosenthal, N. (1999). A retinoic acid-inducible transgenic marker of sino-atrial development in the mouse heart. Development 126, 2677-2687.

Bruneau, B. G., Bao, Z. Z., Fatkin, D., Xavier-Neto, J., Georgakopoulos, D., Maguire, C. T., Berul, C. I., Kass, D. A., Kuroski-de Bold, M. L., de Bold, A. J., Conner, D. A., Rosenthal, N., Cepko, C. L., Seidman, C. E., and Seidman, J. G. (2001). Cardiomyopathy in Irx4-deficient mice is preceded by abnormal ventricular gene expression. Mol. Cell Biol. 21, 1730-1736.

Wang, G. F., Nikovits, W. Jr., Bao, Z.Z., and Stockdale, F.E. (2001). Irx4 forms an inhibitory complex with the vitamin D and retinoic X receptors to regulate cardiac chamber-specific slow MyHC3 expression. J Biol Chem. 276, 28835-28841.

The decisions about which bases to mutate in the three hexads are also not clear. Why are the first two bases mutated in Hexad B and C and the whole region mutated in Hexad A? Is there a reason to believe these bases are particularly important?

As for the reasons behind mutation of the first two bases in Hexad B and Hexad C, there were two:

One reason is because these point mutations in Hexads B and C were planned after the publication of Wang et al., 1996, which defined the major role of Hexad A in ventricular repression. After this discovery, we decided that a higher level of resolution in our mutation approach would be a better way to search for additional regulators of SMyHC III expression, including the atrial regulator that was readily apparent from the results shown in Wang et al., 1996, but had not yet been described.

The second reason is because the two first nucleotides (purines) in a nuclear-receptor binding hexad are critical for the interaction between target DNA and transcription factors of the nuclear receptor family. Substituting pyrimidines for purines in the two first positions of an hexad drastically reduces the affinity of a nuclear response element, and that is why we chose to use TT substitutions in our mutant constructs. Please refer to: Umesono et al., Cell, 1991 65: 12551266 for a review; Mader et al., J Biol Chem, 1993 268:591-600 for a mutation study; Rastinejad et al., EMBO J., 2000 19:1045-1054 for a crystallographic study (as well as additional references listed below).

Mader, S., Chen, J. Y., Chen, Z., White, J., Chambon, P., and Gronemeyer, H. (1993). The patterns of binding of RAR, RXR and TR homo- and heterodimers to direct repeats are dictated by the binding specificites of the DNA binding domains. EMBO J. 12, 50295041.

Ribeiro, R. C., Apriletti, J. W., Yen, P.M., Chin, W. W., and Baxter, J. D. (1994). Heterodimerization and deoxyribonucleic acid-binding properties of a retinoid X receptor-related factor. Endocrinology.135, 2076-2085.

Zhao, Q., Chasse, S. A., Devarakonda, S., Sierk, M. L., Ahvazi, B., and Rastinejad, F. (2000). Structural basis of RXR-DNA interactions. J. Mol. Biol. 296, 509-520.

Shaffer, P. L. and Gewirth, D. T. (2002). Structural basis of VDR-DNA interactions on direct repeat response elements. EMBO J. 21, 2242-2252.

The control mutant also has effects on the chamber distribution of GFP expression.

We note that, in the mouse, MutS did not produce any major changes from the typical wild type phenotypes linked to SMyHC III-HAP transgenic hearts. We concluded, based on our data, that the spacing mutant worked reasonably well as a negative mutation control in mice. We agree that it would have been particularly elegant if a spacing mutant designed for the mouse context worked in the exact same way in the zebrafish. However, the fact that there are slight differences in behavior for the mutated “spacing” constructs in species separated by, millions of years of independent evolution is not really surprising, given that the amino acid sequence of transcription factors can diverge and co-evolve with binding nucleotides and end up drifting quite substantially from an ancestral setup. As we reiterate below, we consider more fundamental the fact that the cNRE is actually able to bias cardiac expression towards a model of preferential atrial expression, even in the context of species separated by millions of years of independent evolution.

Two claims in the paper have weak evidence. Firstly, the conclusion that the cNRE is necessary and sufficient for driving preferential expression in the atrium. Deleting the cNRE does reduce the amount of atrial reporter gene expression but there is not a "conversion" from atrial to ventricular expression as mentioned in line 205. Similarly, a fusion of 5 tandem repeats of the cNRE can induce expression of a ventricular gene in the atria (I'm assuming a single copy is insufficient), but does not abolish ventricular expression.

We agree that our labelling of the cNRE is perhaps too strong, and we have toned it down accordingly to incorporate the much more equilibrated concept that the cNRE biases cardiac expression towards a model of preferential atrial expression.

However, after the corrections suggested, we believe our assertion is now justified. We show that in the mouse, removal of the cNRE is followed by a major reduction of atrial expression coupled to the release of a low, but quite clear level of expression in the ventricles, when compared to the transgenic mouse harboring the wild type SMyHC III promoter. Note that, as expected, the relative power of the cNRE to establish preferential atrial expression is higher in the mouse (a mammal) than it is in the zebrafish (a teleost), which is biologically sound, as mammals and avians are closer, phylogenetically, than teleosts and avians. Yet, the direction of change of expression in atria and ventricles was exactly as expected, if a given motif responsible for preferential atrial expression was removed (the cNRE in our case), that is: marked reduction in atrial expression and small (albeit clearly evident) release of ventricular expression. We believe that these directional changes observed in species separated by millions of years of independent evolution constitute very good biological evidence for the role of the cNRE in driving preferential atrial expression.

Concerning the 5x fusion of cNREs, we chose to produce this multimer for safety purposes only, because we did not want to risk performing incomplete experiments and having to repeat them. However, more to the point, we later compared the efficiency of one (1) versus five (5) cNRE copies in a cell culture context and the results were not different.

Secondly, the authors claim that the cNRE regulatory sequence arose from viral integration into the genomes of galliform species. While this is an attractive mechanism for explaining novel regulatory sequences, the evidence for this is based purely on sequence homology to viral genomes. And this single observation is not robust as the significance of the sequence matches does not appear to be adjusted for sequence matches expected by chance. The "evolutionary pathway" leading to the direction of chamber-specific expression in the heart as highlighted in the abstract has therefore not been demonstrated.

We agree with the reviewer. Because of space constraints, we decided to omit a substantial part of our work from the initial submission of the manuscript. We now include the relevant data in the revised version. We thus mapped the phylogenetic origins of the SMyHC III family of slow myosins and then established how and when the cNREs became topologically associated with the SMyHC III gene. To do that, we repeat masked all available sequences from avian SMyHC III orthologs. As it will become clear below, the cNRE is a rare sequence, rather than a low complexity repeat. Our search for cNREs outside of the quail context (Coturnix coturnix) followed two independent lines. First, we took a scaled, evolution-oriented approach. Initially, we looked for cNREs in species close to the quail (i.e., Galliformes) and then progressively farther, to include derived (i.e., Passeriformes) and basal avians (i.e., Paleognaths) as well as external groups such as crocodilians. While pursuing this line of investigation, it became clear that the cNRE was a rare form of repetitive element, which showed a conserved topological relationship with the SMyHC III gene (i.e., cNREs flanked the SMyHC III genes at 5’ and 3’ regions). Using this topological relationship as a character, we determined when it appeared during avian evolution and then set out to establish the likely origins of this rare repetitive motif. This search for the origins of the cNRE entailed comparisons to databases of repetitive genome elements, until the extreme telomeric nature of the SMyHC III gene became evident. This finding directed us to the fact that the hexad nature of the cNRE is reminiscent of the hexameric character of telomeric direct repeats. Because direct telomeric repeats are exactly featured in the genomes of avian DNA viruses that can infect the germline and integrate into the avian genome, we focused our search for the cNRE on the members of the subfamily Alphaherpesvirinae (Morissette & Flamand, 2010). In this search, we utilized the human herpes simplex virus 1 (HSV1) as a general model for herpes viruses, and a set of four (4) members of the Alphaherpesvirinae family that specifically infect Galliformes (i.e., GaHV1, the virus responsible for avian infectious laryngotracheitis in chicken, GaHV2, the Marek’s disease virus, GaHV3, a non-pathogenic virus, and MeHV1, the non-pathogenic Meleagrid herpesvirus 1 capable of infecting chicken and wild turkey) (Waidner et al., 2009). The search for cNREs in Alphaherpesvirinae was successful. We found six (6) cNRE hits in HSV1, one (1) in GaHV1, and none in MeHV1, GaHV2, and GaHV3. Our evolution-directed approach thus led to the direct recognition that cNREs can be found in the genomes of a family of viruses that contain members that infect avians and integrate their double-stranded DNA into the host germline (Morissette & Flamand, 2010). Therefore, as a second independent approach, as pointed out by the reviewer, we set out to further extend this proof of concept by broadening our search to all known sequenced viruses and perform an unbiased, internally consistent, and quantitative analysis of cNRE presence in viral genomes, as already reported in the initial submission of this manuscript.

Reviewer #3 (Public Review):

Summary:

In this manuscript Nunes Santos et al. use a combination of computation and experimental methods to identify and characterize a cis-regulatory element that mediates expression of the quail Slow Myosin Heavy Chain III (SMyHC III) gene in the heart (specifically in the atria). Previous studies had identified a cis-regulatory element that can drive expression of SMyHC III in the heart, but not specifically (solely) in the atria, suggesting additional regulatory elements are responsible for the specific expression of SMyHC III in the atria as opposed to other elements of the heart. To identify these elements Nunes Santos et al. first used a bioinformatic approach to identify potentially functional nuclear receptor binding sites ("Hexads") in the SMyHC III promoter; previous studies had already shown that two of these Hexads are important for SMyHC III promoter function. They identified a previously unknown third Hexad within the promoter, and propose that the combination of these three (called the complex Nuclear Receptor Element or cNRE) is necessary and sufficient for specific atrial expression of SMyHC III. Next, they use experimental methods to functionally characterize the cNRE including showing that the quail SMyHC III promoter can drive green fluorescent protein (GFP) expression the atrium of developing zebrafish embryos and that the cNRE is necessary to drive the expression of the human alkaline phosphatase reporter gene (HAP) in transgenic mouse atria. Additional experiments show that the cNRE is portable regulatory element that can drive atrial expression and demonstrate the importance of the three Hexad parts. These data demonstrating that the cNRE mediates atrial-specific expression is well-done and convincing. The authors also note the possibility that the cNRE might be derived from an endogenous viral element but further data are needed to support the hypothesis that the cNRE is of viral origin.

Strengths:

1) The experimental work demonstrating that the cNRE is a regulatory element that can mediate the atrial-specific expression of SMyHC III.

We thank reviewer 3 for this thorough appreciation of our work and are pleased with the evaluation of our manuscript’s potential.

Weaknesses:

1) Justification for use of different regulatory elements in the zebrafish (32 bp cNRE) and the mouse transgenic assays (72 bp cNRE), and discussion of the impact of this difference on the results/interpretation.

In general, throughout our work, we sought to obtain maximal coherence with previous studies (see references below) and to simultaneously probe cNRE function at an increased resolution. For that, we utilized previously described mutant SMyHC III promoter constructs (Wang et al., 1996, 1998) and introduced novel site-directed dinucleotide substitution mutants of individual Hexads in the SMyHC III promoter. Actually, the 72-bp construct is not a 72-bp construct. It is a 5’ deletion construct that removed 72 bp from the 840 bp wild type SMyHC III construct, transforming it into a 768-bp SMyHC III promoter construct. Any directional changes observed in cardiac expression by the 768 bp as compared to the wild type promoter was interpreted in the context as missing regulators present in this 5’ 72 bp.

Wang et al., 1996 and 1998 had already shown that Hexads A and B contained a functional VDRE/RARE, which acted as a ventricular repressor. Using the 768-bp SMyHC III promoter in mouse transgenic lines was thus a natural investigation step for us to evaluate whether regulation of the SMyHC III promoter in the mouse was similar in mice as compared to quail cardiac cultures. As shown in the manuscript, deletion of the 72 bp resulted in the release of a low level of expression in ventricles, consistent with the removal of a ventricular repressor (already described by Wang et al., 1996). It also showed a marked reduction in atrial transgene stimulation, suggesting the elimination of a very important atrial activator.

In 1996, Wang and colleagues mapped an atrial activator to the sequence interval of 160 bp, between -840 and -680 bp (Wang et al., 1996). In our mouse transgenics, we reduced this interval to a mere 72 bp, between -840 to -768 bp. This was very useful information. Wang et al., 1998 showed that HF-1a, M-CAT, and E-box sites located between -840 and -808 bp did not influence atrial expression, so now we had a potential interval of only 40 bp between -808 and -768 bp. Further, our transgenic mice indicated that the GATA site located 3’ from Hexads A, B, and C (GATA site changed to a Sal I site at positions -749 to -743 bp) did not work as a general activator, as in the quail. Thus, the only good candidate for the atrial activator in mice inside the 40-bp fragment between -808 and -768 bp was the cNRE, with its three Hexads, A, B and the novel Hexad C. Because Hexads A plus B composed a functional VDRE/RARE that played a role in ventricular repression in the quail, we hypothesized that the atrial activator would be present in Hexad C. We then mutated the two first purines in Hexad C (the most important ones for nuclear receptor binding, please refer to Umesono et al., Cell, 1991 65: 1255-1266 for a review; Mader et al., J Biol Chem, 1993 268:591-600 for a mutation study; Rastinejad et al., EMBO J., 2000 19:1045-1054 for a crystallographic study as well as additional references listed below) and performed the experiments that demonstrated a profound reduction in atrial expression in the mouse context, revealing the long-sought atrial activator.

Mader, S., Chen, J. Y., Chen, Z., White, J., Chambon, P., and Gronemeyer, H. (1993). The patterns of binding of RAR, RXR and TR homo- and heterodimers to direct repeats are dictated by the binding specificites of the DNA binding domains. EMBO J. 12, 50295041.

Ribeiro, R. C., Apriletti, J. W., Yen, P.M., Chin, W. W., and Baxter, J. D. (1994). Heterodimerization and deoxyribonucleic acid-binding properties of a retinoid X receptor-related factor. Endocrinology.135, 2076-2085.

Wang, G. F., Nikovits, W., Schleinitz, M., and Stockdale, F. E. (1996). Atrial chamber-specific expression of the slow myosin heavy chain 3 gene in the embryonic heart. J. Biol. Chem. 271, 19836-19845.

Wang, G. F., Nikovits, W. Jr., Schleinitz, M., and Stockdale, F. E. (1998). A positive GATA element and a negative vitamin D receptorlike element control atrial chamber-specific expression of a slow myosin heavy-chain gene during cardiac morphogenesis. Mol. Cell Biol. 18, 6023-6034.

Zhao, Q., Chasse, S. A., Devarakonda, S., Sierk, M. L., Ahvazi, B., and Rastinejad, F. (2000). Structural basis of RXR-DNA interactions. J. Mol. Biol. 296, 509-520.

Shaffer, P. L. and Gewirth, D. T. (2002). Structural basis of VDR-DNA interactions on direct repeat response elements. EMBO J. 21, 2242-2252.

2) Is the cNRE really "necessary and sufficient"? I define necessary and sufficient in this context as a regulatory element that fully recapitulates the expression of the target gene, so if the cNRE was "necessary and sufficient" to direct the appropriate expression of SMyHC III it should be able to drive expression of a reporter gene solely in the atria. While deletion of the cNRE does reduce expression of the reporter gene in atria it is not completely lost nor converted from atrial to ventricular expression (as I understand the study design would suggest should be the effect), similarly fusion of 5 repeats of the cNRE induces expression of a ventricular gene in the atria but also does not convert expression from ventricle to atria. This doesn't seem to satisfy the requirements of a "necessary and sufficient" condition. Perhaps a discussion of why the expectations for "necessary and sufficient" are not met but are still consistent would be beneficial here.

We agree with your reasoning. Our description of the cNRE was perhaps too strong, and we have toned it down accordingly in the revised manuscript to incorporate a much more equilibrated concept that the cNRE biases cardiac expression towards a model of preferential atrial expression. After these corrections, we believe our novel assertion is justified. We show that in the mouse, removal of the cNRE is followed by a major reduction of atrial expression coupled to the release of a low, but quite clear level of expression in the ventricles, when compared to the transgenic mouse harboring the wild type SMyHC III promoter. Note that, as expected, the relative power of the cNRE to establish preferential atrial expression is higher in the mouse (a mammal) than it is in the zebrafish (a teleost), which is biologically sound, as mammals and avians are closer, phylogenetically, than teleosts and avians. Yet, the direction of change of expression in atria and ventricles was exactly as expected, if a given motif responsible for preferential atrial expression was removed (the cNRE in our case), that is: marked reduction in atrial expression and small (albeit evident) release of ventricular expression. We believe that these directional changes observed in species separated by millions of years of independent evolution constitute very good biological evidence for the role of the cNRE in driving preferential atrial expression.

3) The claim that the cNRE is derived from a viral integration is not supported by the data. Specifically, the cNRE has sequence similarity to some viral genomes, but this need not be because of homology and can also be because of chance or convergence. Indeed, the region of the chicken genome with the cNRE does have repetitive elements but these are simple sequence repeats, such as (CTCTATGGGG)n and (ACCCATAGAG)n, and a G-rich low complexity region, rather than viral elements; The same is true for the truly genome. These data indicate that the cNRE is not derived from an endogenous virus but is a repetitive and low complexity region, these regions are expected to occur more frequently than expected for larger and more complex regions which would cause the BLAST E value to decrease and appear "significant”, but this is entirely expected because short alignments can have high E values by chance. (Also note that E values do not indicate statistical significance, rather they are the number of hits one can "expect" to see by chance when searching specific database.)

We do understand the criticism, but we would like to advance another concept, based on a series of results that we obtained using bioinformatics-oriented and evolution-oriented analyses. We performed a cNRE scan in the Gallus gallus genome (galGal5), using varying numbers of nucleotide mismatches. When we searched the galGaL5 genome with coordinates matching the localization of cNREs obtained using matchPattern with up to 8 mismatches, only thirty-one (31) and thirty-four (34) hits were found in the 5’ and 3’ strands, respectively. This indicates that a cNRE match is a rather uncommon finding in the Gallus gallus genome.

A more systematic profiling of genome occurrence versus nucleotide mismatch indicated that a significant upward inflexion in the relationship between number of cNRE hits and divergence from the original cNRE version (Coturnix coturnix) is recorded only at 12 mismatches or greater. At 8 mismatches, the total number of cNREs on each DNA strand varied little among all avian species examined, remaining close to the average (31+/- 2,2 cNREs for the 5’ strand, range 1748; 34 +/- 3,3 for the 3’ strand, range 14-64). Consistent with the idea that the cNRE is a specific regulatory motif, rather than an abundant, low complexity sequence, there are only two cNRE occurrences in chromosome 19, which harbors AMHC1, the Gallus gallus ortholog of the Coturnix coturnix SMyHC III gene.

Figure 1: Number of cNRE hits to galGal5 according to maximum mismatches allowed: the cNRE is not an abundant low complexity sequence, but rather a rare repetitive sequence with a clear cutoff level of mismatches allowed. Consistent with this, there are only two (2) cNRE sequences in chromosome 19, the chromosome that contains the AMHC1 gene (the chicken ortholog of the quail SMyHC III gene). ## [1] chr19 [16510, 16541] * | 5’-CAAGGACAAAGAGGGGACAAAGAGGCGGAGGT-3 ## [2] chr19 [32821, 32852] * ‘5’-CAAGGACAAAGAGTGGACAAAGAGGCAGACGT-3

In the evolutionary strategy, which we now include, we first mapped the phylogenetic origins of the SMyHC III family of slow myosins and then established how and when the cNREs became topologically associated with the SMyHC III gene. To do that we repeat masked all available sequences from avian SMyHC III orthologs. As it will become clear below, the cNRE is a rare sequence, rather than a low complexity repeat. Our search for cNREs outside of the quail context (Coturnix coturnix) followed two independent lines. First, we took a scaled, evolution-oriented approach. Initially, we looked for cNREs in species close to the quail (i.e., Galliformes) and then progressively farther, to include derived (i.e., Passeriformes) and basal avians (i.e., Paleognaths) as well as external groups such as crocodilians. While pursuing this line of investigation, it became clear that the cNRE was a rare form of repetitive element, which showed a conserved topological relationship with the SMyHC III gene (i.e., cNREs flanked the SMyHC III genes at 5’ and 3’ regions). Using this topological relationship as a character, we determined when it appeared during avian evolution, and then set out to establish the likely origins of this rare repetitive motif. This search for the origins of the cNRE entailed comparisons to databases of repetitive genome elements, until the extreme telomeric nature of the SMyHC III gene became evident. This finding directed us to the fact that the hexad nature of the cNRE is reminiscent of the hexameric character of telomeric direct repeats. Because direct telomeric repeats are exactly featured in the genomes of avian DNA viruses that can infect the germline and integrate into the avian genome (Morissette & Flamand, 2010), we focused our search for the cNRE on the members of the subfamily Alphaherpesvirinae. In this search, we utilized the human herpes simplex virus 1 (HSV1) as a general model for herpes viruses and a set of four (4) members of the Alphaherpesvirinae family that specifically infect Galliformes (i.e., GaHV1, the virus responsible for avian infectious laryngotracheitis in chickens, GaHV2, the Marek’s disease virus, GaHV3, a non-pathogenic virus and MeHV1, the non-pathogenic Meleagrid herpesvirus 1 capable of infecting chicken and wild turkey) (Waidner et al., 2009). The search for cNREs in Alphaherpesvirinae was successful. We found six (6) cNRE hits in HSV1 and one (1) cNRE was detected in GaHV1, but none in MeHV1, GaHV2, and GaHV3.

Our evolution-directed approach thus led to the direct recognition that cNREs up to a cutoff mismatch value of 11 can be found in the genomes of a family of viruses that contain members that infect avians and integrate their double-stranded DNA into the host germline. Therefore, as a second independent approach, we set out to extend this proof of concept by broadening our search to all known sequenced viruses to perform an unbiased, internally consistent, and quantitative analysis of cNRE presence in viral genomes, as already reported in the initial submission of this manuscript.

Author Response:

Reviewer #1 (Public Review):

In this study, Kuppan, Mitrovich, and Vahey investigated the impact of antibody specificity and virus morphology on complement activation by human respiratory syncytial virus (RSV). By quantifying the deposition of components of the complement system on RSV particles using high-resolution fluorescence microscopy, they found that antibodies that bind towards the apex of the RSV F protein in either the pre- or post-fusion conformation activated complement most efficiently. Additionally, complement deposition was biased towards globular RSV particles, which were frequently enriched in F in the post-fusion conformation compared to filamentous particles on which F exists predominantly in the pre-fusion conformation.

Strengths:

1) While many previous studies have examined the properties of antibodies that impact Fc-mediated effector functions, this study offers a conceptual advance in its demonstration that heterogeneity in virus particle morphology impacts complement activation. This novel finding will motivate further research on this topic both in the context of RSV and other viral infections.

2) The use of site-specific labeling of viral proteins and high-resolution fluorescence microscopy represents a technical advance in monitoring interactions among different components of antiviral immune responses at the level of single virus particles.

3) The paper is well written, data are clearly presented and support key claims of the paper with caveats appropriately acknowledged.

We appreciate the reviewer’s supportive comments. In our revised manuscript, we have focused on improving clarity regarding the minor weaknesses noted below.

Minor weaknesses:

Working models and their implications could be clarified and extended. Specifically:

1) The finding that globular particles enriched in F proteins in the post-fusion conformation (Fig 3F) are dominant targets of complement activation as measured by C3 deposition by not only post-F- but also pre-F-specific antibodies (Fig 4B, left) is interesting. This is despite the fact that, as expected, pre-F antibodies bind less efficiently to globular particles (Fig 4B, right). How do the authors reconcile these observations, given that C3 deposition seems to be IgG-concentration-dependent (Fig 2E)?

The reviewer raises an excellent point: globular particles, which accumulate as the virus ages, contain more post-F and less pre-F than particles that have recently been shed from infected cells. These ‘aged’ particles nonetheless accumulate more C3 when incubated with pre-F mAbs than ‘younger’ particles, where the proportion of pre-F is higher. We attribute this to the lower surface curvature of globular particles: they accumulate more C3 in the presence of pre-F mAbs in spite of the reduced availability of pre-F epitopes. Figure 1C and 1F help to support this point. This data shows C3 deposition driven by different antibodies bound to particles enriched in either pre-F (Figure 1C) or post-F (Figure 1F). Importantly, for this experiment the conversion to post-F was driven in such a way that virion morphology is preserved (Figure 1E). In this case, we see a clear reduction in C3 deposition by pre-F mAbs on post-F particles (e.g. for CR9501, the percentage of C3-positive particles drops from 24% on pre-F virus to 6% on post-F-enriched virus). This demonstrates that, in the absence of other changes, conversion of pre-F to post-F reduces complement deposition by pre-F specific mAbs.

Similarly, the reviewer correctly points out that reduced levels of antibody binding lead to lower levels of C3 deposition (Figure 2E); however, as in Figure 1, this data is collected from particles with the same morphologies. Thus, in the absence of additional factors, reduction in mAbs bound to pre-F leads to a reduction in C3 deposition driven by these mAbs. The fact that we observe the opposite trend when changes in particle morphology accompany changes in post-F abundance points to an important role for particle shape in activation of the classical pathway.

2) Based on data in Figure 5-figure supplement 2, the authors argue that "large viruses are poised to evade complement activation when they emerge from cells as highly-curved filaments, but become substantially more susceptible as they age or their morphology is physically disrupted." Could the increase in C3 deposition be alternatively explained by a higher density of F proteins on larger particles instead of / in addition to a larger potential decrease in membrane curvature?

We agree that the density of F on a virus – the number of F trimers per unit surface area - likely contributes to the efficiency of C3 deposition. In Figure 6 – figure supplement 2 (Figure 5 – figure supplement 2 in the original submission), we control for this potential effect by comparing viruses that have the same amount of F (as measured by fluorescence intensities of SrtA-labeled F) that are either in filamentous form or globular form (induced through osmotic swelling). The total amount of F per virus is preserved during swelling, and the membrane surface area will remain constant due to the limited ability of lipid bilayers to stretch7. As a result, the input material for these comparisons is the same in terms of F trimers per unit area, yet the C3:F ratio differs substantially. This leads us to conclude that the differences must be attributable to factors other than the density of F. Importantly, this does not mean that the amount of F per unit surface area does not matter for C3 deposition – only that this is not the effect we are observing here. We have added text (Line 299) to help clarify this point: “This effect is unlikely to arise due to changes in the abundance or density of F in the viral membrane, both of which will remain constant following swelling. Similarly, it does not appear to be purely related to size, as larger viral filaments show similar C3:F ratios as smaller viral filaments.”

3) In the discussion, the authors acknowledge that the implications based on the findings are speculative. However, more clarity on the basis of these speculative models would be useful. For example, it is not clear how the findings directly inform the presented model of immunodominance hierarchies in infants.

We agree that this was unclear in the original manuscript. We have rewritten paragraph 4 of the Discussion to clarify how our results may contribute to the changes in immunodominance that have been observed in RSV between infants and adults.

Reviewer #2 (Public Review):

This is an intriguing study that investigates the role of virus particle morphology on the ability of the first few components in the complement pathway to bind and opsonize RSV virions. The authors use primarily fluorescence microscopy with fluorescently tagged F proteins and fluorescently labeled antibodies and complement proteins (C3 and C4). They observed that antibodies against different epitopes exhibited different abilities to induce C3 binding, with a trend reflecting positioning of IgG Fc more distal to the viral membrane resulting in better complement "activation". They also compared the ability of C3 to deposit on virus produced from cells +/- CD55, which inhibits opsonization, and showed knockout led to greater C3 binding, indicating a role for this complement "defense protein" in RSV opsonization. They also examined kinetics of complement protein deposition (probed by C4 binding) to globular vs filamentous particles, observing that deposition occurred more rapidly to non-filaments.

A better understanding of complement activation in response to viruses can lead to a more comprehensive understanding of the immune response to antigen both beneficial and detrimental, when dysfunctional, during infection as well as mechanisms of combating the viral infection. The study provides new mechanistic information for understanding the properties of an enveloped virus that can influence complement activation, at least in an in vitro setting. It remains to be determined whether these effects manifest in the considerably more complex setting of natural infection or even in the presence of a polyclonal antibody mixture.

The studies are elegantly designed and carefully executed with reasonable checks for reproducibility and controls, which is important especially in a relatively complex and heterogeneous experimental system.

We thank the reviewer for the insightful comments. We have revised the manuscript to help to clarify points of confusion and to address some of the technical points raised here.

Specific points:

1) "Complement activation" involves much more than C3 or C4 binding. Better to use more specific terminology relating to the observable (i.e. fluorescently labeled complement component binding)

We agree with the reviewer. We have revised the manuscript throughout to make our language more accurate and precise.

2) What is the rationalization for concentrations of antibodies used? What range was tested, and how dependent on antibody concentration were the observed complement deposition trends? How do they relate to physiological concentrations, and how would the presence of a more complex polyclonal response that is typically present (e.g. as the authors noted, the serum prior to antibody depletion already mediates complement activation) affect the complement activation trends? The neat, uniform display of Fc for monoclonals that were tested is likely to be quite garbled in more natural antibody response situations. This should be discussed.

We have added discussion of antibody concentrations and possible differences between monoclonal and polyclonal responses to the revised manuscript. Below, we address the specific questions raised here by the reviewer.

We chose to use antibody concentrations that are comparable to the concentrations of dominant clonotypes in post-vaccination serum1. Our goal in selecting relatively high antibody concentrations for our experiments was to focus on understanding the capacity of an antibody to drive complement deposition when it has reached maximum densities on RSV particles. This is discussed starting on Line 125 of Results, and in paragraph 2 of Discussion. Experiments testing a range of antibody concentrations would be valuable, but are likely to strongly reflect differences in the binding affinities of these antibodies, which have been characterized previously.

Although we have not performed titrations for each of the antibodies tested due to the large number of conditions needed and the limited throughput of our experimental approach, the manuscript does present a dilution series for CR9501, the IgG1 mAb with the greatest potency in driving C3 deposition among those tested here. This data (shown in Figure 3E & F in the revised manuscript) shows that as the amount of antibody added in solution decreases over a 16-fold range, C3 deposition decreases as well. The decrease in C3 deposition is roughly commensurate with the reduction in antibody binding, reaching levels that are just above background at an antibody concentration of ~0.6μg/ml (1:800 dilution). We think it is likely that other activating antibodies would show similar trends, while antibodies that do not activate the classical pathway at saturating concentrations would be unlikely to do so across a range of lower concentrations.

We agree with the reviewer that complement deposition driven by polyclonal antibodies is more complex than the monoclonal responses studied here. As discussed in paragraph 2 of our revised Discussion, one effect that polyclonal serum might have is to increase the density of Fcs on the virus by providing antibody mixtures that bind to multiple non-overlapping antigenic sites. We speculate that this would generally increase complement deposition, provided that sufficient antibodies are present that bind to productive antigenic sites (e.g. sites 0/ , II, and V).

Finally, we note that we observe a similar phenomenon where globular particles are preferentially opsonized with C3 in our experiments with polyclonal serum where IgG and IgM have not been depleted (Figure R1). The major limitation of this data – which is resolved by using monoclonal antibodies – is the difficulty of determining to what extent this bias arises due to the epitopes targeted by the polyclonal serum versus the intrinsic sensitivity of the virus particles.

Figure R1: RSV opsonized with polyclonal human serum. A similar bias towards globular particles (white dashed circles) is observed as in experiments with monoclonal antibodies.

3) Are there artifacts or caveats resulting from immobilization of virus particles on the coverslips?

As pointed out by the reviewer, a few possible artifacts or caveats could arise due to the immobilization of viruses on coverslips. These include (1) spurious binding of C1 or other complement components to the immobilizing antibody (3D3); (2) reduced access to viral antigens as a result of immobilization; and (3) inhibition of antibody-induced viral aggregation. We are able to rule out issues associated with (1), because we do not see attachment of C1 or C3 to the coverslip (i.e. outside regions occupied by virus particles). This is consistent with the fact that the antibodies are immobilized on the surface via a C-terminal biotin attached to the heavy chain, which would limit access for C1 binding and prevent the formation of Fc hexamers.

Immobilization on coverslips could reduce the accessibility of a portion of the virus for binding by antibodies and complement proteins. This could effectively shield a portion of the viral surface from assembly of an activating complex, which we estimate requires ~35nm of clearance above the targeted epitope on F8. Importantly, the fraction of the viral surface area that would be shielded would vary for filaments and spheres; to determine if this could influence our results, we calculated the expected magnitude of this effect (Figure R2). To do this, we modeled the virus as being tethered to the surface via a 25nm linkage. This accounts for the length of the biotinylated PEG (~5-15nm for PEG2K, depending on the degree of extension), streptavidin (~5nm), and the anti-G antibody (~10-15nm including the biotinylated C-terminal linker). Although limited structural information is available for RSV G, the ~100 residue, heavily glycosylated region between the viral membrane and the 3D3 epitope likely extends above the height of F (~12nm). Our model assumes that a shell of thickness d surrounding the virus is necessary for antibody-C1 complexes to fit without clashing with the surface (this shell is shaded in gray in the schematic from Figure R2). Tracing the angles at which this shell clashes with the coverslip allows us to calculate the fraction of total surface area that is inaccessible for activation of the classical pathway. The results are plotted on the right side of Figure R2. The relative surface area accessible to a 35nm activating antibody-C1 complex differs between a filament and a sphere of equivalent surface area by about 15%. We conclude that this difference is modest compared to the ~5-fold difference in deposition kinetics we observe between viral filaments and spheres (Figure 4), or the 3- to 10-fold difference in relative C3 deposition we observe on larger filamentous particles after conversion to spheres (Figure 6 – figure supplement 2C).

Finally, by performing experiments on immobilized viruses, we eliminate the possibility for antibody-dependent particle aggregation. While this was necessary for us to get interpretable results, the formation of viral aggregates could affect the dynamics and extent of complement deposition. For example, activation of the classical pathway on one particle in an aggregate could spread to non-activating particles through a “bystander effect”, as has been reported in other contexts9. We are interested in this question and have begun preliminary experiments in this direction; however, we believe that a definitive answer is outside the scope of this current work. To alert readers to this consideration, we have added this to paragraph 2 of the revised Discussion (Line 359).

Figure R2: Estimating the surface accessibility of RSV particles bound to coverslips. Definition of variables: af: radius of cylindrical RSV filament; as: radius of spherical RSV particle of equivalent surface area (see Figure 6 – figure supplement 2A); d: distance needed above the viral surface to accommodate IgG-C1 activating complexes; h: height of viral surface above the coverslip; L: length of the viral filament.

4) How is the "density of antigen" quantitated? What fraction of F or G is labeled? For fluorescence intensity measurements in general, how did the authors ensure their detection was in a linear sensitivity range for the detectors for the various fluorescent channels? Since quantitation of fluorescence intensities is important in this study, some discussion in methods would be valuable.

We have performed this important additional characterization of our fluorescence system and our overall labeling and quantification strategy to address these concerns. The results of this characterization are now included in two new figure supplements in the revised manuscript (Figure 1 – figure supplements 2 & 3).

5) The authors also show that the particle morphology, whether globular or filamentous, as well as relative size and resulting apparent curvature, correlate with ability of C3 to bind. Some link to the abundance of post-fusion F (post-F) is examined and discussed, but I found the back and forth discussion between morphology, C3 binding, and post-F abundance to be confusing and in need of clarification and streamlining. Is there a mechanistic link between morphology changes and post-F level increases? Are the two linked or coincidental (for example does pre-F interaction with matrix help stabilize that conformation, and if lost lead to spontaneous conversion to post-F?). Please clarify.

Specifically, we have separated the discussion of pre-F versus post-F abundance and particle morphology into two different sections in Results, and we have rearranged Figures 4 and 5 (Figures 3 and 4 in the original submission) to improve clarity.

Regarding the question of whether changes in morphology and the pre-F to post-F conversion are coincidental or mechanistically linked: the answer is not entirely clear, although we have collected new data that suggests a connection. We first want to note that the two effects are at least partly separable: brief treatment with a low osmolarity solution causes particle shape to change while preserving pre-F (Figure 6A & B), whereas treating with an osmotically balanced solution with low ionic strength converts pre-F to post-F without affecting virus shape (Figure 1E). However, we were motivated by the reviewer’s questions to look into this further. To determine if the change in viral shape may serve to destabilize the pre-F conformation over time, we compared the relative amounts of pre-F and post-F present in particles that were osmotically swollen to those that were not at 0h and at 24h. In these experiments, particles were swollen using a brief (~1 minute) exposure to low osmolarity conditions before returning them to PBS (Figure R3, left). As expected, we observe no immediate change in pre-F abundance following the brief osmotic shock (Figure R3, right: 0h time point), consistent with Figure 6B. After incubating the particles an additional 24h at 37oC, the post-F-to-pre-F ratio is ~3.5-fold higher in osmotically-swollen particles than in those where filamentous morphology was initially preserved (Figure R3, right: 24h time point). This supports the reviewer’s suggestion that interactions with the matrix may help to stabilize F in the prefusion conformation, since the conversion to post-F is faster when this interaction is disrupted. Whether or not this has any relevance for RSV entry into cells remains to be determined; however, it is worth noting that we observed no clear loss or gain of infectivity in RSV particles following osmotic swelling (Figure 6 – figure supplement 1A). Since this result may be of interest to readers, we have included this new data in Figure 6 – figure supplement 1B, and it is discussed briefly in Results (Line 250).

Figure R3: Determining stability of pre-F following matrix detachment. Left: Experimental design. Right: Comparison of pre-F stability on untreated particles (gray) and particles subjected to brief osmotic swelling (magenta). Distributions show the ratio of post-F (ADI-14353) to pre-F (5C4) intensities per particle, combined for four biological replicates, sampled at 0h (immediately after swelling) and after an additional incubation at 37oC for 24h. Black points show median values for each individual replicate. P-values are determined from a two-sample T test.

6) Since their conclusion is that curvature of the virus surface is a major influence on the ability of complement proteins to bind, I feel that some effort at modeling this effect based upon known structures is warranted. One might also anticipate then that there would be some epitope-dependent effect as a result of changes in curvature that may lead to an exaggeration of the epitope-specific effects for more highly curved particles perhaps than those with lower curvature? Is this true?

The reviewer raises two excellent points: that it may be possible to gain insight into the mechanisms through which curvature dictates C1 binding and other aspects of complement activation through structural modeling, and that such a model may help to identify specific epitope effects that could contribute to curvature dependence.

We developed simulations based on the geometry of RSV, F, and hexameric IgG to try to better understand how curvature may influence initiation of the classical pathway. This model is described in the Methods section (Modeling IgG hexamers on curved surfaces), and the results are discussed in the final two paragraphs of the Results section. In addition, we have included a new figure (Figure 7) to summarize the model’s predictions. This model corroborates the curvature sensitivity of IgG hexamer formation and suggests a possible intuitive explanation for our findings: high curvature effectively increases the distance between epitopes that sit high above the viral membrane, decreasing the likelihood of hexamer formation (Figure 7D). Regarding epitope specific effects, this model suggests that the further the epitope is above the viral membrane, the greater the effect that decreasing curvature will have. However, we find that epitopes closer to the membrane (e.g. those bound by 101F or ADI-19425) are overall very inefficient at activating the classical pathway, potentially due to steric obstruction of the formation of IgG hexamers. Thus, there may be an inherent tradeoff between overcoming steric obstruction (by binding to epitopes distal to the membrane) and sensitivity to surface curvature.

It is important to note that this model is reductionist and does not include detailed structural information. Additional factors may be important for considering epitope-specific effects. For example, antibodies that bind equatorially on F (e.g. ADI-19425, which binds to antigenic site III), show minimal complement deposition in our experiments. However, particles whose curvature approaches the diameter of hexameric IgG or IgM (~20nm) may display these epitopes in a manner that is more accessible. If the curvature necessary to observe such an effect falls outside of the biologically accessible range, it would not be observable in our experiments. Nonetheless, it is possible that a different set of antibodies may drive complement deposition on highly-curved nanoparticle vaccines that are in development10. We have added this important point to the second paragraph of the Discussion.

7) Line 265: it would be useful to confirm the increase C1 binding as a function of morphology as was done for antibody-angle of binding experiments.

We believe that this data is shown in Figure 6B (Figure 5B in the original manuscript).

Reviewer #3 (Public Review):

Overall the manuscript is clearly written and the data are displayed well, with helpful diagrams in the figures to illustrate assays and RSV F epitopes. The engineering of the RSV strain to include a fluorescent reporter and tags on F and G that serve as substrates for fluorophore attachment is impressive and is a strength. The RSV literature is well cited and the interpretation of the results is consistent with structure/function data on RSV F and its interaction with antibodies. This reviewer is not an expert on the experiments performed in this manuscript, but they appear to be rigorously performed with appropriate controls. As such, the conclusions are justified by the data. One weakness is the extent to which the results regarding virion morphology are biologically relevant. Non-filamentous forms of the virion are generally obtained only in vitro as a result of virion purification or biochemical treatment. However, these results may be relevant for certain vaccine candidates, including the failed formalin-inactivated RSV vaccine that was evaluated in the late 1960s and caused vaccine-enhanced disease upon natural RSV infection.

Thank you for these suggestions, which have helped us to better place our results regarding RSV morphology in the context of prior work. We agree with the reviewer that non-filamentous RSV particles are commonly obtained in vitro, and that this morphology does not reflect the structure of the virus as it is budding from infected cells. Our work has characterized the transition from filament to globular / amorphous form, with the finding that it can occur rapidly upon physical or chemical perturbations, as well as more gradually during natural aging: i.e. in the absence of handling or purification. We are also able to detect globular particles accumulating in cultured A549 cells, where no handling has occurred prior to observation (Figure 5 – figure supplement 1). While we do not currently know how well this reflects the tendency of RSV to undergo conversion from filament to sphere in vivo, we propose that it is plausible that such a transformation could occur. To distinguish between what we demonstrate and what we speculate, we write (Line 401): “Although more work is needed to understand the prevalence of globular particles during in vivo infection, our observations that these particles accumulate over time through the conversion of viral filaments – even under normal cell culture conditions - suggest that their presence in vivo is feasible, where the physical and chemical environment would be considerably harsher and more complex.”

We agree with the reviewer that our results may have relevance towards understanding the failed formalin-inactivated vaccine trial. We have added this to paragraph 5 of the Discussion section.

Author Response:

Reviewer #2 (Public Review):

1. The novelty of the current observation of two types of links is overstated, for example, in the abstract: "Our data reveal the existence of two molecular connectors/spacers which likely contribute to the nanometer scale precise stacking of the ROS disks" (Line 25). In fact, both of these links have been shown before (Usukura and Yamada, 1981; Roof and Heuser, 1982; Corless and Schneider, 1987; Corless et al., 1987; Kajimura et al., 2000). These previous studies deserve to be recognized. Of special note is the paper by Usukura and Yamada whose images of the disc rim connectors are by no means less convincing than shown in the current manuscript. On the other hand, the novelty and impact of the data related to peripherin appears to be understated, particularly in the abstract.

We changed the abstract line 27 to: “Our data confirm the existence of two previously observed molecular connectors …”, cite the recommended references in the introduction (lines 54-55), the results (lines 131-132), and the discussion (lines 282/285). To highlight the previous reports, we rephrased the sentence in lines 132-133, “In agreement with these previous findings, we observed structures that connect membranes of two adjacent disks …”; the discussion is rephrased in lines 280-281, “Similar connectors have been observed previously ...” and “… and their statistical analysis confirmed the existence of two distinct connector species.”, and in lines 291-292, “Based on previous studies combined with our quantitative analysis, we put forward a hypothesis for the molecular identity of the disk rim connector which agrees in part with recent models”.

1. Notably, ROM-1 has not been found in peripherin oligomers larger than octamers (e.g. Loewen and Molday, 2000 and subsequent studies by Naash and colleagues). This should be discussed in the context of the current model.

We agree that this is an important aspect. We pick subvolumes along all disk rims, and on average we obtain the ordered scaffold as shown in the manuscript. We expect heterogeneity in the data because of the different degrees of oligomerization and the exclusion of ROM1 from higher oligomers. Our analysis required substantial classification to achieve convergence to a stable average, indeed indicating heterogeneity in the rim structure. However, we could not resolve additional structures to sufficient quality. It might be that this heterogeneity is what ultimately limits our achievable resolution. We added these thoughts in the discussion starting in lines 377-378, “PRPH2-Rom1 oligomers isolated from native sources exhibit varying degrees of polymerization (Loewen and Molday, 2000), and ROM1 is excluded from larger oligomers (Milstein et al., 2020). We could not resolve this heterogeneity as additional structures to sufficient quality by subvolume averaging, but in combination with the inherent flexibility of the disk rim, this heterogeneity might be the reason for the restricted resolution of our averages.”

1. The following statement should be reconsidered given the established role of cysteine-150 in peripherin oligomerization: "We hypothesize that the necessary cysteine residues are located in the head domain of the tetramers (Figure 5B), ..." It has been firmly established that only one cysteine (C150) located in the intradiscal loop is not engaged in intramolecular interactions and is essential for peripherin oligomerization.

Thank you for this advice. We agree and rephrased our discussion in lines 368-371, “The intermolecular disulfide brides are exclusively formed by the PRPH2-C150 and ROM1-C153 cysteine residues, which are located in the luminal domain (Zulliger et al., 2018). We hypothesize that these disulfide bonds (Figure 5B), are responsible for the contacts across rows (Figure 3) ...”

1. Line 340: "A model involving V-shaped tetramers for membrane curvature formation was proposed recently (Milstein et al., 2020), but it comprises two rows of tetramers which are linked in a head-tohead manner. Our analysis instead resolves three rows organized side-by side in situ (Figure 5A)." I am confused by this statement: doesn't your model also show long rows connected head-to-head? The real difference is that Milstein and colleagues proposed four tetramers per rim whereas the current data reveal three.

Thank you for pointing out this imprecise description. The model proposed by Milstein and the model in the old version of our manuscript, both propose linkage between tetramers via their disk luminal domains. In our manuscript, we refer to the luminal domain as the head domain. However, to our understanding, the Milstein model suggests two rows of tetramers, where one tetramer in the first row is rotated 180° with respect to a tetramer in the second row (therefore head-to-head), while our data indicate that the V-shaped repeats which we originally hypothesized to be tetramers are only rotated ~63° with respect to one another and are therefore rather oriented side-by-side:

Fig. 2: Comparison of models for the organization of the ROS disk rim as proposed in in Milstein et al., 2020 (top panel)

and in our work (lower panel). We now rephrased lines 383-385, “Instead, our analysis in situ resolves three rows of repeats which are also linked by the luminal domain but are rather organized side-by-side (Figure 5A).”

1. Line 347: "Our data indicate that the luminal domains of tetramers hold the disk rim scaffold together (Figure 3C), which is supported by the fact that most pathological mutations of PRPH2 affect its luminal domain (Boon et al., 2008; Goldberg et al., 2001). It is possible that these mutations impair the formation of tetramers, rows of tetramers, and their disulfide bond-stabilized oligomerization. These alterations could impede or completely prevent disk morphogenesis which, in turn, would disrupt the structural integrity of ROS, compromise the viability of the retina and ultimately lead to blindness." This is not an original idea, as many studies showed that disruptions in peripherin oligomerization lead to anatomical defects in disc formation and subsequent photoreceptor cell death.

Thank you for pointing this out. Our data are indeed in good agreement with the results made by many groups and further expand on them. We rephrased the manuscript in several places to clarify this relationship: in the abstract lines 32-34, “Our Cryo-ET data provide novel quantitative and structural information on the molecular architecture in ROS and substantiate previous results on proposed mechanisms underlying pathologies of certain PRPH2 mutations leading to blindness.”; in the introduction lines 78-79, “… allowed us to obtain 3D molecular-resolution images of vitrified ROS in a close-to-native state providing further evidence for previously suggested mechanisms leading to ROS dysfunction”; and in the discussion lines 393-397, “In good agreement with previous work, it is possible that these mutations impair the formation of complexes, and their disulfide bond-stabilized oligomerization (Chang et al., 2002; Conley et al., 2019; Zulliger et al., 2018). Hence, these alterations could impede or completely prevent disk morphogenesis …”. Also, additional relevant publications are cited in line 395.

1. In regards to the distance between disc rims and plasma membrane, the authors cite the data obtained with frogs (10 nm) but not a more relevant, previously reported measurement in mice (Gilliam et al, 2012). The value of 18 nm reported in that study is much closer to the currently reported value.

We appreciate the reference to this excellent paper. We added it in lines 335-337, “This value was derived from amphibians (Roof and Heuser, 1982) and deviates considerably from recent results (18 nm, (Gilliam et al., 2012)) and from our current measurements in mice (~25 nm).” Our aim was to point out that a model for ROS organization that is often cited and is otherwise well-founded (BatraSafferling et al., 2006) makes a wrong assumption about distance in the context of the mammalian systems. 7. The authors are (correctly) being very careful in assigning the molecular identity of disc interior connectors to PDE6. However, they are more confident in assigning the disc rim connectors to GARP2, which is reflected in the labeling of these links in figure

1. Their arguments are valid, but these links are not attached to peripherin (a protein considered to be the membrane binding partner for GARPs), which is not immediately consistent with this hypothesis. Perhaps it would be fair to re-label the corresponding links in figure 5 as "disc rim connectors".

That is an excellent and fair suggestion. We changed Figure 5 accordingly.

1. On a similar note, the disc rim connectors seem to be located where ABCA4 is presumed to be localized within the rim, which may not be just a coincidence. The authors already have tomograms obtained from ABCA4 knockout animals. Is it possible to analyze whether these links are preserved in these tomograms?

We agree, this is an important question to address. Unfortunately, neither the biological preparation nor the tomograms of the ABCA4 knockout were as good in quality as for the WT. Still, we frequently see connectors at the disk rim, especially after denoising of the tomograms.

Fig. 3: connectors at disk rims in WT (left) and ABCA4 knockout mice (right).

Sometimes it appears the connectors between adjacent disks are linked via an intradisk densities, which was already observed in Corless et al., 1987. We thought that these densities could be ABCA4 and tried to find them with two approaches in our WT tomograms (data not shown). In the first approach using a segmentation similar to what we did for the connectors between disks, we found an order of magnitude fewer intradisk connectors than (inter)disk rim connectors. In the second approach, we used the positions of segmented (inter)disk rim connectors and classified rotational averages which focused on the disk luminal space next to the contact point of a connector with the disk membrane. Again, less than 10% of the disk rim connector subvolumes were assigned to classes with an additional luminal density. Both experiments indicate that disk rim connectors sometimes occur with an additional luminal density. In total, we found less than 100 of these intradisk densities, an observation which seems to be preserved in WT and ABCA4 KO. Based on this small number of positions/locations, however, we cannot draw any conclusion. Therefore, we did not add this point to the manuscript.

Author Response

Public Evaluation Summary:

The authors re-analyzed a previously published dataset and identify patterns suggestive of increased bacterial biodiversity in the gut may creating new niches that lead to gene loss in a focal species and promote generation of more diversity. Two limitations are (i) that sequencing depth may not be sufficient to analyze strain-level diversity and (ii) that the evidence is exclusively based on correlations, and the observed patterns could also be explained by other eco-evolutionary processes. The claims should be supported by a more detailed analysis, and alternative hypotheses that the results do not fully exclude should be discussed. Understanding drivers of diversity in natural microbial communities is an important question that is of central interest to biomedically oriented microbiome scientists, microbial ecologists and evolutionary biologists.

We agree that understanding the drivers of diversity in natural communities is an important and challenging question to address. We believe that our analysis of metagenomes from the gut microbiomes is complementary to controlled laboratory experiments and modeling studies. While these other studies are better able to establish causal relationships, we rely on correlations – a caveat which we make clear, and offer different mechanistic explanations for the patterns we observe.

We also mention the caveat that we are only able to measure sub-species genetic diversity in relatively abundant species with high sequencing depth in metagenomes. These relatively abundant species include dozens of species in two metagenomic datasets, and we see no reason why they would not generalize to other members of the microbiome. Nonetheless, further work will be required to extend our results to rarer species.

Our revised manuscript includes two major new analyses. First, we extend the analysis of within-species nucleotide diversity to non-synonymous sites, with generally similar results. This suggests that evolutionarily older, less selectively constrained synonymous mutations and more recent non-synonymous mutations that affect protein structure both track similarly with measures of community diversity – with some subtle differences described in the manuscript.

Second, we extend our analysis of dense time series data from one individual stool donor and one deeply covered species (B. vulgatus) to four donors and 15 species. This allowed us to reinforce the pattern of gene loss in more diverse communities with greater statistical support. Our correlational results are broadly consistent with the predictions of DBD from modeling and experimental studies, and they open up new lines of inquiry for microbiome scientists, ecologists, and evolutionary biologists.

Reviewer #1 (Public Review):

This paper makes an important contribution to the current debate on whether the diversity of a microbial community has a positive or negative effect on its own diversity at a later time point. In my view, the main contribution is linking the diversity-begets-diversity patterns, already observed by the same authors and others, to genomic signatures of gene loss that would be expected from the Black Queen Hypothesis, establishing an eco-evolutionary link. In addition, they test this hypothesis at a more fine-grained scale (strain-level variation and SNP) and do so in human microbiome data, which adds relevance from the biomedical standpoint. The paper is a well-written and rigorous analysis using state-of-the-art methods, and the results suggest multiple new experiments and testable hypotheses (see below), which is a very valuable contribution.

We thank the reviewer for their generous comments.

That being said, I do have some concerns that I believe should be addressed. First of all, I am wondering whether gene loss could also occur because of environmental selection that is independent of other organisms or the diversity of the community. An alternative hypothesis to the Black Queen is that there might have been a migration of new species from outside and then loss of genes could have occurred because of the nature of the abiotic environment in the new host, without relationship to the community diversity. Telling the difference between these two hypotheses is hard and would require extensive additional experiments, which I don't think is necessary. But I do think the authors should acknowledge and discuss this alternative possibility and adjust the wording of their claims accordingly.

We concur with the reviewer that the drivers of the correlation between community diversity and gene loss are unclear. Therefore, we have now added the following text to the Discussion:

“Here we report that genome reduction in the gut is higher in more diverse gut communities. This could be due to de novo gene loss, preferential establishment of migrant strains encoding fewer genes, or a combination of the two. The mechanisms underlying this correlation remain unclear and could be due to biotic interactions – including metabolic cross-feeding as posited by some models (Estrela et al., 2022; San Roman and Wagner, 2021, 2018) but not others (Good and Rosenfeld, 2022) – or due to unknown abiotic drivers of both community diversity and gene loss.”

Additionally, we have revised Figure 1 to show that strain invasions/replacements, in addition to evolutionary change, could be an important driver of changes in intra-species diversity in the microbiome.

Another issue is that gene loss is happening in some of the most abundant species in the gut. Under Black Queen though, we would expect these species to be most likely "donors" in cross-feeding interactions. Authors should also discuss the implications, limitations, and possible alternative hypotheses of this result, which I think also stimulates future work and experiments.

We thank the reviewer for raising this point. It is unclear to us whether the more abundant species would be donors in cross-feeding interactions. If we understand correctly, the reviewer is suggesting that more abundant donors will contribute more total biomass of shared metabolites to the community. This idea makes sense under the assumption that the abundant species are involved in cross-feeding interactions in the first place, which may or may not be the case. As our work heavily relies on a dataset that we previously analyzed (HMP), we wish to cite Figure S20 in Garud, Good et al. 2019 PLoS Biology in which we found there are comparable rates of gene changes across the ~30 most abundant species analyzed in the HMP. This suggests that among the most abundant species analyzed, there is no relationship between their abundance and gene change rate.

That being said, we acknowledge that our study is limited to the relatively abundant focal species and state now in the Discussion: “Deeper or more targeted sequencing may permit us to determine whether the same patterns hold for rarer members of the microbiome.”

Regarding Figure 5B, there is a couple of questions I believe the authors should clarify. First, How is it possible that many species have close to 0 pathways? Second, besides the overall negative correlation, the data shows some very conspicuous regularities, e.g. many different "lines" of points with identical linear negative slope but different intercept. My guess is that this is due to some constraints in the pathway detection methods, but I struggle to understand it. I think the authors should discuss these patterns more in detail.

We sincerely thank the reviewer for raising this issue, as it prompted us to investigate more deeply the patterns observed at the pathway level. In short, we decided to remove this analysis from the paper because of a number of bioinformatics issues that we realized were contributing to the signal. However, in support of BQH-like mechanisms at play, we do find evidence for gene loss in more diverse communities across multiple species in both the HMP and Poyet datasets. Below we detail our investigation into Figure 5b and how we arrived at the conclusion that is should be removed:

(1) Regarding data points in Figure 5B where many focal species have “zero pathways”,we firstly clarify how we compute pathway presence and richness. Pathway abundance data per species were downloaded from the HMP1-2 database, and these pathway abundances were computed using HUMAnN (HMP Unified Metabolic Analysis Network). According to HUMAnN documentation, pathway abundance is proportional to the number of complete copies of the pathway in the community; this means that if at least one component reaction in a certain pathway is missing coverage (for a sample-species pair), the pathway abundance may be zero (note that HUMAnN also employs “gap filling” to allow no more than one required reaction to have zero abundance). As such, it is likely that insufficient coverage, especially for low-abundance species, causes many pathways to report zero abundance in many species in many samples. Indeed, 556 of the 649 species considered had zero “present” pathways (i.e. having nonzero abundance) in at least 400 of the 469 samples (see figure below).

(2) We thank the reviewer for pointing out the “conspicuous regularities” in Figure 5B,particularly “parallel lines” of data points that we discovered are an artifact of the flawed way in which we computed “community pathway richness [excluding the focal species].” Each diagonal line of points corresponds to different species in the same sample, and because community pathway richness is computed as the total number of pathways [across all species in the sample] minus the number of pathways in the focal species, the current Figure 5B is really plotting y against X-y for each sample (where X is a sample’s total community pathway richness, and y is the pathway richness of an individual species in that sample). This computation fails to account for the possibility that a pathway in an excluded focal species will still be present in the community due to redundancy, and indeed BQH tests for whether this redundancy is kept low in diverse communities due to mechanisms such as gene loss.

We attempted to instead plot community pathway richness defined as the number of unique pathways covered by all species other than the focal species. This is equivalent to [number of unique pathways across all species in a sample] minus the [number of pathways that are ONLY present in the focal species and not any other species in the sample]. However, when we recomputed community pathway richness this way, it is rare that a pathway is present in only one species in a sample. Moreover, we find that with the exception of E. coli, focal species pathway richness tended to be very similar across the 469 samples, often reaching an upper limit of focal species pathway richness observed. (It is unclear to what extent lower pathway richnesses are due to low species abundance/low sample coverage versus gene loss). This new plot reveals even more regularities and is difficult to interpret with respect to BQH. (Note that points are colored by species; the cluster of black dots with outlying high focal pathway richness corresponds to the “unclassified” stratum which can be considered a group of many different species.)

Overall, because community pathway richness (excluding a focal species) seems to primarily vary with sample rather than focal species in this dataset when using the most simple/strict definition of community pathway richness as described above, it is difficult to probe the Black Queen Hypothesis using a plot like Figure 5B. As pointed out by reviewers, lack of sequencing depth to analyze strain-level diversity and accurately quantify pathway abundance, irrespective of species abundance, seems to be a major barrier to this analysis. As such, we have decided to remove Figure 5B from the paper and rewrite some of our conclusions accordingly.

Finally, I also have some conceptual concerns regarding the genomic analysis. Namely, genes can be used for biosynthesis of e.g. building blocks, but also for consumption of nutrients. Under the Black Queen Hypothesis, we would expect the adaptive loss of biosynthetic genes, as those nutrients become provided by the community. However, for catabolic genes or pathways, I would expect the opposite pattern, i.e. the gain of catabolic genes that would allow taking advantage of a more rich environment resulting from a more diverse community (or at least, the absence of pathway loss). These two opposing forces for catabolic and biosynthetic genes/pathways might obscure the trends if all genes are pooled together for the analysis. I believe this can be easily checked with the data the authors already have, and could allow the authors to discuss more in detail the functional implications of the trends they see and possibly even make a stronger case for their claims.

We thank the reviewer for their suggestion. As explained above, we have removed the pathway analysis from the paper due to technical reasons. However, we did investigate catabolic and biosynthetic pathways separately as suggested by the reviewer as we describe below:

We obtained subsets of biosynthetic pathways and catabolic pathways by searching for keywords (such as “degradation” for catabolic) in the MetaCyc pathway database. After excluding the “unclassified” species stratum, we observe a total of 279 biosynthetic and 167 catabolic pathways present in the HMP1-2 pathway abundance dataset. Using the corrected definition of community pathway richness excluding a focal species, for each pathway type—either biosynthetic or catabolic—we plotted focal species pathway richness against community pathway richness including all pathways regardless of type:

We observe the same problem where, within a sample, community pathway richness excluding the focal species hardly varies no matter which focal species it is, due to nearly all of its detected pathways being present in at least one other species; this makes the plots difficult to interpret.

Reviewer #2 (Public Review):

The authors re-analysed two previously published metagenomic datasets to test how diversity at the community level is associated with diversity at the strain level in the human gut microbiota. The overall idea was to test if the observed patterns would be in agreement with the "diversity begets diversity" (DBD) model, which states that more diversity creates more niches and thereby promotes further increase of diversity (here measured at the strain-level). The authors have previously shown evidence for DBD in microbiomes using a similar approach but focusing on 16S rRNA level diversity (which does not provide strain-level insights) and on microbiomes from diverse environments.

One of the datasets analysed here is a subset of a cross-sectional cohort from the Human Microbiome Project. The other dataset comes from a single individual sampled longitudinally over 18 months. This second dataset allowed the authors to not only assess the links between different levels of diversity at single timepoints, but test if high diversity at a given timepoint is associated with increased strain-level diversity at future timepoints.

Understanding eco-evolutionary dynamics of diversity in natural microbial communities is an important question that remains challenging to address. The paper is well-written and the detailed description of the methodological approaches and statistical analyses is exemplary. Most of the analyses carried out in this study seem to be technically sound.

We thank the reviewer for their kind words, comments, and suggestions.

The major limitation of this study comes with the fact that only correlations are presented, some of which are rather weak, contrast each other, or are based on a small number of data points. In addition, finding that diversity at a given taxonomic rank is associated with diversity within a given taxon is a pattern that can be explained by many different underlying processes, e.g. species-area relationships, nutrient (diet) diversity, stressor diversity, immigration rate, and niche creation by other microbes (i.e. DBD). Without experiments, it remains vague if DBD is the underlying process that acts in these communities based on the observed patterns.

We thank the reviewer for their comments. First, regarding the issue of this being a correlative study, we now more clearly acknowledge that mechanistic studies (perhaps in experimental settings) are required to fully elucidate DBD and BQH dynamics. However, we note that our correlational study from natural communities is complementary to experimental and modeling studies, to test the extent to which their predictions hold in more complex, realistic settings. This is now mentioned throughout the manuscript, most explicitly at the end of the Introduction:

“Although such analyses of natural diversity cannot fully control for unmeasured confounding environmental factors, they are an important complement to controlled experimental and theoretical studies which lack real-world complexity.”

Second, to increase the number of data points analyzed in the Poyet study, we now include 15 species and four different hosts (new Figure 5). The association between community diversity and gene loss is now much more statistically robust, and consistent across the Poyet and HMP time series.

Third, we acknowledge more clearly in the Discussion that other processes, including diet and other environmental factors can generate the DBD pattern. We also now stress more prominently the possibility that strain migration across hosts may be responsible for the patterns observed. For example, in Figure 1, we illustrate the possibility of strain migration generating the patterns we observe.

Below we quote a paragraph that we have now added in the Discussion:

"Second, we cannot establish causal relationships without controlled experiments. We are therefore careful to conclude that positive diversity slopes are consistent with the predictions of DBD, and negative slopes with EC, but unmeasured environmental drivers could be at play. For example, increased dietary diversity could simultaneously select for higher community diversity and also higher intra-species diversity. In our previous study, we found that positive diversity slopes persisted even after controlling for potential abiotic drivers such as pH and temperature (Madi et al., 2020), but a similar analysis was not possible here due to a lack of metadata. Neutral processes can account for several ecological patterns such as species-area relationships (Hubbell, 2001), and must be rejected in favor of niche-centric models like DBD or EC. Using neutral models without DBD or EC, we found generally flat or negative diversity slopes due to sampling processes alone and that positive slopes were hard to explain with a neutral model (Madi et al., 2020). These models were intended mainly for 16S rRNA gene sequence data, but we expect the general conclusions to extend to metagenomic data. Nevertheless, further modeling and experimental work will be required to fully exclude a neutral explanation for the diversity slopes we report in the human gut microbiome.”

Finally, we now put more emphasis on the importance of migration (strain invasion) as a non-exclusive alternative to de novo mutation and gene gain/loss. This is mentioned in the Abstract and is also illustrated in the revised Figure 1.

Another limitation is that the total number of reads (5 mio for the longitudinal dataset and 20 mio for the cross-sectional dataset) is low for assessing strain-level diversity in complex communities such as the human gut microbiota. This is probably the reason why the authors only looked at one species with sufficient coverage in the longitudinal dataset.

Indeed, this is a caveat which means we can only consider sub-species diversity in relatively abundant species. Nevertheless, this allows us to study dozens of species in the HMP and 15 in the more frequent Poyet time series. As more deeply sequenced metagenomes become available, future studies will be able to access the rarer species to test whether the same patterns hold or not. This is now mentioned prominently as a caveat our study in the second Discussion paragraph:

“First, using metagenomic data from human microbiomes allowed us to study genetic diversity, but limited us to considering only relatively abundant species with genomes that were well-covered by short sequence reads. Deeper or more targeted sequencing may permit us to determine whether the same patterns hold for rarer members of the microbiome. However, it is notable that the majority of the dozens of species across the two datasets analyzed support DBD, suggesting that the phenomenon may generalize.”

We also note that rarefaction was only applied to calculate community richness, not to estimate sub-species diversity. We apologize for this confusion, which is now clarified in the Methods as follows:

“SNV and gene content variation within a focal species were ascertained only from the full dataset and not the rarefied dataset.”

Analyzing the effect of diversity at a given timepoint on strain-level diversity at a later timepoint adds an important new dimension to this study which was not assessed in the previous study about the DBD in microbiomes by some of the authors. However, only a single species was analysed in the longitudinal dataset and comparisons of diversity were only done between two consecutive timepoints. This dataset could be further exploited to provide more insights into the prevailing patterns of diversity.

We thank the reviewer for raising this point. We now have considered all 15 species for which there was sufficient coverage from the Poyet dataset, which included four different stool donors. Additionally, in the HMP dataset, we analyze 54 species across 154 hosts, with both datasets showing the same correlation between community diversity and gene loss.

Additionally, we followed the suggestion of the reviewer of examining additional time lags, and in Figure 5 we do observe a dependency on time. This is now described in the Results as follows:

“Using the Poyet dataset, we asked whether community diversity in the gut microbiome at one time point could predict polymorphism change at a future time point by fitting GAMs with the change in polymorphism rate as a function of the interaction between community diversity at the first time point and the number of days between the two time points. Shannon diversity at the earlier time point was correlated with increases in polymorphism (consistent with DBD) up to ~150 days (~4.5 months) into the future (Figure S4), but this relationship became weaker and then inverted (consistent with EC) at longer time lags (Fig 5A, Table S8, GAM, P=0.023, Chi-square test). The diversity slope is approximately flat for time lags between four and six months, which could explain why no significant relationship was found in HMP, where samples were collected every ~6 months. No relationship was observed between community richness and changes in polymorphism (Table S8, GAM, P>0.05).”

Finally, the evidence that gene loss follows increase in diversity is weak, as very few genes were found to be lost between two consecutive timepoints, and the analysis is based on only a single species. Moreover, while positive correlation were found between overall community diversity and gene family diversity in single species, the opposite trend was observed when focusing on pathway diversity. A more detailed analysis (of e.g. the functions of the genes and pathways lost/gained) to explain these seemingly contrasting results and a more critical discussion of the limitations of this study would be desirable.

We agree that our previous analysis of one species in one host provided weak support for gene loss following increases in diversity. As described in the response above, we have now expanded this analysis to 15 focal species and 4 independent hosts with extensive time series. We now analyze this larger dataset and report the more statistically robust results as follows:

“We found that community Shannon diversity predicted future gene loss in a focal species, and this effect became stronger with longer time lags (Fig 5B, Table S9, GLMM, P=0.006, LRT for the effect of the interaction between the initial Shannon diversity and time lag on the number of genes lost). The model predicts that increasing Shannon diversity from its minimum to its maximum would result in the loss of 0.075 genes from a focal species after 250 days. In other words, about one of the 15 focal species considered would be expected to lose a gene in this time frame.

Higher Shannon diversity was also associated with fewer gene gains, and this relationship also became stronger over time (Fig 5C, Table S9, GLMM, P=1.11e-09, LRT). We found a similar relationship between community species richness and gene gains, although the relationship was slightly positive at shorter time lags (Fig 5D, Table S9, GLMM, P=3.41e-04, LRT). No significant relationship was observed between richness and gene loss (Table S9, GLMM, P>0.05). Taken together with the HMP results (Fig 4), these longer time series reveal how the sign of the diversity slope can vary over time and how community diversity is generally predictive of reduced focal species gene content.”

As described in detail in the response to Reviewer 1 above, we found that the HUMAnN2 pathway analyses previously described suffered from technical challenges and we deemed them inconclusive. We have therefore removed the pathway results from the manuscript.

Reviewer #3 (Public Review):

This work provides a series of tests of hypothesis, which are not mutually exclusive, on how genomic diversity is structured within human microbiomes and how community diversity may influence the evolution of a focal species.

Strengths:

The paper leverages on existing metagenomic data to look at many focal species at the same time to test for the importance of broad eco-evolutionary hypothesis, which is a novelty in the field.

Thank you for the succinct summary and recognition of the strengths of our work.

Weaknesses:

It is not very clear if the existing metagenomic data has sufficient power to test these models.

It is not clear, neither in the introduction nor in the analysis what precise mechanisms are expected to lead to DBD.

The conclusion that data support DBD appears to depend on which statistics to measure of community diversity are used. Also, performing a test to reject a null neutral model would have been welcome either in the results or in the discussion.

In our revised manuscript, we emphasize several caveats – including that we only have power to test these hypotheses in focal species with sufficient metagenomic coverage to measure sub-species diversity. We also describe more in the Introduction how the processes of competition and niche construction can lead to DBD. We also acknowledge that unmeasured abiotic drivers of both community diversity and sub-species diversity could also lead to the observed patterns. Throughout the manuscript, we attempt to describe the results and acknowledge multiple possible interpretations, including DBD and EC acting with different strengths on different species and time scales. Our previous manuscript assessing the evidence for DBD using 16S rRNA gene amplicon data from the Earth Microbiome Project (Madi et al., eLife 2020) assessed null models based on neutral ecological theory, and found it difficult to explain the observation of generally positive diversity slopes without invoking a non-neutral mechanism like DBD. While a new null model tailored to metagenomic data might provide additional nuance, we think developing one is beyond the scope of the manuscript – which is in the format of a short ‘Research Advance’ to expand on our previous eLife paper, and we expect that the general results of our previously reported null model provide a reasonable intuition for our new metagenomic analysis. This is now mentioned in the Discussion as follows:

“In our previous study, we found that positive diversity slopes persisted even after controlling for potential abiotic drivers such as pH and temperature (Madi et al., 2020), but a similar analysis was not possible here due to a lack of metadata. Neutral processes can account for several ecological patterns such as species-area relationships (Hubbell, 2001), and must be rejected in favor of niche-centric models like DBD or EC. Using neutral models without DBD or EC, we found generally flat or negative diversity slopes due to sampling processes alone and that positive slopes were hard to explain with a neutral model (Madi et al., 2020). These models were intended mainly for 16S rRNA gene sequence data, but we expect the general conclusions to extend to metagenomic data. Nevertheless, further modeling and experimental work will be required to fully exclude a neutral explanation for the diversity slopes we report in the human gut microbiome.”

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):

Zou et al. presented a comprehensive study where they generated single-cell RNA profiling of 138,982 cells from 13 samples of six patients including AK, squamous cell carcinoma in situ (SCCIS), cSCC, and their matched normal tissues, covering comprehensive clinical courses of cSCC. Using bioinformatics analysis, they identified keratinocytes, CAFs, immune cells, and their subpopulations. The authors further compared signatures within subpopulations of keratinocytes along with the clinical progression, especially basal cells, and identified many interesting genes. They also further validate some of the markers in an independent cohort using IHC, followed by some knockdown experiments using cSCC cell lines.

The strength of this study is the unique data set they have created, providing the community with invaluable resources to study and validate their findings. However, a lot of analyses were not robust enough to support the claims and conclusions in the paper. More clarification and cross-comparison with polished data are needed to further strengthen the study and claims.

1) Stemness markers were used. The authors used COL17A1, TP63, ITGB1, and ITGA3 to represent stemness markers. However, these were not common classic stemness markers used in cSCC. What is the source claiming these genes were stemness markers in cSCC? TP63 is a master regulator and early driver event in SCC, while COL17A1, ITGB1, and ITGA3 are all ECM genes. The authors need to use commonly well-known stem cell markers in cSCC, e.g., LGR5, to mark stem-like cells.

Thanks for raising this good point. We may not have provided a clear description of the markers COL17A1, TP63, ITGB1, and ITGA3 in the previous texts. We would like to clarify that these genes were used as the markers of epidermal stem cells in normal skin samples rather than tumor stem cells in cSCC. To avoid any possible misunderstanding, we revised the main text accordingly and added the references [4-11].

2) Cell proportion analysis. The authors used the mean proportions to compare different clinical groups for subpopulations of keratinocytes, e.g., Figure 2B, and Figure 5B. This is not robust, as no statistics can be derived from this. For example, from Fig 2A, it is clearly shown there is a high level of heterogeneity of cellular compositions for normal samples. One cannot say which group is higher or lower simply based on mean not variance as well.

We replotted the proportion analysis with statistics and presented the new graphs in Figure 2-figure supplement 1 for Figure 2B and Figure 5-figure supplement 1 for Figure 5B.

3) Basal tumour cells in SCCIS and SCC. To make the findings valid, authors need to compare these cells/populations with the keratinocyte cell populations defined by Ji et al. Cell 2020. Do basal-SCCIS-tumours cells, also in SCC samples, resemble any of the population defined in Ji et al. Ji et al. also had 10 match normal, thus the authors need to validate their findings of SCC vs normal analysis using the Ji et al. dataset.

Thanks for this valuable suggestion. We compared basal tumor cell in our study with the cell populations defined in Ji et al. Cell 2020 data using SingleCellNet [1]. The results showed that both the basal-SCCIS-tumor cells of SCCIS and basal tumor cells of cSCC in our study closely resemble the Tumor_KC_Basal subcluster defined in Ji et al’s paper (Figure 4-figure supplement 4, C and D). Tumor_KC_Basal highly expressed CCL2, CXCL14, FTH1, MT2A, which is consistent with our findings in basal tumor cells.

4) Copy number analysis. Authors used inferCNV to perform copy number analysis using scRNA-seq data and identified CNVs in subpopulations of keratinocytes in SCCIS and SCC. To ensure these CNVs were not artefacts, were some of the CNVs identified by inferCNV well-known copy number changes previously reported in cSCC?

In poorly-differentiated cSCC sample, the significant gains in chromosome 7, 9 and deletion in chromosome 10 were reported in previous study, indicating the reliability of the CNV analysis results (Figure 5-figure supplement 2) [12].

5) Pseudotime analysis lines 308-313. Not sure the pseudotime analysis added much as, as it is unclear two distinct subgroups were identified from this analysis. Suggest removing this to keep it neater

Thank you for this suggestion. We have deleted the result of pseudotime analysis.

6) Selection of candidate genes for validation using IHC and cell line work. For example, lines 205-206, lines 352-356 and lines 437-441, authors selected several genes associated with AK and SCC to further validate using IHC and cell line knockdown work. What are the criteria for selecting those genes for validation? It is unclear to readers how these were selected. It reads like a fishing experiment, then followed by a knockdown. Clear rationale/criteria need to be elaborated.

The first consideration of candidate gene selection is the fold change of expression. We have provided the statistical results of DEGs in Supplementary file 1b, 1h, 1j-1m. Then we selected top changed genes and conducted an extensive literature search on these genes. We prioritized genes that, although not directly associated with cSCC development, have a close relationship with related pathways, as determined through functional enrichment analysis. These genes were arranged for further verification experiments. We have added more details in main text and methods section.

7) TME. Compared to keratinocytes populations, the investigation of TME cells was weak. (a) can authors produce UMAP files just for T cells, DC cells, and fibroblasts separately? Figure 7B is not easy to see those subclusters. (b) similar to what was done for keratinocytes, can authors find differentially expressed clusters and genes among the different clinical groups, associated with disease progression? (c) where are the myeloid cell populations, also B cells?

Thank you for your suggestions. (a) We have added the UMAP files for T cells, DC cells and stromal cells separately in new Figure 7A. (b) We identified DEGs in TME cells among the different groups. Several key genes showed monotonically changing trends associated with disease progression. For example, with the increase of malignancy, FOS shows down-regulation while S100A8 and S100A9 monotonically increase in all three types of TME cells (Figure 7C). (c) We identified two types of myeloid cell populations, macrophage and monocyte derived DCs (MoDC). We didn’t find other myeloid cells, such as neutrophil. For B cells, there were only 28 B cells in poorly-differentiated cSCC sample, which didn’t meet the threshold for further cell-cell communication analysis.

8) Heat shock protein genes line 327-329. HSP signature was well-known to be induced via tissue dissociation and library prep during the scRNA experiment. How could the authors be sure these were not artefacts induced by the experiment? If authors regress their gene expression against HSP gene signatures, would this cluster still be identified?

Thank you for this valuable suggestion. It is important to note that the Basal-SCCIS-tumor cluster was identified through CNV analysis, rather than the HSP signature. To address this concern and further validate this result, “AddModuleScore” function in Seurat package was used to regress gene expression against HSP gene signatures for retrieved basal cells. Our result showed that Basal_SCCIS tumor population still can be identified after regression, even more clearly (Author response image 1).

Author response image 1.

The identity of Basal-SCCIS-tumor cluster considering regression against HSP signatures.

9) Cell-cell communication analysis. The authors claimed that that cell-to-cell interaction was significantly enhanced in poorly-differentiated cSCC, and multiple interaction pathways were significantly active. How was this kind of analysis carried out? How did the authors define significance? what statistical method was used? these were all unclear. Furthermore, it is difficult to judge the robustness of the cell-cell communication analysis. Were these findings also supported by another method, such as celltalker, and cellphoneDB?

To determine the significance of the increased overall cell-to-cell interaction strength between two groups, we utilized CellChat to obtain the communication strength in different samples. We combined the communication strength based on cell type pairs, where missing values were set to 0. We performed a paired Wilcoxon test to determine whether the enhancement of cell-to-cell interaction between samples was significant.

For the comparison of outgoing or incoming interaction strength of the same cell types between two groups, we first extracted the communication strength of each signal pathway contributing to outgoing or incoming strength, and then merged the strengths of signal pathways among samples, where the strength of non-shared pathways with missing value was determined to be 0. Subsequently, we performed a paired Wilcoxon test to define the significance.

For multiple groups comparisons, the Kruskal-Wallis rank sum test was first performed. If the p-value is less than 0.1, the pairwise Wilcoxon test was used for subsequent pairwise comparisons. The comparison of individual signaling pathways between groups is similar to the above. We defined p-value < 0.1 as significance threshold. We have added the significance test method in figure legend for Figure 7 and Figure 8 as well as and detailed statistical data in new Supplementary file 1q-1u.

As suggested, we also used the approach of CellPhoneDB based on CellChatDB database to verify our cell-cell communication results. There are 55-58% of the ligand-receptor interactions predicted by CellChat were also predicted by CellPhoneDB (Author response image 2). The enhancement of cell interaction through MHC-II, Laminin and TNF signaling pathways in poorly-differentiated cSCC sample compare to normal sample were consistent in both CellChat and CellPhoneDB (Figure 8C and Figure 8-figure supplement 1B).

Author response image 2.

The overlap of the predicted ligand-receptor interactions between CellChat and CellPhoneDB.

10) Statistics and significance. In general, the detail of statistics and significance was lacking throughout the paper. Authors need to specify what statistical tests were used, and the p-values. It is difficult to judge the correctness of the test, and robustness without seeing the stats.

We have included all statistics and significance values in the figure legend and supplemental tables, and described the statistical tests in the methods section. In this revision, we have added the necessary details of statistics and significance in the main text and figures.

11) Overall, this manuscript needs a lot of re-writing. A lot of discussion was also included in the results, making it really difficult to read overall. The authors should simplify the results sections, remove the discussion bits, and further highlight and streamline with the key results of this paper.

Thanks a lot for this advice. We have revised the paper thoroughly, removed discussion in results section to make the manuscript easier to read.

Author Response:

Reviewer #1 (Public Review):

5.The reported data point to an important role of the premotor and parietal regions of the left as compared to the right hemisphere in the control of ipsilateral and contralateral limb movements. These are also the regions where the electrodes were primarily located in both subgroups of patients. I have 2 concerns in this respect. The first concern refers to the specific locus of these electrodes. For premotor cortex, the authors suggest PMd as well as PMv as potential sites for these bilateral representations. The other principal site refers to parietal cortex but this covers a large territory. It would help if more specific subregions for the parietal cortex can be indicated, if possible. Do the focal regions where electrodes were positioned refer to the superior vs inferior parietal cortex (anterior or posterior), or intra-parietal sulcus. Second, the manuscript's focus on the premotor-parietal complex emerges from the constraints imposed by accessible anatomical locations in the participants but does not preclude the existence of other cortical sites as well as subcortical regions and cerebellum for such bilateral representations. It is meaningful to clarify this and/or list this as a limitation of the current approach.

On the first issue, we have updated the manuscript to specify the subregion within the parietal cortex in which we see stronger across-arm generalization - namely, the superior parietal cortex. On the second issue, we have added text in the Discussion that reference subcortical areas shown to exhibit laterality differences in bimanual coordination, providing a more holistic picture of bimanual representations across the brain. In addition, we acknowledge that with our current patient population we are limited to regions with substantial electrode coverage, which does not include all areas of the brain.

6.The evidence for bilateral encoding during unilateral movement opens perspectives for a better understanding of the control of bimanual movements which are abundant during every day life. In the discussion, the authors refer to some imaging studies on bimanual control in order to infer whether the obtained findings may be a consequence of left hemisphere specialization for bimanual movement control, leading to speculations about the information that is being processed for each of both limb movements. Another perspective to consider is the possibility that making a movement with one limb may require postural stabilization in the trunk and contralateral body side, including a contribution from the opposite limb that is supposedly resting on the start button. Have the authors considered whether this postural mechanism could (partly) account for this bilateral encoding mechanism, in particular, because it appears more prominent during movement execution as compared to preparation. Furthermore, could the prominence of bilateral encoding during movement execution be triggered by inflow of sensory information about both limbs from the visual as well as the somatosensory systems.

Thank you for these comments. We have added a paragraph to the Discussion to address the hypothesis that some component of ipsilateral encoding may be related to postural stabilization.

In response to the final point in this comment, we agree that bilateral information during execution could be reflective of afferent inputs (somatosensory and/or visual). However, the encoding model shows that activity in premotor and parietal regions are well predicted based on kinematics during the task. While visual and somatosensory system information are likely integrated in these areas, the kinematic encoding would point to a more movement-based representation.

Reviewer #2 (Public Review):

Weaknesses: 1. Although the current human ECoG data set is valuable, there is still large variability in electrode coverage across the patients (I fully acknowledge the difficulty). This makes statistical assessment a bit tricky. The potential factors of interest in the current study would be Electrode (=Region), Subject, Hemisphere, and their interactions. The tricky part is that Electrode is nested within Subject, and Subject is nested within Hemisphere. Permutation-based ANOVA used for the current paper requires proper treatment of these nested factors when making permutations (Anderson and Braak, 2003). With this regard, sufficient details about how the authors treated each factor, for instance, in each pbANOVA, are not provided in the current version of the manuscript. Similarly, the scope of statistical generalizability, whether the inference is within-sample or population-level, for the claims (e.g., statement about the hemispheric or regional difference) needs to be clarified.

We discuss at length the issue of electrode variability and have addressed this in the revised manuscript. Graphically, we have added a Supplemental Figure (S2). Statistically, we appreciate the point about the need for the analysis to address the nested structure of the data. We have redone all of the statistics, now using a permutation-based linear mixed effects model with a random effect of patient. This approach did not change any of the findings.

As to the comment about hemispheric or regional differences, the data show that both are important factors. Our hemispheric effect is characterized by stronger ipsilateral encoding in the left hemisphere and subsequently better across-arm generalization (Figures 2-4). We then examine the spatial distribution of electrodes that generalized well or poorly and found clusters in both hemispheres of electrodes that generalize poorly. In contrast, only in the left hemisphere did we find clusters of electrodes that generalize well. These electrodes were localized to PMd, PMv and superior parietal cortex (Fig 5D). In summary, we argue that activity patterns in M1 are similar in the left and right hemispheres, but there is a marked asymmetry for activity patterns over premotor and parietal cortices.

Additional contexts that would help readers interpret or understand the significance of the work: The greater amount of shared movement representation in the left hemisphere may imply the greater reliance of the left arm on the left hemisphere. This may, in turn, lead to the greater influence of the ongoing right arm motion on the left arm movement control during the bimanual coordination. Indeed, this point is addressed by the authors in the Discussion (page 15, lines 26-41). One critical piece of literature missing in this context is the work done by Yokoi, Hirashima, and Nozaki (2014). In the experiments using the bimanual reaching task, they in fact found that the learning by the left arm is to the greater degree influenced by the concurrent motion of the right arm than vice versa (Yokoi et al., J Neurosci, 2014). Together with Diedrichsen et al. (2013), this study will strengthen the authors' discussion and help readers interpret the present result of left hemisphere dominance in the context of more skillful bimanual action.

The Yokoi paper is a very important paper in revealing hemispheric asymmetries during skilled bimanual movements. However, we think it is problematic to link the hemispheric asymmetries we observe to the behavioral effects reported in the Yokoi paper (namely, that the nondominant, left arm was more strongly influenced by the kinematics of the right arm). One could hypothesize that the left hemisphere, given its representation of both arms, could be controlling both arms in some sort of direct way (and thus the action of the right arm will have an influence on left arm movement given the engagement of the same neural regions for both movements). It is also possible that the left hemisphere is receiving information about the state of both the right and left arms, and this underlies the behavioral asymmetry reported in Yokoi.

Reviewer #3 (Public Review):

In the present work, Merrick et al. analyzed ECoG recordings from patients performing out-and-back reaching movements. The authors trained a linear model to map kinematic features (e.g., hand speed, target position) to high frequency ECoG activity (HFA) of each electrode. The two primary findings were: 1) encoding strength (as assessed by held-out R2 values) of ipsilateral and contralateral movements was more bilateral in the left hemisphere than in the right and 2) across-arm generalization was stronger in the left hemisphere than in the right. As the authors point out in the Introduction, there are known 'asymmetries between the two hemispheres in terms of praxis', so it may not be surprising to find asymmetries in the kinematic encoding of the two hemispheres (i.e., the left hemisphere contributes 'more equally' to movements on either side of the body than the right hemisphere).

There is one point that I feel must be addressed before the present conclusions can be reached and a second clarification that I feel will greatly improve the interpretability of the results.

First, as is often the case when working with patients, the authors have no control over the recording sites. This led to some asymmetries in both the number of electrodes in each hemisphere (as the authors note in the Discussion) and (more importantly) in the location of the recording electrodes. Recording site within a hemisphere must be controlled for before any comparisons between the hemispheres can be made. For example, the authors note that 'the contralateral bias becomes weaker the further the electrodes are from putative motor cortex'. If there happen to be more electrodes placed further from M1 in the left hemisphere (as Supplementary Figure 1 seems to suggest), than we cannot know whether the results of Figures 2 and 3 are due to the left hemisphere having stronger bilateral encoding or simply more electrodes placed further from M1.

The reviewer makes a very valid point and this comment has led to our inclusion of a new Supplementary Figure, S2, in which we quantify the percentage of electrodes in each subregion.

Second, it would be useful if the authors provided a bit of clarification about what type of kinematic information the linear model is using to predict HFA. I believe the paragraph titled 'Target modulation and tuning similarity across arms' suggests that there is very little across-target variance in the HFA signal. Does this imply that the model is primarily ignoring the Phi and Theta (as well as their lagged counterparts) and is instead relying on the position and speed terms? How likely is it that the majority of the HFA activity around movement onset reflects a condition-invariant 'trigger signal' (Kaufman, et al., 2016). This trigger signal accounts for the largest portion of neural variance around movement onset (by far), and the weight of individual neurons in trigger signal dimensions tend to be positive, which means that this signal will be strongly reflected in population activity (as measured by ECoG). This interpretation does not detract from the present results in any way, but it may serve to clarify them.

To address this comment, we have added a new figure (Fig 6) which shows the relative contribution of each kinematic feature as well as their average weights across time for both contralateral and ipsilateral movements. This figure also addresses the reviewer’s question about the contribution of the target position to the model. As can be seen, features that reflect timing/movement initiation (position, speed) make a larger contribution compared to the two features which capture directional tuning (theta, phi). As the reviewer suggested, this result is in line Kaufman et al. (2016) which reported that a condition-invariant ‘trigger signal’ comprises the largest component of neural activity. We note that the target dependent features theta and phi still make a substantial contribution to the model (relative contribution: contra = 32%, ipsi = 37%). Previously, we have tested the contribution of the theta and phi features by comparing two models, one that only used position and speed (Movement model) and one that also included the two angular components phi and theta (Target Model). For a subset of electrodes, the held-out predictions were significantly better using the Target Model, a result we take as further evidence of electrode tuning within our dataset.

The figure below shows an electrode located in M1 that is tuned to targets when the patient reached with their contralateral arm as an example. We believe that having an explicit depiction of how the four features contribute to the HFA predictions will help the reader evaluate the model. These points are now addressed in the text in the results section discussing Figure 6.

Author Response

Reviewer #3 (Public Review):

This manuscript by Pendse et al aimed to identify the role of the complement component C1q in intestinal homeostasis, expecting to find a role in mucosal immunity. Instead, however, they discovered an unexpected role for C1qa in regulating gut motility. First, using RNA-Seq and qPCR of cell populations isolated either by mechanical separation or flow cytometry, the authors found that the genes encoding the subunits of C1q are expressed predominantly in a sub-epithelial population of cells in the gut that Cd11b+MHCII+F4/80high, presumably macrophages. They support this conclusion by analyzing mice in which intestinal macrophages are depleted with anti-CSF1R antibody treatment and show substantial loss of C1qa, b and c transcripts. Then, they generate Lyz2Cre-C1qaflx/flx mice to genetically deplete C1qa in macrophages and assess the consequences on the fecal microbiome, transcript levels of cytokines, macromolecular permeability of the epithelial barrier, and immune cell populations, finding no major effects. Furthermore, provoking intestinal injury with chemical colitis or infection (Citrobacter) did not reveal macrophage C1qa-dependent changes in body weight or pathogen burden.

Then, they analyzed C1q expression by IHC of cross-sections of small and large intestine and find that C1q immunoreactivity is detectable adjacent to, but not colocalizing with, TUBB3+ nerve fibers and CD169+ cells in the submucosa. Interestingly, they find little C1q immunoreactivity in the muscularis externa. Nevertheless, they perform RNA-sequencing of LMMP preparations (longitudinal muscle with adherent myenteric plexus) and find a number of changes in gene ontology pathways associates with neuronal function. Finally, they perform GI motility testing on the conditional knockout mice and find that they have accelerated GI transit times manifesting with subtle changes in small intestinal transit and more profound changes in measures of colonic motility.

Overall, the manuscript is very well-written and the observation that macrophages are the major source of C1q in the intestine is well supported by the data, derived from multiple approaches. The observations on C1q localization in tissue and the strength of the conclusions that can be drawn from their conditional genetic model of C1qa depletion, however, would benefit from more rigorous validation.

1) Interpretation of the majority of the findings in the paper rest on the specificity of the Lyz2 Cre for macrophages. While the specificity of this Cre to macrophages and some dendritic cells has been characterized in the literature in circulating immune cells, it is not clear if this has been characterized at the tissue level in the gut. Evidence demonstrating the selectivity of Cre activity in the gut would strengthen the conclusions that can be drawn.

As indicated by the reviewer, Cre expression driven by the Lyz2 promoter is restricted to macrophages and some myeloid cells in the circulation (Clausen et al., 1999). To better understand intestinal Lyz2 expression at a cellular level, we analyzed Lyz2 transcripts from a published single cell RNAseq analysis of intestinal cells (Xu et al., 2019; see Figure below). These data show that intestinal Lyz2 is also predominantly expressed in gut macrophages with limited expression in dendritic cells and neutrophils.

Figure. Lyz2 expression from single cell RNAseq analysis of mouse intestinal cells. Data are from Xu et al., Immunity 51, 696-708 (2019). Analysis was done through the Single Cell Portal, a repository of scRNAseq data at the Broad Institute.

Additionally, our study shows that intestinal C1q expression is restricted to macrophages (CD11b+MHCII+F4/80hi) and is absent from other gut myeloid cell lineages (Figure 1E-H). This conclusion is supported by our finding that macrophage depletion via anti-CSF1R treatment also depletes most intestinal C1q (Figure 2A-C). Importantly, we found that the C1qaDMf mice retain C1q expression in the central nervous system (Figure 2 – figure supplement 1). Thus, the C1qaDMf mice allow us to assess the function of macrophage C1q in the gut and uncouple the functions of macrophage C1q from those of C1q in the central nervous system.

2) Infectious and inflammatory colitis models were used to suggest that C1qa depletion in Lyz2+ lineage cells does not alter gut mucosal inflammation or immune response. However, the phenotyping of the mice in these models was somewhat cursory. For example, in DSS only body weight was shown without other typical and informative read-outs including colon length, histological changes, and disease activity scoring. Similarly, in Citrobacter only fecal cfu were measured. Especially if GI motility is accelerated in the KO mice, pathogen burden may not reflect efficiency of immune-mediated clearance alone.

We have added additional results which support our conclusion that C1qaDMf mice do not show a heightened sensitivity to acute chemically induced colitis. In Figure 3 – figure supplement 1 we now show a histological analysis of the small intestines of DSS-treated C1qafl/fl and C1qaΔMφ mice. This analysis shows that C1qaDMf mice have similar histopathology, colon lengths, and histopathology scores following DSS treatment. Likewise, our revised manuscript includes histological images of the colons of Citrobacter rodentium-infected C1qafl/fl and C1qaΔMφ mice showing similar pathology (Figure 3 – figure supplement 2).

3) The evidence for C1q expression being restricted to nerve-associated macrophages in the submucosal plexus was insufficient. Localization was shown at low magnification on merged single-planar images taken from cross-sections. The data shown in Figure 4C is not of sufficient resolution to support the claims made - C1q immunoreactivity, for example, is very difficult to even see. Furthermore, nerve fibers closely approximate virtually type of macrophage in the gut, from those in the lamina propria to those in the muscularis….Finally, the resolution is too low to rule out C1q immunoreactivity in the muscularis externa.

Similar points were raised by Reviewer 2. Our original manuscript claimed that C1q-expressing macrophages were mostly located near enteric neurons in the submucosal plexus but were largely absent from the myenteric plexus. However, as both Reviewers have pointed out, this conclusion was based solely on our immunofluorescence analysis of tissue cross-sections.

To address this concern we further characterized C1q+ macrophage localization by performing a flow cytometry analysis on macrophages isolated from the mucosa (encompassing both the lamina propria and submucosa) and the muscularis, finding similar levels of C1q expression in macrophages from both tissues (Figure 4 – figure supplement 1 in the revised manuscript). Although the mucosal macrophage fraction encompasses both lamina propria and submucosal macrophages, our immunofluorescence analysis (Figure 4 B and C) suggests that the mucosal C1q-expressing macrophages are mostly from the submucosal plexus. This observation is consistent with the immunofluorescence studies of CD169+ macrophages shown in Asano et al., which suggest that most C169+ macrophages are located in or near the submucosal region, with fewer near the villus tips (Fig. 1e, Nat. Commun. 6, 7802).

Most importantly, our flow cytometry analysis indicates that the muscularis/myenteric plexus harbors C1q-expressing macrophages. To further characterize C1q expression in the muscularis, we performed RNAscope analysis by confocal microscopy of the myenteric plexus from mouse small intestine and colon (Figure 4D). The results show numerous C1q-expressing macrophages positioned close to myenteric plexus neurons, thus supporting the flow cytometry analysis. We note that although the majority of C1q immunofluorescence in our tissue cross-sections was observed in the submucosal plexus, we did observe some C1q expression in the muscularis by immunofluorescence (Figure 4B and C). We have rewritten the Results section to take these new findings into account.

Is the 5um average on the proximity analysis any different for other macrophage populations to support the idea of a special relationship between C1q-expressing macrophages and neurons?

We agree that the proximity analysis lacks context and have therefore removed it from the figure. The other data in the figure better support the idea that C1q+ macrophages are found predominantly in the submucosal and myenteric plexuses and that they are closely associated with neurons at these tissue sites.

There are many vessels in the submucosa and many associated perivascular nerve fibers - could the proximity simply reflect that both cell types are near vessels containing C1q in circulation?

Our revised manuscript includes RNAscope analysis showing C1q transcript expression by macrophages that are closely associated with enteric neurons (Figure 4D). These findings support the idea that the C1q close to enteric neurons is derived from macrophages rather than from the circulation.

4) A major disconnect was between the observation that C1q expression is in the submucosa and the performance of RNA-seq studies on LMMP preparations. This makes it challenging to draw conclusions from the RNA-Seq data, and makes it particularly important to clarify the specificity of Lyz2-Cre activity.

Our revised manuscript provides flow cytometry data (Figure 4 – figure supplement 1) and RNAscope analysis (Figure 4D) showing that C1q is expressed in macrophages localized to the myenteric plexus. This accords with the results of our RNAseq analysis, which indicates altered LMMP neuronal function in C1qa∆Mφ mice (Figure 6A and B). Since neurons in the myenteric plexus are known to govern gut motility, it also helps to explain our finding that gut motility is accelerated in C1qa∆Mφ mice.

Finally, the pathways identified could reflect a loss of neurons or nerve fibers. No assessment of ENS health in terms of neuronal number or nerve fiber density is provided in either plexus.

Reviewers 1 and 2 also raised this point. Our revised manuscript includes a comparison of the numbers of enteric neurons in C1qafl/fl and C1qaΔMφ mice. There were no marked differences in neuron numbers in C1qaDMf mice when compared to C1qafl/fl controls (Figure 5A and B). There were also similar numbers of inhibitory (nitrergic) and excitatory (cholinergic) neuronal subsets and a similar enteric glial network (Figure 5C-E). Thus, our data suggest that the altered gut motility in the C1qaΔMφ mice arises from altered neuronal function rather than from an overt loss of neurons or nerve fibers. This conclusion is further supported by increased neurogenic activity of peristalsis (Figure 6H and I), and the expression of the C1q receptor BAI1 on enteric neurons (Figure 6 – figure supplement 4).

5) To my knowledge, there is limited evidence that the submucosal plexus has an effect on GI motility. A recent publication suggests that even when mice lack 90% of their submucosal neurons, they are well-appearing without overt deficits (PMID: 29666241). Submucosal neurons, however, are well known to be involved in the secretomotor reflex and fluid flux across the epithelium. Assessment of these ENS functions in the knockout mice would be important and valuable.

Our revised manuscript provides new data showing C1q expression by muscularis macrophages in the myenteric plexus. We analyzed muscularis macrophages by flow cytometry and found that they express C1q (Figure 4 – figure supplement 1). These findings are further supported by RNAscope analysis of C1q expression in wholemounts of LMMP from small intestine and colon (Figure 4D and E). These results are thus consistent with the increased CMMC activity and accelerated gut motility in the C1qaDMf mice. As suggested by the reviewer, our finding of C1q+ macrophages in the submucosal plexus indicates that C1q may also have a role controlling the function of submucosal plexus neurons. We are further exploring this idea through extensive additional experimentation. Given the expanded scope of these studies, we are planning to include them in a follow-up manuscript.

6) Immune function and GI motility can be highly sex-dependent - in all experiments mice of both sexes were reportedly used but it is not clear if sex effects were assessed.

This is a great point, and as suggested by the reviewer we indeed did encounter differences between male and female mice in our preliminary assays of gut motility. We therefore conducted our quantitative comparisons of gut motility between C1qafl/fl and C1qaDMf mice in male mice and now clearly indicate this point in the Materials and Methods.

Author Response

Reviewer #1 (Public Review):

This is a very interesting paper describing membrane potential dynamics of hippocampal principal cells during UP/DOWN transitions and sharp-wave ripples. Using whole-cell in combination with linear LFP recordings in head-fixed awake mice, the authors show striking differences of membrane potential responses in principal cells from the dentage gyrus, CA3 and CA1 sectors. The authors propose that switches between a dominant inhibitory excitable state and a disinhibited non-excitable state control the intra-hippocampal dynamics during UP/DOWN transitions.

Obtaining intracellular recordings in vivo is commendable. The authors provide valuable data and analysis. While data show clear trends and some of the conclusions are well supported, the authors may need to clarify the following potential confounds, which can actually impact their conclusions and interpretation:

1- All the analysis is based in z-scored membrane potential responses but the mean resting membrane potential is never reported. For DG granule cells recorded in awake conditions, the membrane potential is usually hyperpolarized so that most of the effect may be due to reversed GABAa mediated currents. Similarly, for those cells exhibiting the non-expected polarization during UP/DOWN states there may be drifts around reversal potentials explaining their behavior. Moreover, regional trends on passive and active membrane parameters and connectivity can actually explain part of the variability. A longitudinal comparison of state Vm and spikes in fig.5 suggests that some of the largest depolarized responses are not correlated with firing. Authors should evaluate this angle, ideally showing the distribution of membrane potential values across cells and regions and confronting this with the different membrane potential responses.

We added Figure 1 - figure supplement 4, which now describes the mean resting membrane potential, input resistance, burst propensity, and spikes per burst for the recorded cells. These data are provided in Figure 1 - source data 1 together with a recording identifier that can be used to link each cell to all other figure panels and data files. We further added Figure 1 - figure supplement 1, which provides examples of morphological information for our recordings, Figure 1 - figure supplement 2 that shows examples of bursts from morphologically identified neurons, and Figure 1 - figure supplement 3 that shows the locations of recorded cells.

In addition, we added Figure 5 - figure supplement 4 that includes the resting Vm and proximodistal location of cells in relation to their UP-DOWN modulation. We did not detect any significant trends with respect to brain state modulation. DG cells are more hyperpolarized compared to CA3 and CA1 cells and are closest to the reversal potential for GABAa (Figure 1 - figure supplement 4). The lack of any clear trends with respect to the resting Vm suggests that drifts around the GABAa reversal potential are unlikely to be a major factor driving variability in the observed UDS modulation.

2- While there are some trends for each hippocampal regions, there is also individual variability across cells during UP/DOWN transitions (fig.5) and near ripples (fig.6). What part of this variability can be explained by proximodistal and/or deep-superficial differences of cell location and identity? Can authors provide some morphological validation, even if in only a subset of cells? For CA3, proximodistal heterogeneity for intrinsic properties and entorhinal input responses are well documented in intracellular recordings both in vitro and in vivo. What is the location of CA3 cell contributing to this study? For CA1 cells, deep-superficial trends of GABAergic perisomatic inhibition and connectivity with input pathways dominate firing responses. Regarding DG cells, are all they from the upper blade?

We now provide morphological validation for a subset of cells (Figure 1 - figure supplement 1). Since we patch multiple cells in each experiment it is not possible to unequivocally determine their depth within the cell layer, although it is possible to confirm that they are granule cells or pyramidal cells in experiments where all labeled cells are principal neurons (Figure 1 - figure supplement 1). In addition, we added Figure 1 - figure supplement 3 that shows the proximodistal locations of recorded cells. With respect to the DG cells 20/22 are from the upper blade, with only two granule cells recorded in the lower blade (Figure 1 - figure supplement 3).

We added Figure 5 - figure supplement 4 that includes the resting Vm and proximodistal location of each cell as a function of UP-DOWN modulation. We did not detect any significant trends with respect to UDS modulation.

In addition, we added Figure 6 - figure supplement 1 that includes the resting Vm and proximodistal location of each cell as a function of ripple modulation. This figure shows that the most depolarized CA3 cells tend to hyperpolarize most during ripples, consistent with the fact that these cells are furthest away from the GABAa reversal potential and experience the highest driving force. No other significant trends were detected, although we would like to note that our recordings do not span the full proximodistal axis and may hence not be ideally suited to test the dependence of our results on proximodistal location.

3- AC-coupled LFP recordings cannot provide unambiguous identification of the sign of phasic CSD signals, because fluctuations accompanying UP/DOWN states alter the baseline reference. This is actually the case, given changes of membrane potential accompanying UP/DOWN transitions. I recommend reading Brankack et al. 1993 doi: 10.1016/0006-8993(93)90043-m. The authors should acknowledge this limitation and discuss how it could influence their results. One potential solution to get rid of this effect is using principal/independent component analysis for blind source separation.

We acknowledge the inherent limitations of AC-coupled recordings in regards to CSD analysis (Brankack et al., 1993). However, we do not believe these limitations affect our analysis or results for the reasons illustrated in Figure R1. Specifically, we do not attempt to measure the low frequency (< 1 Hz) CSD content directly. Instead, we extract the envelope of the rectified fast CSD transients. In the original submission we referred to this envelope signal as “DG CSD magnitude”, which may have been confusing. In the revised manuscript we use “DG CSD activity” instead to remove any suggestion that the low frequency CSD signal was directly measured. Notice that because of the rectification step the envelope signal is insensitive to the actual polarity of the fast transient CSD fluctuations. Using the envelope, we identify UP states as time periods when the rate and amplitude of EC input current transients, rather than the DC level, increases, in accordance with previous publications (Isomura et al., 2006). We further validated that the extracted UP/DOWN states reflect modulation of pupil diameter and ripple rate, quantities that are independently measured.

Figure R1. Deriving slow envelope signal from AC coupled recordings. (A) In this example the true CSD signal contains both a slow component (8 Hz) and a fast component (80 Hz) that is amplitude modulated by the slow component. Such phase-amplitude coupling is well known between theta and gamma oscillations in the hippocampus. The true CSD shows a current sink with time-varying magnitude. (B) The power spectral density (PSD) estimate of the signal in (A) shows both the slow (8 Hz) and fast (three peaks near 80 Hz) components. (C) Assume LFP recordings are obtained with a high-pass filter that has eliminated the slow component. Consequently, the estimated CSD signal contains only fast fluctuations. Furthermore, instead of a time-varying current sink it shows quickly alternating sinks and sources (both negative and positive values). The slow component can be visualized as the amplitude envelope (interrupted red line) of the signal. (D) PSD estimate shows that the slow component is absent from the extracted CSD signal. (E) Rectifying the CSD estimate (black) and then filtering (red) approximately recovers the true slow component (red interrupted). This is how the DG CSD activity signal is obtained. (F) PSD estimate of the rectified and filtered CSD signal recovers the slow component (interrupted red vertical line).

Reviewer #2 (Public Review):

In this manuscript "Inhibition is the hallmark of CA3 intracellular dynamics around awake ripples" the authors obtained Vm recordings from CA1, CA3 and DG neurons while also obtaining local field potentials across the CA1 and DG layers. This enabled them to identify periods of up and down state transitions, and to detect sharp-wave ripples (SWRs). Using these data, they then came to the conclusion that compared to CA1 and DG, the Vm of more CA3 neurons is hyperpolarized at the approximate time of SWRs.

Unfortunately, for the following reasons, the current manuscript does not necessarily support this conclusion:

Recordings are obtained in mice who are recently (same day) recovering from craniotomy surgery/anesthesia and have no training on head fixation. This means that the behavioral state is abnormal, and the animal may have residual anesthesia effects.

The main surgery for implanting the head-fixation apparatus and marking the coordinates for multisite and pipette insertion was carried out at least two days before the experiment. On the day of the experiment animals were briefly lightly anesthetized (<1 hr, at <1% isoflurane at 1 lit/min) for the sole purpose of resecting the dura at the two sites for multisite probe and pipette insertion. This procedure was carried out on the same day as the experiment in order to minimize the time the brain was exposed and optimize the quality of the recordings. Experiments began at least six hours after this short procedure. Furthermore, animals were given time to get familiarized with the behavioral apparatus before recordings began and showed no signs of distress.

Previous studies show that about 95% of isoflurane is eliminated within minutes by exhalation (Holaday et al., 1975). The further elimination of isoflurane proceeds with a fast phase with half-time of about 7-9 min and a slower phase with half-time of about 100-115 min (Chen et al., 1992), with the faster phase reflecting elimination from the brain (Litt et al., 1991). Given these considerations there should be negligible residual isoflurane from the short anesthesia six hours later when recordings are initiated.

In order to further investigate whether the short and light anesthesia during the day of recordings has any effect on the results reported in the paper, we carried out additional experiments in which we performed the surgery, including dura removal, 3 days before the recording session. The animals were habituated under head-fixation on the spherical treadmill for two hour periods each of the two days following the surgery. On the third day after surgery, we carried out recordings without any surgical procedures or anesthesia. The durations of UP and DOWN states without same day anesthesia were similar to those obtained in our previous experiments (Figure 2- figure supplement 4). The additional CA3 whole-cell recordings obtained in these new experiments have the same hyperpolarization features typical of our previous recordings. These additional experiments argue that the brief anesthesia on the day of recordings has no significant effect on the results.

Most of the paper is dedicated to dynamics around up-down state transitions, not focused on ripples.

We changed the title to “Up-Down states and ripples differentially modulate membrane potential dynamics across DG, CA3, and CA1 in awake mice” to reflect the analysis of both UP-DOWN state transitions and ripples. The two analyses are linked as the brain state modulation accounts for the slow Vm modulation around ripples.

Vm should be examined raw first, then split into fast and slow -the cell lives with the raw Vm.

The raw Vm can be obtained by adding the slow and fast Vm components. Hence the behavior of the Vm around ripples can be obtained by adding the panels of columns 1 and 3 in Figure 6. Decomposing into the slow and fast components illustrates how the slow modulation around ripples is due to brain state modulation of the slow component of the Vm (Figure 6).

While some (assumed) CA3 principal cells were hyperpolarized around the time of ripples, saying inhibition is the hallmark of CA3 dynamics around ripples is an exaggeration, especially because it does not seem mechanistically tied to anything else.

While a small fraction of CA3 cells is excited around ripples, the majority is inhibited. We suggest that the inhibition of the majority of CA3 neurons can account for the sparse and selective activation of CA3 around ripples.

The use of ripple onset time is questionable, since the detected onset of the ripple depends on the detector settings, amplifier signal-to-noise ratio, etc. The best and most widely used (including by a subset of these authors) metric is the ripple peak time.

We added Figure 6 - figure supplement 2, which shows that the Vm modulation around peak ripple power is the same as the modulation around ripple start, except for a small time shift due to the fact that the ripple power peaks shortly after ripple start. Our focus on ripple onset facilitates characterizing the timing of pre-ripple activity, such as the Vm depolarization observed before ripple onset for DG and CA1 neurons.

There is not enough raw data (or quality metrics) shown to judge the quality of the data, especially for the whole cell recordings. For instance what was the input resistance of the neurons? Was the access resistance constant?

We added Figure 1 - figure supplement 4, which now describes the mean resting membrane potential, input resistance, burst propensity, and spikes per burst for the recorded cells. These data are provided in Figure 1 - source data 1 together with a recording identifier that can be used to link each cell to all other figure panels and data files. We further added Figure 1- figure supplement 1, which provides examples of morphological information for our recordings, Figure 1 - figure supplement 2 that shows examples of bursts from morphologically identified neurons, and Figure 1 - figure supplement 3 that shows the locations of recorded cells.

There is not enough explanation regarding why the reported results on the spiking of CA1 and CA3 neurons in SWRs is so different than previously published. In general, whole cell recording is not the most reliable way to record spike timing, and the presented whole cell data differ from previously published juxtacellular and extracellular recording methods, which better preserve physiological spiking activity.

The CA1 neurons in this study depolarize and elevate their firing around ripples, consistent with previous intracellular and extracellular recordings. Our study reveals hyperpolarization of the majority of CA3 cells while only a small fraction is depolarized. This is consistent with the sparse activation of CA3 around ripples previously reported with extracellular studies. The overall firing rate change of CA3 neurons around ripples is a balance between the firing rate elevation of the small subset of activated cells and the net decrease in firing across the rest of the population. Since the baseline firing rate of CA3 pyramidal neurons in quiet wakefulness and sleep is low, the ripple-associated inhibition may not be readily observable in the spiking of individual CA3 neurons due to a “floor effect”. The overall rate of CA3 neurons we record increases before ripple onset, consistent with previous studies (Fig. 6D4). The subthreshold hyperpolarization of the majority of neurons provides novel insights into the mechanisms ensuring sparse and selective activation of the CA3 population around ripples.

The number of neurons from each area is not reported.

The number of cells was (indirectly) reported as the number of rows in Figs. 3-7. We now report the number of cells explicitly: 22 DG cells, 32 CA3 cells, and 32 CA1 cells.

There is no verification of cell type so it is inappropriate to assume that all neurons are the principal neurons.

We added Figure 1 - figure supplement 1, which shows morphological identification of recorded cells. We patch multiple cells in each experiment, but we can confirm the morphological identity of principal neurons when all stained cells have morphology of dentate granule cells or CA3/CA1 pyramidal neurons. The properties of morphologically identified cells in Figure 1 - figure supplement 1 are typical of all recorded cells (morphologically identified neurons from Figure 1 - figure supplement 1 are shown as diamonds in Figure 1- figure supplement 4, while the rest are shown as dots). There were no significant differences between the two groups (p > 0.05 t-test; p > 0.05 Wilcoxon rank sum test).

Are the fluctuations in the CA3 Vm generally smaller than for CA1 and DG because of physiology or technical reasons?

The recordings were done in exactly the same way across areas, arguing against technical reasons for any differences observed across the hippocampal subfields.

Reviewer #3 (Public Review):

During slow wave sleep and quiet immobility, communication between the hippocampus and the neocortex is thought to be important for memory formation notably during periods of hippocampal synchronous activity called sharp-wave ripple events. The cellular mechanisms of sharp-wave ripple initiation in the hippocampus are still largely unknown, notably during awake immobility. In this paper, the authors addressed this question using patch-clamp recordings of principal cells in different hippocampal subfields (CA3, CA1 and the dentate gyrus) combined with extracellular recordings in awake head-fixed mice as well as computer modeling. Using the current source density (CSD) profile of local field potential (LFP) recordings in the molecular layer of the dentate gyrus as a proxy of UP/DOWN state activity in the entorhinal cortex they report the preferential occurrence of sharp-wave ripple (recorded in area CA1) during UP states with a higher probability toward the end of the UP state (unlike eye blinks which preferentially occur during DOWN states). Patch-clamp recordings reveal that a majority of dentate granule cells get depolarized during UP state while a majority of CA3 pyramidal cells get hyperpolarized and CA1 pyramidal cells show a more mixed behavior. Closer examination of Vm behavior around state transitions revealed that CA3 pyramidal cells are depolarized and spike at the DOWN/UP transition (with some cells depolarizing even earlier) and then progressively hyperpolarize during the course of the UP state while DGCs and CA1 pyramidal cells tend to depolarize and fire throughout the UP state. Interestingly, CA3 pyramidal cells also tend to be hyperpolarized during ripples (except for a minority of cells that get depolarized and could be instrumental in ripple generation), while DGCs and CA1 pyramidal cells tend to be depolarized and fire. The strong activation of dentate granule cells during ripples is particularly interesting and deserves further investigations. The observation that the probability of ripple occurrence increases toward the end of the UP state, when CA3 pyramidal cells are maximally hyperpolarized, suggests that the inhibitory state of the CA3 hippocampal network could be permissive for ripple generation possibly by de-inactivation of voltage-gated channels thus increasing their excitability (i.e. ability to get excited). Altogether, these results confirm previous work on the impact of slow oscillations on the membrane potential of hippocampal neurons in vivo under anesthesia but also point to specificities possibly linked to the awake state. They also invite to revisit previous models derived from in vitro recordings attributing synchronous activity in CA3 to a global build-up of excitatory activity in the network by suggesting a role for Vm hyperpolarization in preserving the excitability of the CA3 network.

1) In light of recent report of heterogeneity within hippocampal cell types (and notably description of a new CA3 pyramidal cell type instrumental for sharp-wave ripple generation) (Hunt et al., 2018), the small minority of CA3 pyramidal cells depolarized during ripples deserve more attention. These cells are indeed likely key in the generation of sharp wave ripple. Several analyses could be performed in order to decipher whether they have specific intrinsic properties (baseline Vm, firing threshold, burst propensity), whether they are located in specific sub-areas of CA3 (a versus b, deep versus superficial) and whether they are distinctively modulated during UP/DOWN states.

Following the reviewer’s suggestion we now analyze the properties and UDS modulation of the CA3 neurons that are depolarized around ripples (Figure 6 - figure supplement 3). These neurons have comparable resting Vm, spike thresholds, and burst propensity as the rest of the CA3 population (p > 0.05, t-test). These CA3 cells had lower firing probability in the DOWN state. The locations of the depolarized cells are distributed across CA3c,b and are not clustered compared to the rest of the cells (Figure R2).

Figure R2. Proximodistal locations of CA3 cells that depolarize during ripples. Same as Figure 1 - figure supplement 3, but CA3 cells showing depolarization in their ripple-triggered average (RTA) response are marked with black dots. There was no significant difference in the proximodistal locations of these cells compared to the rest of the CA3 population (p > 0.05, t-test).

The population of athorny cells described in Hunt et al. represents a small percentage of CA3 cells (10-20%) that are concentrated in the CA3a region, which we do not sample in our recordings. Hence, the depolarized cells are unlikely to correspond to the athorny cells reported in Hunt et al.

2) The authors use CSD analysis in the DG as a proxy of synaptic inputs coming from the EC to define alternating periods of UP and DOWN states. I have few questions concerning this procedure: 1- It is unclear if only periods when animals was still/immobile were analyzed. 2- How coherent were these periods with slow oscillations recorded in the cortex (which are also recorded with the linear probe?).

The analysis was restricted to periods of immobility, which comprise the majority of the recording time as the animals are not performing any task. Cortical LFPs exhibit high coherence for low frequencies (<1 Hz) with the rectified DG CSD signal (Figure R3), although the contribution of volume conduction to this effect cannot be ruled out.

Figure R3. Coherence between DG CSD power and cortical LFP. (Top) population average magnitude squared coherence between DG CSD power (rectified CSD from the DG molecular layer) and cortical LFP across all recorded datasets. Notice the elevated coherence at low frequencies (< 1 Hz, vertical interrupted line) as well as the peak at theta ( 7-8 Hz). Volume conduction from other brain areas (i.e. the hippocampus) contributes to the cortical LFP and may be responsible for the coherence at theta, as well as at low frequencies. (Bottom) Each row in the pseudocolor image shows the coherence between DG CSD power and cortical LFP for a given dataset.

3- How long did these periods last? Did they occur during classically described hippocampal states (LIA/SIA) or do they correspond to a different state (Wolansky et al., J Neurosci 2006).

The distribution of UP and DOWN state durations is shown in Figure 2 - figure supplement 4.

We also added Figure 2 - supplementary figure 8 that shows the distribution of LIA and SIA transitions as a function of UDS phase. The LIA and SIA states were computed based on LFPs from CA1 stratum radiatum as described in (Hulse et al., 2017). The detected LIA→SIA transitions map very closely to UP→DOWN transitions. The SIA→LIA transitions are also concentrated around DOWN→UP transitions, but the distribution is broader compared to the LIA→SIA transitions. These observations are consistent with UP states broadly overlapping with LIA and DOWN states with SIA.

3) To better characterize hippocampal CSD profiles around ripples and UP/Down states transitions, could you plot ripple and UDS transition-triggered average CSD profiles across hippocampal subfields?

We added Figure 2 - supplementary figure 7 that shows average CSD profiles around UP/DOWN state transitions and ripples.

4) The duration of UP states appears longer than that reported in anesthetized animals. To ascertain this fact could the authors quantify and report mean UP and DOWN states durations? Shorter DOWN states would decrease the probability to detect ripple. Could the authors correct for this bias in their analysis of ripple occurrence during UP and DOWN states?

We report the medians and means of the distributions of UP and DOWN durations in Figure 2 - figure supplement 4. Ripples occur almost exclusively during the UP states, with almost no ripples occurring in DOWN states. Furthermore, the duration of UP and DOWN states is comparable suggesting that the duration of DOWN states does not bias the probability of ripple detection. We also added Figure 2 - figure supplement 2B, showing the rate (in Hz) of ripple occurrence as a function of UDS phase, which explicitly controls for UDS phase occupancy.

The duration of UP and DOWN states in quiet wakefulness depend on the behavior of the animal, attentional state, and external stimuli and need not be the same as in anesthesia or sleep when the animal is not behaving and is less responsive to external stimuli. To provide validation that the extracted UP and DOWN states in quiet wakefulness indeed correspond to genuine brain states, we show that the pupil diameter and ripple rates which are independently extracted are strongly modulated around the extracted UP and DOWN states.

5) The authors report a high coherence between the Vm of an example CA3 pyramidal cells and UP/DOWN state in DG. Was it a general property of a majority of CA3 pyramidal cells? The coherence values should be reported for all CA3 pyramidal cells.

We added Figure 2 - figure supplement 1, which reports the coherence of all cells across the subfields with the rectified DG CSD. The coherence values are similar across cells and subfields. We also report correlations between the slow component of the Vm and DG CSD activity for all cells in Figure 3. Neurons in CA3 exhibit negative correlations in contrast to DG and CA1, with the absolute values of the correlations similar across the subfields.

6) Was the high coherence between DG CSD magnitude and CA3 Vm specific to these slow oscillatory periods or a more general feature of the DG/CA3 functional coupling. For example, was it also observed during theta/movement periods?

Figure 2 - figure supplement 1 reports the coherence of all cells across the subfields with rectified DG CSD over the entire recording duration. Mice do not perform any tasks during the recordings so periods of immobility and quiet wakefulness comprise the majority of the recording session and are the focus of our analysis. During some occasional theta periods there is increased coherence in the theta frequency band (figure R4).

7) Fig. 6 shows depolarization and increase firing in DGCs up to 150 ms prior to ripple onset. However, ripples sometime occur in bursts with one ripple following others. Could such phenomenon explain the firing prior to ripples? (which would in fact correspond to firing during a previous ripple). What is the behavior of firing rate and Vm of different cells types if analysis is restricted to isolated ripples? This analysis is notably important in CA3 where feedback inhibition following a first ripple could lead to hyperpolarization « during » the next ripple.

We added a new figure (Figure 7 - figure supplement 2) that compares Vm aligned to the onset of isolated single ripples vs. ripple doublets. The pre-ripple depolarization in DG and CA1 is similar for isolated ripples and ripple doublets arguing against the hypothesis that pre-ripple responses are a reflection of ripple bursts.

Author Response

Reviewer #1 (Public Review):

The manuscript by Royall et al. builds on previous work in the mouse that indicates that neural progenitor cells (NPCs) undergo asymmetric inheritance of centrosomes and provides evidence that a similar process occurs in human NPCs, which was previously unknown.

The authors use hESC-derived forebrain organoids and develop a novel recombination tag-induced genetic tool to birthdate and track the segregation of centrosomes in NPCs over multiple divisions. The thoughtful experiments yield data that are concise and well-controlled, and the data support the asymmetric segregation of centrosomes in NPCs. These data indicate that at least apical NPCs in humans undergo asymmetric centrosome inheritance. The authors attempt to disrupt the process and present some data that there may be differences in cell fate, but this conclusion would be better supported by a better assessment of the fate of these different NPCs (e.g. NPCs versus new neurons) and would support the conclusion that younger centriole is inherited by new neurons.

We thank the reviewer for their supportive comments (“…thoughtful experiments yield data that are concise and well-controlled…”).

Reviewer #2 (Public Review):

Royall et al. examine the asymmetric inheritance of centrosomes during human brain development. In agreement with previous studies in mice, their data suggest that the older centrosome is inherited by the self-renewing daughter cell, whereas the younger centrosome is inherited by the differentiating daughter cell. The key importance of this study is to show that this phenomenon takes place during human brain development, which the authors achieved by utilizing forebrain organoids as a model system and applying the recombination-induced tag exchange (RITE) technology to birthdate and track the centrosomes.

Overall, the study is well executed and brings new insights of general interest for cell and developmental biology with particular relevance to developmental neurobiology. The Discussion is excellent, it brings this study into the context of previous work and proposes very appealing suggestions on the evolutionary relevance and underlying mechanisms of the asymmetric inheritance of centrosomes. The main weakness of the study is that it tackles asymmetric inheritance only using fixed organoid samples. Although the authors developed a reasonable mode to assign the clonal relationships in their images, this study would be much stronger if the authors could apply time-lapse microscopy to show the asymmetric inheritance of centrosomes.

We thank the reviewer for their constructive and supportive comments (“…the study is well executed and brings new insights of general interest for cell and developmental biology with particular relevance to developmental neurobiology….”). We understand the request for clonal data or dynamic analyses in organoids (e.g., using time-lapse microscopy). We also agree that such data would certainly strengthen our findings. However, as outlined above (please refer to point #1 of the editorial summary), this is unfortunately currently not feasible. However, we have explicitly discussed this shortcoming in our revised manuscript and why future experiments (with advanced methodology) will have to do these experiments.

Reviewer #3 (Public Review):

In this manuscript, the authors report that human cortical radial glia asymmetrically segregates newly produced or old centrosomes after mitosis, depending on the fate of the daughter cell, similar to what was previously demonstrated for mouse neocortical radial glia (Wang et al. 2009). To do this, the authors develop a novel centrosome labelling strategy in human ESCs that allows recombination-dependent switching of tagged fluorescent reporters from old to newly produced centrosome protein, centriolin. The authors then generate human cortical organoids from these hESCs to show that radial glia in the ventricular zone retains older centrosomes whereas differentiated cells, i.e. neurons, inherit the newly produced centrosome after mitosis. The authors then knock down a critical regulator of asymmetric centrosome inheritance called Ninein, which leads to a randomization of this process, similar to what was observed in mouse cortical radial glia.

A major strength of the study is the combined use of the centrosome labelling strategy with human cortical organoids to address an important biological question in human tissue. This study is similarly presented as the one performed in mice (Wang et al. 2009) and the existence of the asymmetric inheritance mechanism of centrosomes in another species grants strength to the main claim proposed by the authors. It is a well-written, concise article, and the experiments are well-designed. The authors achieve the aims they set out in the beginning, and this is one of the perfect examples of the right use of human cortical organoids to study an important phenomenon. However, there are some key controls that would elevate the main conclusions considerably.

We thank the reviewer for their overall support of our findings (“..authors achieve the aims they set out in the beginning, and this is one of the perfect examples of the right use of human cortical organoids to study an important phenomenon…”). We also understand the reviewer’s request for additional experiments/controls that “…would elevate the main conclusions considerably.”

1) The lack of clonal resolution or timelapse imaging makes it hard to assess whether the inheritance of centrosomes occurs as the authors claim. The authors show that there is an increase in newly made non-ventricular centrosomes at a population level but without labelling clones and demonstrating that a new or old centrosome is inherited asymmetrically in a dividing radial glia would grant additional credence to the central conclusion of the paper. These experiments will put away any doubt about the existence of this mechanism in human radial glia, especially if it is demonstrated using timelapse imaging. Additionally, knowing the proportions of symmetric vs asymmetrically dividing cells generating old/new centrosomes will provide important insights pertinent to the conclusions of the paper. Alternatively, the authors could soften their conclusions, especially for Fig 2.

We understand the reviewer’s request. As outlined above (please refer to point #1 of the editorial summary), we had tried previously to add data using single cell timelapse imaging. However, due to the size and therefore weakness of the fluorescent signal we had failed despite extensive efforts. According to the reviewer’s suggestion we have now explicitly discussed this shortcoming and softened our conclusions.

2) Some critical controls are missing. In Fig. 1B, there is a green dot that does not colocalize with Pericentrin. This is worrying and providing rigorous quantifications of the number of green and tdTom dots with Pericentrin would be very helpful to validate the labelling strategy. Quantifications would put these doubts to rest. Additionally, an example pericentrin staining with the GFP/TdTom signal in figure 4 would also give confidence to the reader. For figure 4, having a control for the retroviral infection is important. Although the authors show a convincing phenotype, the effect might be underestimated due to the incomplete infection of all the analyzed cells.

We have included more rigorous quantifications in our revised manuscript.

For Figure 1: There are indeed some green speckles that might be misinterpreted as a green centrosome. However, the speckles are usually smaller and by applying a strict size requirement we exclude speckles. To check whether the classifier might interpret any speckles as centrosomes, we manually checked 60 green “dots” that were annotated as centrosome. From these images all green spots detected as centrosome co-localized with Pericentrin signal (Images shown in Author response image 1).

For Figure 4: as we are comparing cells that were either infected with a retrovirus expressing scrambled or Ninein-targeting shRNA we compare cells that experienced a similar treatment. Besides that, only cells infected with the virus express Cre-ERT2 whereby only the centrosomes of targeted cells were analyzed. Accordingly, we only compare cells expressing scrambled or Ninein-targeting shRNA, all surrounding “wt” cells are not considered.

Author response image 1.

Pictures used to test the classifier. Each of the green “dots” recognized by the classifier as a Centriolin-NeonGreen-containing centrosome (green) co-localized with Pericentrin signal (white).

3) It would be helpful if the authors expand on the presence of old centrosomes in apical radial glia vs outer radial glia. Currently, in figure 3, the authors only focus on Sox2+ cells but this could be complemented with the inclusion of markers for outer radial glia and whether older centrosomes are also inherited by oRGCs. This would have important implications on whether symmetric/asymmetric division influences the segregation of new/old centrosomes.

That is an interesting question and we do agree that additional analyses, stratified by ventricular vs. oRGCs would be interesting. However, at the time points analysed there are only very few oRGCs present (if any) in human ESC-derived organoids (Qian et al., Cell, 2016). However, we have now added this point for future experiments to our discussion.

Author Response

Reviewer #1 (Public Review):

[...] Recently, pupil dilation was linked to cholinergic and noradrenergic neuromodulation as well as cortical state dynamics in animal research. This work adds substantially to this growing research field by revealing the temporal and spatial dynamics of pupil-linked changes in cortical state in a large sample of human participants.

The analyses are thorough and well conducted, but some questions remain, especially concerning unbiased ways to account for the temporal lag between neural and pupil changes. Moreover, it should be stressed that the provided evidence is of indirect nature (i.e., resting state pupil dilation as proxy of neuromodulation, with multiple neuromodulatory systems influencing the measure), and the behavioral relevance of the findings cannot be shown in the current study.

Thank you for your positive feedback and constructive suggestions. We are especially grateful for the numerous pointers to other work relevant to our study.

1. Concerning the temporal lag: The authors' uniformly shift pupil data (but not pupil derivative) in time for their source-space analyses (see above). However, the evidence for the chosen temporal lags (930 ms and 0 ms) is not that firm. For instance, in the cited study by Reimer and colleagues [1] , cholinergic activation shows a temporal lag of ~ 0.5 s with regard to pupil dilation - and the authors would like to relate pupil time series primarily to acetylcholine. Moreover, Joshi and colleagues [2] demonstrated that locus coeruleus spikes precede changes in the first derivative of pupil dilation by about 300 ms (and not 0 ms). Finally, in a recent study recording intracranial EEG activity in humans [3], pupil dilation lagged behind neural events with a delay between ~0.5-1.7s. Together, this questions the chosen temporal lags.

More importantly, Figures 3 and S3 demonstrate variable lags for different frequency bands (also evident for the pupil derivative), which are disregarded in the current source-space analyses. This biases the subsequent analyses. For instance, Figure S3 B shows the strongest correlation effect (Z~5), a negative association between pupil and the alpha-beta band. However, this effect is not evident in the corresponding source analyses (Figure S5), presumably due to the chosen zero-time-lag (the negative association peaked at ~900 ms)).

As the conducted cross-correlations provided direct evidence for the lags for each frequency band, using these for subsequent analyses seems less biased.

This is an important point and we gladly take the opportunity to clarify this in detail. In essence, choosing one particular lag over others was a decision we took to address the multi-dimensional issue of presenting our results (spectral, spatial and time dimensions) and fix one parameter for the spatial description (see e.g. Figure 4). It is worth pointing out first that our analyses were all based on spectral decompositions that necessarily have limited temporal resolutions. Therefore, any given lag represents the center of a band that we can reasonably attribute to a time range. In fact, Figure 3C shows how spread out the effects are. It also shows that the peaks (troughs) of low and high frequency ranges align with our chosen lag quite well, while effects in the mid-frequency range are not “optimally” captured.

As picking lags based on maximum effects may be seen as double dipping, we note that we chose 0.93 sec a priori based on the existing literature, and most prominently based on the canonical impulse response of the pupil to arousing stimuli that is known to peak at that latency on average (Hoeks & Levelt, 1993; Wierda et al. 2012; also see Burlingham et al.; 2021). This lag further agrees with the results of reference [3] cited by the reviewer as it falls within that time range, and with Reimer et al.’s finding (cited as [1] above), as well as Breton-Provencher et al. (2019) who report a lag of ~900 ms sec (see their Supplementary Figure S8) between noradrenergic LC activation and pupil dilation. Finally, note that it was not our aim to relate pupil dilations to either ACh or NE in particular as we cannot make this distinction based on our data alone. Instead, we point out and discuss the similarities of our findings with time lags that have been reported for either neurotransmitter before.

With respect to using different lags, changing the lag to 0 or 500 msec is unlikely to alter the reported effects qualitatively for low- and high frequency ranges (see Figure 3C), as both the pupil time series as well as fluctuations in power are dominated by very slow fluctuations (<< 1 Hz). As a consequence, shifting the signal by 500 msec has very little impact. For comparison, below we provide the reviewer with the results presented in Figure 4 but computed based on zero (Figure R1) and 500-msec (Figure R2) lags. While there are small quantitative differences, qualitatively the results remain mostly identical irrespective of the chosen lag.

Figure R1. Figure equivalent to main Figure 4, but without shifting the pupil.

In sum, choosing one common lag a priori (as we did here) does not necessarily impose more of a bias on the presentation of the results than choosing them post-hoc based on the peaks in the cross-correlograms. However, we have taken this point as a motivation to revise the Results and Methods sections where applicable to strengthen the rationale behind our choice. Most importantly, we changed the first paragraph that mentions and justifies the shift as follows, because original wording may have given the false impression that the cross-correlation results influenced lag choice:

“Based on previous reports (Hoeks & Levelt, 1993; Joshi et al., 2016; Reimer et al., 2016), we shifted the pupil signal 930 ms forward (with respect to the MEG signal). We introduced this shift to compensate for the lag that had previously been observed between external manipulations of arousal (Hoeks & Levelt, 1993) as well as spontaneous noradrenergic activity (Reimer et al., 2016) and changes in pupil diameter. In our data, this shift also aligned with the lags for low- and high-frequency extrema in the cross-correlation analysis (Figure 3B).”

Figure R2. Figure equivalent to main Figure 4, but with shifting the pupil with respect to the MEG by 500 ms.

Related to this aspect: For some parts of the analyses, the pupil time series was shifted with regard to the MEG data (e.g., Figure 4). However, for subsequent analyses pupil and MEG data were analyzed in concurrent 2 s time windows (e.g., Figure 5 and 6), without a preceding shift in time. This complicates comparisons of the results across analyses and the reasoning behind this should be discussed.

The signal has been shifted for all analyses that relate to pupil diameter (but not pupil derivative). We have added versions of the following statement in the respective Results and Methods section to clarify (example from Results section ‘Nonlinear relations between pupil-linked arousal and band-limited cortical activity’):

“In keeping with previous analyses, we shifted the pupil time series forward by 930 msec, while applying no shift to the pupil derivative.”

1. The authors refer to simultaneous fMRI-pupil studies in their background section. However, throughout the manuscript, they do not mention recent work linking (task-related) changes in pupil dilation and neural oscillations (e.g., [4-6]) which does seem relevant here, too. This seems especially warranted, as these findings in part appear to disagree with the here-reported observations. For instance, these studies consistently show negative pupil-alpha associations (while the authors mostly show positive associations). Moreover, one of these studies tested for links between pupil dilation and aperiodic EEG activity but did not find a reliable association (again conflicting with the here-reported data). Discussing potential differences between studies could strengthen the manuscript.

We have added a discussion of the suggested works to our Discussion section. We point out however that a recent study (Podvalny et al., https://doi.org/10.7554/eLife.68265) corroborates our finding while measuring resting-state pupil and MEG simultaneously in a situation very similar to ours. Also, we note that Whitmarsh et al. (2021) (reference [6]) is actually in line with our findings as we find a similar negative relationship between alpha-range activity in somatomotor cortices and pupil size.

Please also take into account that results from studies of task- or event-related changes in pupil diameter (phasic responses) cannot be straightforwardly compared with the findings reported here (focusing on fluctuations in tonic pupil size) , due to the inverse relationship between tonic (or baseline) and phasic pupil response (e.g. Knapen et al., 2016). This means that on trials with larger baseline pupil diameter, phasic pupil dilation will be smaller and vice versa. Hence, a negative relation between the evoked change in pupil diameter and alpha-band power can very well be consistent with the positive correlation between tonic pupil diameter and alpha-band activity that we report here for visual cortex.

In section ‘Arousal modulates cortical activity across space, time and frequencies’ we have added:

“Seemingly contradicting the present findings, previous work on task-related EEG and MEG dynamics reported a negative relationship between pupil-linked arousal and alpha-range activity in occipito-parietal sensors during visual processing (Meindertsma et al, 2017) and fear conditioning (Dahl et al. 2020).Note however that results from task-related experiments, that focus on evoked changes in pupil diameter rather than fluctuations in tonic pupil size, cannot be directly compared with our findings. Similar to noradrenergic neurons in locus coeruleus (Aston-Jones & Cohen, 2005), phasic pupil responses exhibit an inverse relationship with tonic pupil size (Knapen et al., 2016). This means that on trials with larger baseline pupil diameter (e.g. during a pre-stimulus period), the evoked (phasic) pupil response will be smaller and vice versa. As a consequence, a negative correlation between alpha-band activity in the visual cortex and task-related phasic pupil responses does not preclude a positive correlation with tonic pupil size during baseline or rest as reported here. In line with this, Whitmarsh et al., 2021 found a negative relationship between alpha-activity and pupil size in the somatosensory cortex that agrees with our finding. Although using an event-related design to study attention to tactile stimuli, this relationship occurred in the baseline, i.e. before observing any task-related phasic effects on pupil-linked arousal or cortical activity.”

In section ‘Arousal modulation of cortical excitation-inhibition ratio’ we have added: “The absence of this effect in visual cortices may explain why Kosciessa et al. (2021) found no relationship between pupil-linked arousal and spectral slope when investigating phasic pupil dilation in response to a stimulus during visual task performance. However, this behavioral context, associated with different arousal levels, likely also changes E/I in the visual cortex when compared with the resting state (Pfeffer et al., 2018).”

Finally, in the Conclusion we added (note: ‘they’ = the present results): “Further, they largely agree with similar findings of a recent independent report (Podvalny et al., 2021).”

Related to this aspect: The authors frequently relate their findings to recent work in rodents. For this it would be good to consider species differences when comparing frequency bands across rodents and primates (cf. [7,8]).

Throughout our Results section we have mainly remained agnostic with respect to labeling frequency ranges when drawing between-species comparisons, and have only reverted to it as a justification for a dimension reduction for some of the presented analysis. Following your comment however, we have phrased the following section in the Discussion, section ‘Arousal modulates cortical activity across space, time and frequencies’, more carefully:

“The low-frequency regime referred to in rodent work (2—10Hz; e.g., McGinley et al., 2015) includes activity that shares characteristics with human alpha rhythms (3—6Hz; Nestogel and McCormick, 2021; Senzai et al. 2019). The human equivalent however clearly separates from activity in lower frequency bands and,here, showed idiosyncratic relationships with pupil-linked arousal.”

1. Figure 1 highlights direct neuromodulatory effects in the cortex. However, seminal [9-11] and more recent work [12,13] demonstrates that noradrenaline and acetylcholine also act in the thalamus which seems relevant concerning the interpretation of low frequency effects observed here. Moreover, neural oscillations also influence neuromodulatory activity, thus the one-headed arrows do not seem warranted (panel C) [3,14].

This is a very good point. First, we would like to note that we have extended on acknowledging thalamic contributions to low-frequency (specifically alpha) effects in response to the Reviewer’s point 11 (‘Recommendations for authors’ section below). Also, we have added a reference to the role of potential top-down (reverse) influences to our Discussion, section ‘Arousal modulates cortical activity across space, time and frequencies’, as follows:

“Further, we note that our analyses and interpretations focus on arousal-related neuromodulatory influences on cortical activity, whereas recent work also supports a reverse “top-down” route, at least for frontal cortex high-frequency activity on LC spiking activity (Totah et al., 2021).”

Ultimately, however, we decided to leave the arrows in Figure 1C uni-directional to keep in line with the rationale of our research that stems mostly from rodent work, which also emphasises the indicated directionality. Also, reference [3] is highly interesting for us because it actually aligns with our data: The authors show that a spontaneous peak of high-frequency band activity (>70 Hz) in insular cortex precedes a pupil dilation peak (or plateau) in two of three participants by ~500msec (which mimics a pattern found for task-evoked activity; see their Figure 5b/c). We find a maximum in our cross-correlation between pupil size and high frequency band activity (>64 Hz) that indicates a similar lag (see our Figure 3B). Importantly, both results do not rule out a common source of neuromodulation for the effects. We have added the following to the end of the section ‘An arousal-triggered cascade of activity in the resting human brain’:

“In fact, Kucyi & Parvizi (2020) found spontaneous peaks of high-frequency band activity (>70 Hz) in the insular cortex of three resting surgically implanted patients that preceded pupil dilation by ~500msec - a time range that is consistent with the lag of our cross-correlation between pupil size and high frequency (>64Hz) activity (see Figure 3B). Importantly, they showed that this sequence mimicked a similar but more pronounced pattern during task performance. Given the purported role of the insula (Menon & Uddin, 2015), this finding lends support to the idea that spontaneous covariations of pupil size and cortical activity signal arousal events related to intermittent 'monitoring sweeps' for behaviourally relevant information.”

1. In their discussion, the authors propose a pupil-linked temporal cascade of cognitive processes and accompanying power changes. This argument could be strengthened by showing that earlier events in the cascade can predict subsequent ones (e.g., are the earlier low and high frequency effects predictive of the subsequent alpha-beta synchronization?)-

We added this cascade angle as one possible interpretation of the observed effects. We fully agree that this is an interesting question but would argue that this would ideally be tested in follow-up research specifically designed for that purpose. The suggested analysis would add a post-hoc aspect to our exploratory investigation in the absence of a suitable contrast, while also potentially side-tracking the main aim of the study. We have revised the language in this section and added the following changes (bold) to the last paragraph to emphasise the speculatory aspect, and clarify what we think needs to be done to look into this further and with more explanatory power.

“The three scenarios described here are not mutually exclusive and may explain one and the same phenomenon from different perspectives. Further, it remains possible that the sequence we observe comprises independent effects with specific timings. A pivotal manipulation to test these assumptions will be to contrast the observed sequence with other potential coupling patterns between pupil-linked arousal and cortical activity during different behavioural states.”

Author Response

Reviewer #1 (Public Review):

The study by Akter et al demonstrates that astrocyte-derived L-lactate plays a key role in schema memory formation and promotes mitochondrial biogenesis in the Anterior Cingulate Cortex (ACC).

The main tool used by the authors is the DREADD technology that allows to pharmacologically activate receptors in a cell-specific manner. In the study, the authors used the DREADD technique to activate appropriately transfected astrocytes, a subtype of muscarinic receptor that is not normally present in cells. This receptor being coupled to a Gi-mediated signal transduction pathway inhibiting cAMP formation, the authors could demonstrate cell-(astrocyte) specific decreases in cAMP levels that result in decreased L-lactate production by astrocytes.

Behaviorally this pharmacological manipulation results in impairments of schema memory formation and retrieval in the ACC in flavor-place paired associate paradigms. Such impairments are prevented by co-administration of L-lactate.

The authors also show that activation of Gi signaling resulting in L-lactate decreased release by astrocytes impairs mitochondrial biogenesis in neurons in an L-lactate reversible manner.

By using MCT 2 inhibitors and an NMDAR antagonist the authors conclude that the molecular mechanisms underlying the observed effects are mediated by L-lactate entering neurons through MCT2 transporters and involve NMDAR.

Overall, the article's conclusions are warranted by the experimental evidence, but some weak points could be addressed which would make the conclusions even stronger.

The number of animals in some of the experiments is on the low side (4 to 6).

In the revised manuscript, we have increased the animal numbers in two key experimental groups (hM4Di-CNO and Control groups) of behavioral experiments. Now the animal numbers in different groups are as follows:

• 15 rats in hM4Di-CNO group

o Further divided into two subgroups for probe tests (PT1-4) conducted during flavor-place paired associate training; 8 rats in the hM4Di-CNO (saline) and 7 rats in the hM4Di-CNO (CNO) subgroups receiving I.P. saline or I.P. CNO, respectively, before these PTs.

• 8 rats in the Control group

• 7 rats in the Rescue group (hM4Di-CNO+L-lactate)

• 4 rats in the Control-CNO group. Animal number in this group was not increased as it was apparent from these 4 rats that CNO alone was not impairing the PA learning and memory retrieval in these rats (AAV8-GFAP-mCherry injected). Their result was very similar to the control group. Additionally, in a previous study (Liu et al., 2022), we showed that CNO administration in the rats injected with AAV8-GFAP-mCherry into the hippocampus does not show any impairments in schema.

Also, in the newly added open field test experiments to investigate the locomotor activity as suggested by the Reviewer #2, 8 rats were used in each group.

The use of CIN to inhibit MCT2 is not optimal. Authors may want to decrease MCT2 expression by using antisense oligonucleotides.

In the revised manuscript, we have conducted the experiment using MCT2 antisense oligodeoxynucleotide (ODN) as suggested.

To test whether the L-lactate-induced neuronal mitochondrial biogenesis is dependent on MCT2, we bilaterally injected MCT2 antisense oligodeoxynucleotide (MCT2-ODN, n=8 rats, 2 nmol in 1 μl PBS per ACC) or scrambled ODN (SC-ODN, n=8 rats, 2 nmol in 1 μl PBS per ACC) into the ACC. After 11 hours, bilateral infusion of L-lactate (10 nmol, 1 μl) or ACSF (1 μl) was given into the ACC and the rats were kept in the PA event arena. After 60 mins (12 hours from MCT2-ODN or SC-ODN administration), the rats were sacrificed. As shown in Author response image 1B, SC-ODN+L-lactate group showed significantly increased relative mtDNA copy number compared to the SC-ODN+ACSF group (p<0.001, ANOVA followed by Tukey's multiple comparisons test). However, this effect was completely abolished in MCT2-ODN+L-lactate group, suggesting that MCT2 is required for the L-lactate-induced mitochondrial biogenesis in the ACC.

We have integrated this new data and results in the revised manuscript.

Author response image 1.

Mitochondrial biogenesis by L-lactate is dependent on MCT2 and NMDAR. A. Experimental design to investigate whether MCT2 and NMDAR activity are required for L-lactate-induced mitochondrial biogenesis. B and C. mtDNA copy number abundance in the ACC of different rat groups relative to nDNA. Data shown as mean ± SD (n=4 rats in each group). ***p<0.001, ANOVA followed by Tukey's multiple comparisons test.

The experiment using AVP to block NMDAR only partially supports the conclusions. Indeed, blocking NMDAR will knock down any response that involves these receptors, whether L-lactate is necessary or not.

In the current study we found that Astrocytic Gi activation in the ACC reduced L-lactate level in the ECF of ACC which was also associated with decreased PGC-1α/SIRT3/ATPB/mtDNA abundance suggesting downregulation of mitochondrial biogenesis pathway. We also found that exogenous administration of L-lactate into the ACC of astrocytic Gi-activated rats rescued this downregulation. In line with this, in a recently published study (Akter et al., 2023), we found upregulation of mitochondrial biogenesis pathway in the hippocampus neurons of exogenous L-lactate-treated anesthetized rats. Another recent study has demonstrated that exercise-induced L-lactate release from skeletal muscle or I.P. injection of L-lactate can induce hippocampal PGC-1α (which is a master regulator of mitochondrial biogenesis) expression and mitochondrial biogenesis in mice (Park et al., 2021). Together, these results provide compelling evidence that L-lactate promotes mitochondrial biogenesis.

L-lactate is known to promote expression of synaptic plasticity genes like Arc, c-Fos, and Zif268 in neurons (Yang et al., 2014). After entry into the neuronal cytoplasm, mainly through MCT2, it is converted into pyruvate by lactate dehydrogenase 1 (LDH1). This conversion also produces NADH, affecting the redox state of the neuron. NADH positively modulates the activity of NMDAR resulting in enhanced Ca2+ currents, the activation of intracellular signaling cascades, and the induction of the expression of plasticity-associated genes (Yang et al., 2014; Magistretti & Allaman, 2018). The study demonstrated that L-lactate–induced plasticity gene expression was abolished in the presence of NMDAR antagonists including D-APV (Yang et al., 2014). These results suggested that the MCT2 and NMDAR are key players in the regulation of L-lactate induced plasticity gene expression.

In the current study, we investigated whether similar mechanisms might be involved in L-lactate-induced neuronal mitochondrial biogenesis. We now used MCT2 antisense oligodeoxynucleotide to decrease the expression of MCT2 (as mentioned in the previous response and Author response image 1B) and showed that MCT2 is necessary for L-lactate-induced mitochondrial biogenesis to manifest, indicating that L-lactate’s entry into the neuron is required. As mentioned before, after entry into neuron, L-lactate is converted into pyruvate by LDH, which also produce NADH, which in turn potentiates NMDAR activity. Therefore, we investigated whether NMDAR activity is required for L-lactate-induced mitochondrial biogenesis. We used D-APV to inhibit NMDAR (Author response image 1C) and found that L-lactate does not increase mtDNA copy number abundance if D-APV is given, suggesting that NMDAR activity is required for L-lactate to promote mitochondrial biogenesis.

NMDAR serves diverse functions. Therefore, as mentioned by the reviewer, blocking NMDAR may knock down many such functions. While our current data only suggests the involvement of MCT2 and NMDAR in the upregulation of mitochondrial biogenesis by L-lactate, we have not investigated other mechanisms and pathways modulating mitochondrial biogenesis that are either dependent or independent of MCT2 and NMDAR activity. Further studies are needed in future to dissect and better understand this interesting observation. We have now clarified this in the discussion section of the manuscript.

Is inhibition of glycogenolysis involved in the observed effects mediated by Gi signaling? Indeed, L-lactate is formed both by glycolysis and glycogenolysis. The authors could test whether the glycogen metabolism-inhibiting drug DAB would mimic the effects of Gi activation.

In this study we have shown that astrocytic Gi activation in the ACC leads to a decrease in the cAMP and L-lactate. L-lactate is produced by glycogenolysis and glycolysis. cAMP in astrocytes acts as a trigger for L-lactate production (Choi et al., 2012; Horvat, Muhič, et al., 2021; Horvat, Zorec, et al., 2021; Zhou et al., 2021) by promoting glycogenolysis and glycolysis (Vardjan et al., 2018; Horvat, Muhič, et al., 2021; Horvat, Zorec, et al., 2021). Therefore, one promising explanation of reduced L-lactate level observed in our study is the reduction of L-lactate production in the astrocyte due to decreased glycogen metabolism as a result of decreased cAMP. We have now mentioned this in the discussion.

DAB is an inhibitor of glycogen phosphorylase that suppresses L-lactate production. It was shown to impair memory by decreasing L-lactate (Newman et al., 2011; Suzuki et al., 2011; Iqbal et al., 2023). As we found that the impairment in the schema memory and mitochondrial biogenesis was associated with decreased L-lactate level in the ACC and that the exogenous L-lactate administration can rescue the impairments, it is likely that DAB will mimic the effect of Gi activation in terms of schema memory and mitochondrial biogenesis. However, further study is needed to confirm this.  

Reviewer #2 (Public Review):

The manuscript of Akter et al is an important study that investigates the role of astrocytic Gi signaling in the anterior cingulate cortex in the modulation of extracellular L-lactate level and consequently impairment in flavor-place associates (PA) learning. However, whereas some of the behavioral observations and signaling mechanism data are compelling, the conclusions about the effect on memory are inadequate as they rely on an experimental design that does not allow to differentiate acute or learning effect from the effect outlasting pharmacological treatments, i.e. effect on memory retention. With the addition of a few experiments, this paper would be of interest to the larger group of researchers interested in neuron-glia interactions during complex behavior.

• Largely, I agree with the authors' conclusion that activating Gi signaling in astrocytes impairs PA learning, however, the effect on memory retrieval is not that obvious. All behavioral and molecular signaling effects described in this study are obtained with the continuous presence of CNO, therefore it is not possible to exclude the acute effect of Gi pathway activation in astrocytes. What will happen with memory on retrieval test when CNO is omitted selectively during early, middle, or late session blocks of PA learning?

We have now added 8 more rats to the hM4Di-CNO group (i.e., the group with astrocytic Gi activation) to clarify the memory retrieval. These rats underwent flavor-place paired associate (PA) training similar to the previously described rats (n=7) of this group, that is they received CNO 30 minutes before and 30 minutes after the PA training sessions (S1-2, S4-8, S10-17). However, contrasting to the previous rats of this group which received CNO before PTs (PT1, PT2, PT3), we omitted the CNO (instead administered I.P. saline) selectively on these PTs conducted at the early, middle, and late stage of PA training, as suggested by the reviewer. These newly added rats did not show memory retrieval in these PTs, suggesting that the rats were not learning the PAs from the PA training sessions. See Author response image 2C-E, where this subgroup is denoted as hM4Di-CNO (Saline).

We then continued more PA training sessions (S21 onwards, Author response image 2B) for these rats without CNO. They gradually learned the PAs. PTs (PT5, PT6, PT7; Author response image 2G-I) were done during this continuation phase of PA training; once without CNO (i.e., with I.P. saline instead), and another one with CNO. As seen in the Author response image 2H and 2I, they retrieved the memory when PT6 and PT7 were done without CNO. However, if these PTs were done with CNO, they could not retrieve the memory. Together these results suggest that ACC astrocytic Gi activation by CNO during PT can impair memory retrieval in rats which have already learned the PAs.

As shown in the Author response image 2B, we replaced two original PAs with two new PAs (NPA 9 and 10) at S34. This was followed by PT8 (S35). As seen in Author response image 2J, these rats retrieved the NPA memory if the PT is done without CNO. However, they could not retrieve the NPA memory if the PT was done with CNO. This result suggests that ACC astrocytic Gi activation by CNO during PT can impair NPA memory retrieval.

In summary, these data show that astrocytic Gi activation in the ACC can impair PA memory retrieval. We have integrated this new data and results in the revised manuscript.

Author response image 2.

A. PI (mean ± SD) during the acquisition of the six original PAs (OPAs) (S1-2, 4-8, 10-17) and new PAs (NPAs) (S19) of the control (n=8), hM4Di-CNO (n=15), and rescue (hM4Di-CNO+L-lactate) (n=7) groups. From S6 onwards, hM4Di-CNO group consistently showed lower PI compared to control. However, concurrent L-lactate administration into the ACC (rescue group) can rescue this impairment. B. PI (mean ± SD) of hM4Di-CNO group (n=8) from S21 onwards showing gradual increase in PI when CNO was withdrawn. C, D, and E. Non-rewarded PTs (PT1, PT2, and PT3 conducted on S3, S9, and S18, respectively) to test memory retrieval of OPAs for the control, hM4Di-CNO, and rescue groups. The percentage of digging time at the cued location relative to that at the non-cued locations are shown (mean ± SD). In both PT2 and PT3, the control group spent significantly more time digging the cued sand well above the chance level, indicating that the rats learned OPAs and could retrieve it. Contrasting to this, hM4Di-CNO group did not spend more time digging the cued sand well above the chance level irrespective of CNO administration before the PTs. The rescue group showed results similar to the hM4Di-CNO group if CNO is given without L-lactate. On the other hand, they showed results similar to the control group if L-lactate is concurrently given with CNO, indicating that this group learned OPAs and could retrieve it. p < 0.05, p < 0.01, p < 0.001, one-sample t-test comparing the proportion of digging time at the cued sand well with the chance level of 16.67%. F. Non-rewarded PT4 (S20) which was conducted after replacing two OPAs with two NPAs (NPA 7 & 8) in S19 for the control, hM4Di-CNO, and rescue groups. Results show that the control group spent significantly more time digging the new cued sand well above the chance level indicating that the rats learned the NPAs from S19 and could retrieve it in this PT. Contrasting to this, hM4Di-CNO group did not spend more time digging the new-cued sand well above the chance level irrespective of CNO administration before the PT. The rescue group showed results similar to the hM4Di-CNO group if CNO is given without L-lactate. On the other hand, they showed results similar to the control group if L-lactate is concurrently given with CNO indicating that this group learned NPAs from S19 and could retrieve it. p < 0.001, one-sample t-test comparing the proportion of digging time at the new cued sand well with the chance level of 16.67%. G, H, and I. Non-rewarded PTs (PT5, PT6, and PT7 conducted on S23, S27, and S33, respectively) to test memory retrieval of OPAs for the hM4Di-CNO group. In both PT6 and PT7, the rats spent significantly more time digging the cued sand well above the chance level if the tests are done without CNO, indicating that the rats learned the OPAs and could retrieve it. However, CNO prevented memory retrieval during these PTs. p < 0.001, one-sample t-test comparing the proportion of digging time at the cued sand well with the chance level of 16.67%. J. Non-rewarded PT4 (S35) which was conducted after replacing two OPAs with two NPAs (NPA 9 & 10) in S34 for the hM4Di-CNO group. Results show that the rats spent significantly more time digging the new cued sand well above the chance level if CNO was not given before the PT, indicating that the rats learned the NPAs from S34 and could retrieve it in this PT. However, if CNO is given before the PT, the retrieval is impaired. *p < 0.001, one-sample t-test comparing the proportion of digging time at the new cued sand well with the chance level of 16.67%.

• I found it truly exciting that the administration of exogenous L-lactate is capable to rescue CNO-induced PA learning impairment, when co-applied. Would it be possible that this treatment has a sensitivity to a particular stage of learning (acquisition, consolidation, or memory retrieval) when L-lactate administration would be the most efficacious?

The hM4Di-CNO group, when continued with PA training without CNO (S21-S32) (Author response image 2B), was able to learn the six original PAs (OPAs). In the PT7 done at S33 (Author response image 2I), this group of rats was able to retrieve the memory if the test was done without CNO but could not retrieve the memory if CNO was given. Similarly, the Rescue group (hM4Di-CNO+L-lactate) (Author response image 2A), which received both CNO and L-lactate during PA training sessions (S1-S17), they were able to learn the OPAs. And at PT3 done at S18 (Author response image 2E), these rats were able to retrieve the memory when the test was done with CNO+L-lactate but not if the test is done with only CNO. Together, these results clearly show that ACC astrocytic Gi activation with CNO impairs memory retrieval and exogenous L-lactate can rescue the impairment. Therefore, it can be concluded that the memory retrieval is sensitive to L-lactate.

The PA learning is hippocampus-dependent. Over the course of repeated PA training, systems consolidation occurs in the ACC, after which the already learned PA memory (schema) becomes hippocampus-independent (Tse et al., 2007; Tse et al., 2011). A higher activation (indicated by expression of c-Fos) in the hippocampus relative to the ACC during the early period of schema development, and the reverse at the late stage was observed in our previous study (Liu et al., 2022). However, rapid assimilation of new PA into the ACC requires simultaneous activation/retrieval of previous schema from ACC and hippocampus dependent new PA learning (Tse et al., 2007; Tse et al., 2011). During new PA learning, increase of c-Fos neurons in both CA1 and ACC was detected (Liu et al., 2022).

Our hM4Di-CNO group received CNO 30 mins before and after each PA training session in S1-S17 (Author response image 2A). Also, the Rescue group similarly received CNO+L-lactate before and after each PA training session in S1-S17. Therefore, while this study design allowed us to conclude that ACC astrocytic Gi activation impairs PA learning and that exogenous L-lactate can rescue the impairment, it does not allow clear differentiation of the effects of these treatments on memory acquisition and consolidation. Further studies are needed to investigate this.

• The hypothesis that observed learning impairments could be associated with diminished mitochondrial biogenesis caused by decreased l-lactate in the result of astrocytic Gi-DREADDS stimulation is very appealing, but a few key pieces of evidence are missing. So far, the hypothesis is supported by experiments demonstrating reduced expression of several components of mitochondrial membrane ATP synthase and a decrease in relative mtDNA copy numbers in ACC of rats injected with Gi-DREADDs. L-lactate injections into ACC restored and even further increased the expression of the above-mentioned markers. Co-administration of NMDAR antagonist D-APV or MCT-2 (mostly neuronal) blocker 4-CIN with L-lactate, prevented L-lactate-induced increase in relative mtDNA copy. I am wondering how the interference with mitochondrial biogenesis is affecting neuronal physiology and if it would result in impaired PA learning or schema memory.

The observation of diminished mitochondrial biogenesis in the astrocytic Gi-activated rats that showed impaired PA learning is exciting. However, our study does not provide experimental data on how mitochondrial biogenesis could be associated with impaired PA learning and schema memory. Results from several previous studies linked mitochondrial biogenesis and its regulators such as PGC-1α and SIRT3 to diverse neuronal and cognitive functions as described in the discussion section of the manuscript. In the revised manuscript, we have provided further discussion as follows to discuss potential mechanisms:

“In this study, we have demonstrated that ACC astrocytic Gi activation impairs PA learning and schema formation, PA memory retrieval, and NPA learning and retrieval by decreasing L-lactate level in the ACC. Although we have shown that these impairments are associated with diminished expression of proteins of mitochondrial biogenesis, the precise mechanisms of how astrocytic Gi activation affects neuronal functions and schema memory remain to be elucidated. We previously demonstrated that neuronal inhibition in either the hippocampus or the ACC impairs PA learning and schema formation (Hasan et al., 2019). In another recent study (Liu et al., 2022), we showed that astrocytic Gi activation in the CA1 impaired PA training-associated CA1-ACC projecting neuronal activation. Yao et al. recently showed that reduction of astrocytic lactate dehydrogenase A (an enzyme that reversibly catalyze L-lactate production from pyruvate) in the dorsomedial prefrontal cortex reduces L-lactate levels and neuronal firing frequencies, promoting depressive-like behaviors in mice (Yao et al., 2023). These impairments could be rescued by L-lactate infusion. It is possible that the impairment in PA learning and schema observed in our study might have involved a similar functional consequence of reduced neuronal activity in the ACC neurons upon astrocytic Gi activation.

Schema consolidation is associated with synaptic plasticity-related gene expression (such as Zif268, Arc) in the ACC (Tse et al., 2011). L-lactate, after entry into neurons, can be converted to pyruvate during which NADH is also produced, promoting synaptic plasticity-related gene expression by potentiating NMDA signaling in neurons (Yang et al., 2014; Margineanu et al., 2018). Furthermore, L-lactate acts as an energy substrate to fuel learning-induced de novo neuronal translation critical for long-term memory (Descalzi et al., 2019). On the other hand, mitochondria play crucial role in fueling local translation during synaptic plasticity (Rangaraju et al., 2019). Therefore, it could be hypothesized that the rescue of astrocytic Gi activation-mediated impairment of schema by exogenous L-lactate could have been mediated by facilitating synaptic plasticity-related gene expression by directly fueling the protein translation, potentiating NMDA signaling, as well as increasing mitochondrial capacity for ATP production by promoting mitochondrial biogenesis. Furthermore, the potential involvement of HCAR1, a receptor for L-lactate that may regulate neuronal activity (Bozzo et al., 2013; Tang et al., 2014; Herrera-López & Galván, 2018; Abrantes et al., 2019), cannot be excluded. Future research could explore these potential mechanisms, examining the interactions among them, and determining their relative contributions to schema. Our previous study also showed that ACC myelination is necessary for PA learning and schema formation, and that repeated PA training is associated with oligodendrogenesis in the ACC (Hasan et al., 2019). Oligodendrocytes facilitate fast, synchronized, and energy efficient transfer of information by wrapping axons in myelin sheath. Furthermore, they supply axons with glycolysis products, such as L-lactate, to offer metabolic support (Fünfschilling et al., 2012; Lee et al., 2012). The association of oligodendrogenesis and myelination with schema memory may suggest an adaptive response of oligodendrocytes to enhance metabolic support and neuronal energy efficiency during PA learning. Given the impairments in PA learning observed in the ACC astrocytic Gi-activated rats in the current study, it is reasonable to conclude that the direct metabolic support to axons provided by oligodendrocytes is not sufficient to rescue the schema impairments caused by decreased L-lactate levels upon astrocytic Gi activation. On the other hand, L-lactate was shown to be important for oligodendrogenesis and myelination (Sánchez-Abarca et al., 2001; Rinholm et al., 2011; Ichihara et al., 2017). Therefore, it is tempting to speculate that a decrease in L-lactate level may also impede oligodendrogenesis and myelination, consequently preventing the enhanced axonal support provided by oligodendrocytes and myelin during schema learning. Recently, a study has demonstrated that upon demyelination, mitochondria move from the neuronal cell body to the demyelinated axon (Licht-Mayer et al., 2020). Enhancement of this axonal response of mitochondria to demyelination, by targeting mitochondrial biogenesis and mitochondrial transport from the cell body to axon, protects acutely demyelinated axons from degeneration. Given the connection between schema and increased myelination, it remains an open question whether L-lactate-induced mitochondrial biogenesis plays a beneficial role in schema through a similar mechanism. Nevertheless, our results contribute to the mounting evidence of the glial role in cognitive functions and underscores the new paradigm in which glial cells are considered as integral players in cognitive functions alongside neurons. Disruption of neurons, myelin, or astrocytes in the ACC can disrupt PA learning and schema memory.”

Reviewer #3 (Public Review):

Akter et al. investigated how the astroglial Gi signaling pathway in the rat anterior cingulate cortex (ACC) affects cognitive functions, in particular schema memory formation. Using a stereotactic approach they intracranially introduced AAV8 vectors carrying mCherry-tagged hM4Di DREADD (Designer Receptor Exclusively Activated by Designer Drugs) under astrocyte selective GFAP promotor (AAV8-GFAP-hM4Di-mCherry) into the AAC region of the rat brain. hM4Di DREADD is a genetically modified form of the human M4 muscarinic (hM4) receptor insensitive to endogenous acetylcholine but is activated by the inert clozapine metabolite clozapine-N-oxide (CNO), triggering the Gi signaling pathway. The authors confirmed that hM4Di DREADD is selectively expressed in astrocytes after the application of the AAV8 vector by analysing the mCherry signals and immunolabeling of astrocytes and neurons in the ACC region of the rat brain. They activated hM4Di DREADD (Gi signalling) in astrocytes by intraperitoneal administration of CNO and measured cognitive functions in animals after CNO administration. Activation of Gi signaling in astrocytes by CNO application decreased paired-associate (PA) learning, schema formation, and memory retrieval in tested animals. This was associated with a decrease in cAMP in astrocytes and L-lactate in extracellular fluid as measured by immunohistochemistry in situ and in awake rats by microdialysis, respectively. Administration of exogenous L-lactate rescued the astroglial Gi-mediated deficits in PA learning, memory retrieval, and schema formation, suggesting that activation of astroglial Gi signalling downregulates L-lactate production in astrocytes and its transport to neurons affecting memory formation. Authors also show that expression level of proteins involved in mitochondrial biogenesis, which is associated with cognitive functions, is decreased in neurons, when Gi signalling is activated in astrocytes, and rescued when exogenous L-lactate is applied, suggesting the implication of astrocyte-derived L-lactate in the maintenance of mitochondrial biogenesis in neurons. The latter depended on lactate MCT2 transporter activity and glutamate NMDA receptor activity.

The paper is very well written and discussed. The conclusions of this paper are well supported by the data. Although this is a study that uses established and previously published methodologies, it provides new insights into L-lactate signalling in the brain, particularly in AAC, and further confirms the role of astroglial L-lactate in learning and memory formation. It also raises new questions about the molecular mechanisms underlying astrocyte-derived L-lactate-mediated mitochondrial biogenesis in neurons and its contribution to schema memory formation.

• The authors discuss astrocytic L-lactate signalling without considering the recently discovered L-lactate-sensitive Gs and Gi protein-coupled receptors in the brain, which are present in both astrocytes and neurons. The use of nonendogenous L-lactate receptor agonists (Compound 2, 3-chloro-5-hydroxybenzoic acid) would clarify the implication of L-lactate receptor signalling in schema memory formation.

In the revised manuscript, we have included this point in the discussion section to mention the potential role of HCAR1 in schema memory as follows:

“Schema consolidation is associated with synaptic plasticity-related gene expression (such as Zif268, Arc) in the ACC (Tse et al., 2011). L-lactate, after entry into neurons, can be converted to pyruvate during which NADH is also produced, promoting synaptic plasticity-related gene expression by potentiating NMDA signaling in neurons (Yang et al., 2014; Margineanu et al., 2018). Furthermore, L-lactate acts as an energy substrate to fuel learning-induced de novo neuronal translation critical for long-term memory (Descalzi et al., 2019). On the other hand, mitochondria play crucial role in fueling local translation during synaptic plasticity (Rangaraju et al., 2019). Therefore, it could be hypothesized that the rescue of astrocytic Gi activation-mediated impairment of schema by exogenous L-lactate could have been mediated by facilitating synaptic plasticity-related gene expression by directly fueling the protein translation, potentiating NMDA signaling, as well as increasing mitochondrial capacity for ATP production by promoting mitochondrial biogenesis. Furthermore, the potential involvement of HCAR1, a receptor for L-lactate that may regulate neuronal activity (Bozzo et al., 2013; Tang et al., 2014; Herrera-López & Galván, 2018; Abrantes et al., 2019), cannot be excluded. Future research could explore these potential mechanisms, examining the interactions among them, and determining their relative contributions to schema.”

• The use of control animals transduced with an "empty" AAV9 vector (AAV8-GFAP-mCherry) compared with animals transduced with AAV8-GFAP-hM4Di-mCherry throughout the study would strengthen the results of this study, since transfection itself, as well as overexpression of the mCherry protein, may affect cell function.

We thank the reviewer for pointing this. The schema experiment includes a control group (Control-CNO group) of rats injected with AAV8-GFAP-mCherry bilaterally into the ACC. As shown in Author response image 3, after habituation and pretraining, these rats were trained for PA learning similarly to the other groups. Before 30 mins and after 30 mins of each PA training session, they received I.P. CNO. The PA learning, schema formation, memory retrieval, NPA learning and retrieval, and latency (time needed to commence digging at the correct well) were similar to the control group of rats. This result is consistent with our previous study where rats bilaterally injected with AAV8-GFAP-mCherry into CA1 of hippocampus did not show impairments in PA learning and schema formation upon CNO treatment (Liu et al., 2022).

Author response image 3.

A. PI (mean ± SD) during the acquisition of the original six PAs (OPAs) (S1-2, 4-8, 10-17) and new PAs (NPAs) (S19) of the control (n=6) and control-CNO (n=4) groups. B. Non-rewarded PTs (PT1, PT2, and PT3 done on S3, S9, and S18, respectively) to test memory retrieval of OPAs for the control-CNO group. C. Non-rewarded PT4 (S20) which was done after replacing two OPAs with two NPAs (NPA 7 & 8) in S19 for the control-CNO group. D. Latency (in seconds) before commencing digging at the correct well for control and control-CNO groups. Data shown as mean ± SD.

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Author Response:

Reviewer #1 (Public Review):

The physical principles underlying oligomerization of GPCRs are not well understood. Here, authors focused on oligomerization of A2AR. They found that oligomerization of A2AR is mediated by the intrinsically disordered, extramembraneous C-terminal tail. Using experiment and MD simulation, they mapped the regions that are responsible for oligomerization and dissected the driving forces in oligomerization.

This is a nice piece of work that applies fundamental physical principles to the understanding of an important biological problem. It is a significant finding that oligomerization of A2AR is mediated by multiple weak interactions that are "tunable" by environmental factors. It is also interesting that solute-induced, solvent-mediated "depletion interactions" can be a key driving force in membrane protein-protein interactions.

Although this work is potentially a significant contribution to the fields of GPCRs and molecular biophysics of membrane proteins in general, there are several concerns that would need to be implemented to strengthen the conclusions.

1) How reasonably would the results obtained in the micellar environment be translated into the phenomenon in the cell membranes?

1a) Here authors measured oligomerization of A2AR in detergent micelles, not in the bilayer or cellular context. Although the cell membranes would provide another layer of complexity, the hydrophobic properties and electrostatics of the negatively charged membrane surface may cooperate or compete with the interactions mediated by the C-terminal tail, especially if the oligomerization is mediated by multiple weak interactions.

The translatability of properties of membrane proteins in detergent micelles to the cellular context is a valid concern. However, this shortcoming applies to all biophysical studies of membrane proteins in non-native environments. Even for membrane proteins reconstituted in liposomes, the question arises whether the artificial lipid composition that differs from that in the human plasma membrane would alter protein properties, especially as surface charges and cholesterol content can impact membrane protein dynamics, association, and stability. In that sense, this question cannot be answered satisfyingly, especially for GPCRs that are notoriously difficult to isolate. However, we can offer some perspectives. The propensity for membrane proteins to associate and oligomerize, if anything, is greater in lipid bilayers compared to that in detergent micelles, while detergent micelles can effectively solubilize membrane protein monomers (Popot and Engelman, Biochem 1990, 29 (17), 4031–4037). Hence, the findings that A2AR readily oligomerizes in detergent micelles and that the degree of oligomerization can be systematically tuned by the C-terminal length of A2AR in the same micellar system suggest that inter-A2AR interactions are modulating receptor oligomerization; we speculate that A2AR oligomers will be present or be enhanced in the lipid bilayer environment. In fact, in the cellular context, it has been shown that A2AR assembles into homodimers at the cell surface in transfected HEK293 cells (Canals et al, J Neurochem 2004, 88, 726–734) and into higher- order oligomers at the plasma membrane in Cath.A differentiated neuronal cells (Vidi et al, FEBS Lett 2008, 582, 3985–3990). Furthermore, C-terminally truncated A2AR has been demonstrated to show no protein aggregation or clustering on the cell surface, a process otherwise observed in the WT form (Burgueno et al, J Biol Chem 2003, 278 (39), 37545–37552). These results provide the research community with a valid starting point to discover factors that control oligomerization of A2AR in the cellular context.

1b) Related to the point above (1a), I wonder if MD simulation could provide an insight into the role of the lipid bilayer in the inter- or intra-molecular interactions involving the tail. Although the neutral POPC bilayer was employed in the simulation, the tail-membrane interaction may affect oligomerization since the tail is intrinsically disordered and possess a significant portion of nonpolar residues (Fig. S4).

The reviewer brings up a valid point about the ability for MD simulations to provide insights into the role of membrane-protein interactions. In response to the reviewer, we performed additional analysis focusing on the interactions of the C-terminus with the lipid bilayer. Overall, as the C-terminus is extended, there is a decrease in its interaction with the cytoplasmic leaflet of the membrane (left figure below). More specifically, we find that the C-terminal segment associated with helix 8 (residues 291 to 314) interacts tightly with the membrane, while the rest of the C-terminus (an intrinsically disordered segment) more weakly interacts with the membrane, regardless of truncation (right figure below). As the C-terminus is extended, the inherent conformational flexibility leads to a decrease in the interactions between the protein and the bilayer. We also observe that shorter stretches of the disordered segment do have the ability to interact more closely with the membrane. While these portions include charged residues that can participate in formation of the dimer interface, no general trends are observed. We therefore cannot draw any conclusions regarding the role of C-terminal-membrane interactions on the dimerization of A2AR. What we do know is that the MD simulations presented here should be considered a model study that reveals that the charged and disordered C-terminus of A2AR can account for oligomerization via multiple and weak inter-protomer contacts.

MD simulations showing (Left) average distance of all C-terminal residues and (right) average per-residue distance from the cytoplasmic membrane of the lipid bilayer.

2) Ensuring that the oligomer distributions are thermodynamic products.

Since authors interpret the SEC results on the basis of thermodynamic concepts (driving forces, depletion interactions, etc.), it would be important to verify that the distribution of different oligomeric states is the outcome of the thermodynamic control. There is a possibility that the distribution is the outcome of the "kinetic trapping" during detergent solubilization.

This is an important question. As we have shown in the manuscript, the A2AR dimer level was found to be reduced in the presence of TCEP (Figure 2B), suggesting that disulfide linkages have a role in facilitating A2AR oligomerization. However, disulfide cross-linking reaction cannot be the sole driving force of A2AR oligomerization because (1) a significant population of A2AR dimer remained resistant to TCEP (Figure 2B), (2) A2AR oligomer levels decreased progressively with the shortening of the C-terminus (Figure 3), and (3) A2AR oligomerization is driven by depletion interactions enhanced with increasing ionic strength (Figure 5).

To answer whether A2AR oligomer is a thermodynamic or kinetic product, we tested the stability and reversibility of the A2AR monomer and dimer/oligomer population. We used SEC to separate these populations of both the A2AR-WT and A2AR-Q372ΔC variants, then performed a second round of SEC to observe their repopulation, if any. The results are summarized in the figure below, which we will include in the revised manuscript as Figure 5-figure supplement 1.

We find that the SEC-separated monomers repopulate measurably into dimer/oligomer, with the total oligomer level after redistribution comparable with that of the initial samples for both A2AR WT (initial: 2.87; redistributed: 1.60) and A2AR-Q372ΔC (initial: 1.49; redistributed: 1.40) (Figure 5-figure supplement 1A). This observation indicates that A2AR oligomer is a thermodynamic product with a lower free energy compared with that of the monomer. This is consistent with the results we have shown in the manuscript that the oligomer levels of A2AR-WT are consistent (1.34–2.87; Table S1) and that A2AR oligomerization can be modulated with ionic strengths via depletion interactions (Figure 5).

Figure S5. The dimer/oligomerization of A2AR is a thermodynamic process where the dimer and HMW oligomer once formed are kinetically trapped. (A) SEC chromatograms of the consecutive rounds of SEC performed on A2AR-WT and Q372ΔC. The first rounds of SEC are to separate the dimer/oligomer population and the monomer population, while the second rounds of SEC are performed on these SEC-separated populations to assess their stability and reversibility. The total oligomer level is expressed relative to the monomeric population in arbitrary units. (B) Energy diagram depicting A2AR oligomerization progress. The monomer needs to overcome an activation barrier (EA), driven by depletion interactions, to form the dimer/oligomer. Once formed, the dimer/oligomer populations are kinetically trapped by disulfide linkages.

Interestingly, the SEC-separated dimer/oligomer populations do not repopulate to form monomers (Figure 5-figure supplement 1). This observation is, again, consistent with a published study of ours on A2AR dimers (Schonenbach et al, FEBS Lett 2016, 590, 3295–3306). This observation furthermore indicates that once the oligomers are formed, some are kinetically trapped and thus cannot redistribute into monomers.

We believe that disulfide linkages are likely candidates that kinetically stabilize A2AR oligomers, as demonstrated by their redistribution into monomers only in the presence of a reducing agent (Figure 2B). Taken together, we suggest that A2AR oligomerization is a thermodynamic process (Figure 5-figure supplement 1B), with the monomer overcoming the activation energy (EA) by depletion interactions to repopulate into dimer/oligomer with a slightly lower free energy (given that we see a distribution between the two). Once formed, the redistributed dimer/oligomer populations can be kinetically stabilized by disulfide linkages.

3) The claim that the C-terminal tail is engaged in "cooperative" interactions is too qualitative (p. 11 line 274, p.12 line 279 and p.18 line 426).

This claim seems derived from Fig. 3b and Figs. 4b-c. However, the gradual decrease in the dimer level and the number of interactions may indicate that different parts in the C-terminal tail contribute to dimerization additively rather than cooperatively. The large decrease in the number of interactions may stem from the large decrease in the length (395 to 354). Probably, a more quantitative measure would be the number of interactions (H-bonds/salt bridges) normalized to the tail length upon successive truncation. Even in that case, the polar/charged residues would not be uniformly distributed along the primary sequence, making the quantitative argument of cooperativity challenging.

The request to clarify our basis to refer to a cooperative interaction is well taken. Figure 4B and 4C show that the truncation of one part of the C-terminus (segment 335–394) leads to a reduction in contacts of a different part (segment 291–334) of A2AR. Therefore, we conclude that the binding interactions that occur in segment 291–334 are altered by the interactions exerted by the segment 335–394. This characteristic is consistent with allosteric interactions. We believe that characterizing these interactions as “cooperative” is possible but is not fully justified in this work. We also agree with the comment that quantifying the role and segments involved in contacts would be challenging. The manuscript has been amended to use the term “allosteric” in place of “cooperative”.

4) On the compactness and conformation of the C-terminal tail:

Although the C-terminal tail is known as "intrinsically disordered", the results seem to indicate that its conformation is rather compact (or collapsed) with a number of intra- and intermolecular polar interactions (Fig. 4) and buried nonpolar residues (Fig. 6), which are subject to depletion interactions (Fig. 5). This raises a question if the tail indeed "intrinsically disordered" as is known. Recent folding studies on IDPs (Riback et al. Science 2017, 358, 238-; Best, Curr Opin Struct Biol 2020, 60, 27-) suggest that IDPs are partially expanded or expanded rather than collapsed.

We agree that our results seem to suggest that the conformation of the C-terminus could be partially compact. However, by stating that the C-terminus on average is an intrinsically disordered region (IDR), we do not exclude the possibility of partially structured regions, or greater compactness than that of an excluded volume polymer. IDR or IDP should refer to all proteins or protein regions that do not adopt a unique structure. By that standard, we know that the C-terminus of A2AR falls into that category according to our experiments and MD simulation, as well as the literature. In isolation, the majority the C-terminus is indeed an IDR, as has been demonstrated not only by simulations but also by experimental data. In fact, the C-terminus exhibits partial alpha-helical structure, and transiently populates beta-sheet conformations, depending on its state and buffer conditions (Piirainen et al, Biophys J 2015, 108 (4), 903–917). The literature studies suggest that A2AR’s C-terminus may adopt a greater level of compactness when interactions are formed between the C-terminus and the rest of the A2AR oligomer.

Reviewer #2 (Public Review):

The authors expressed A2A receptor as wild type and modified with truncations/mutations at the C-terminus. The receptor was solubilized in detergent solution, purified via a C-terminal deca-His tag and the fraction of ligand binding-competent receptor separated by an affinity column. Receptor oligomerization was studied by size exclusion chromatography on the purified receptor solubilized in a DDM/CHAPS/CHS detergent solution. It was observed that truncation greatly reduces the tendency of A2A to form dimers and oligomers. Mechanistic insights into interactions that facilitate oligomerization were obtained by molecular simulations and the study of aggregation behavior of peptide sequences representing the C-terminus of A2A. It is concluded that a multitude of interactions including disulfide linkages, hydrogen bonds electrostatic- and depletion interactions contribute to aggregation of the receptor.

The general conclusions appear to be correct and the paper is well written. This is a study of protein association in detergent solution. It is conceivable that observations are relevant for A2A receptors in cell membranes as well. However, extrapolation of mechanisms observed on receptor in detergent micelles to receptor in membranes should proceed with caution. In particular, the spatial arrangement of oligomerized receptor molecules in micelles may differ from arrangement in lipid bilayers. The lipid matrix may have a profound influence on oligomerization.

The ultimate question to answer is how oligomerization alters receptor function. This will have to be addressed in a future study.

We could not agree more. We address the concern regarding the translatability of properties of membrane proteins in detergent micelles to the cellular context in our response to Reviewer 1. In short, we believe the general propensity for A2AR to form dimers/oligomers and the role of the C-terminus will hold in the cellular context. However, even if it does not, given that biophysical structure-function studies of GPCRs are conducted in detergent micelles and other artificial environments, it is critical to understand the role of the C-terminus in the oligomerization of reconstituted A2AR in detergent micelles. How oligomerization alters receptor function is a question that is always on our mind and should be the the focus of future studies. Indeed, it has been demonstrated that truncation of the A2AR C-terminus significantly reduces receptor association with Gαs and cAMP production in cellular assays (Koretz et al, Biophys J 2021, https://doi.org/10.1016/j.bpj.2021.02.032). The results presented in this manuscript, which have demonstrated the impact of C-terminal truncation on A2AR oligomerization, will offer critical understanding for such study of the functional consequences of A2AR oligomerization.

Reviewer #3 (Public Review):

The work of Nguyen et al. demonstrates the relevant role of the C-terminus of A2AR for its homo-oligomerization. A previous work (Schonenbach et al. 2016) found that a point mutation of C394 in the C-terminus (C394S) reduces homo-oligomerization. Following this direction, more mutants were generated, the C-terminus was also truncated at different levels, and, using size-exclusion chromatography (SEC), the oligomerization levels of A2AR variants were assessed. Overall, these experiments support the role of the C-terminus in the oligomerization process. MD studies were performed and the non-covalent interactions were monitored. To 'identify the types of non-covalent interaction(s)', A2AR variants were also analysed modulating the ionic strength from 0.15 to 0.95 M. The C-terminus peptides were investigated to assess their interaction in absence of the TM domain.

The SEC results on the A2AR variants strongly support the main conclusion of the paper, but some passages and methodologies are less convincing. The different results obtained for dimerization and oligomerization are low discussed. The MD simulations are performed on models that are not accurately described - structural information currently available may compromise the quality of the model and the validity of the results (i.e., applying MD simulations to low-resolution models may not be appropriate for the goal of this analysis, moreover the formation of disulfide bonds cannot be simulated but this can affect the conformation and consequently the interactions to be monitored). Although the C-terminus is suggested as 'a driving factor for the oligomerization', the TM domain is indeed involved in the process and if and how it will be affected by modulating the solvent ionic strength should be discussed.

We thank the reviewer for the overall positive assessment and critical input. We will respond to the comments as followed.

The qualitative trend for dimerization is consistent with that for oligomerization, as demonstrated in Figs. 2A, 3B, and 5. For example, a reduction in both dimerization and oligomerization was observed upon C394X mutations (Figure 2A), as well as upon systematic truncations (Figure 3B), while very similar trends were seen for the change in the dimer and oligomer levels of all four constructs upon variation of ionic strength (Figure 5).

We agree that the experimental observation and MD simulation only incompletely describe the state of the A2AR dimer/oligomer. For example, we discover the impact of ERR:AAA mutations of the C-terminus (Figure 3C) on oligomer formation, but do not know whether this segment interacts with the TM domain or C-terminus of the neighboring A2AR. MD simulations suggest that the inter-protomer interface certainly involves inter-C-termini contact. We also mention that the A2AR oligomeric interfaces could be asymmetric, suggesting that the C-terminus can interact with other parts of the receptor, including the TM domain. However, we do not have evidence that the TM domain directly interact with each other to stabilize A2AR oligomers, and thus cannot discuss the effect of the solvent ionic strength on how the TM domain contributes to A2AR oligomerization. We minimize such discussion in our manuscript because we have incomplete insights. What we can say is that multiple and weak inter-protomer interactions that contribute to the dimer and oligomer interface formation prominently involve the C-terminus. Ultimately, the structure of the A2AR dimer/oligomer needs to be solved to answer the reviewer’s question fully.

With respect to the validity of our model, we restricted ourselves to using the best-available X-ray crystal structure for A2AR. Since this structure (PDB 5G53) does not include the entire C-terminus, we resorted to using homology modeling software (i.e., MODELLER) to predict the structures of the C-terminus. In our model, the first segment of the C-terminus consisting of residues 291 to 314 were modeled as a helical segment parallel to the cytoplasmic membrane surface while the rest of the C-terminus was modeled as intrinsically disordered. MODELLER is much more accurate in structural predictions for segments less than 20 residues. This limitation necessitated that we run an equilibrium MD simulation for 2 µs to obtain a well-equilibrated structure that possesses a more viable starting conformation. We have included this detailed description of our model in lines 641–650. To validate our models of all potential variants of A2AR, we calculated the RMSD and RMSF for each truncated variant. Our results clearly show that the transmembrane helical bundle is very stable, as expected, and that the C-terminus is more flexible (see figure below). This flexibility is somewhat consistent for lengths up to 359 residues, with a more noticeable increase in flexibility for the 394-residue variant of A2AR.

Root mean square fluctuation (RMSF) from sample trajectories of truncated variants modeled from the crystal structure of the adenosine A2AR bound to an engineered G protein (PDB ID 5G53), and the root mean square deviation (RMSD) of the C-terminus of each variant starting from residue 291.

Author Response:

Reviewer #1 (Public Review):

Wang et al., investigated the role of RNA m6A modification in intestinal epithelial cells (IECs) in the context of rotavirus infection. The authors found that the mice which specifically lacks METTL3 in IECs show resistance to rotavirus infection. They attributed this effect to increased IFN and ISG expression presumably via IRF7 upregulation. Further genetic IRF7 ablation in IECs led to the sensitivity rotavirus infection. They also found that ALKBH5 is suppressed by a rotaviral protein, although the knockout of ALKBH5 in IECs did not influence viral infection.

Overall, although the resistance of IEC-specific METTL3-deficient mice upon rotavirus infection via the control of IRF7 is a novel and interesting finding, the proposed model is not fully supported by the findings here. Especially, the following points need to be addressed:

We are grateful to the reviewer for the complimentary summary of our research. We also appreciate the valuable experiments suggested by the reviewer to improve our manuscript. We have added additional important controls and mechanistic data to further support our conclusions.

1) The m6A dot blot used in Figure 1 is not a good measurement system of total m6A modification levels, because the antibody used here also detects other RNA modification, m6Am (PMID: 31676230). Therefore, it is unclear if the increase of m6A dot blot intensity is due to the increase of m6A in RNAs mediated by METTL3 in IECs. The authors should investigate the m6A levels in IECs, not BMDMs, under METTL3 deficiency. Ideally, this analysis should be done using mass spectrometry.

We thank the reviewer for raising a critical point. We have tried several methods to avoid the potential non-specific detection of the previous antibody (Synaptic System, #202003) we used, which was reported to detect m6Am as well.

1.We have included Dot Blot data for m6A modification in Mettl3^△IEC and WT IECs during RV infection by using another m6A antibody (Anti-N6-methyladenosine (m6A), Sigma-Aldrich, Cat. No. ABE572-I). (see below and also Fig. 1d, 1e)

2.We have included mass spectrometry data for m6A modification in IECs during development (see below and also Fig. 1c) or RV infection (see below and also Fig. s3a).

These data suggested m6A modifications in IECs are indeed regulated during the development or RV infection. We have included the descriptions in the text.

Figure 1. Rotavirus infection increases global m6A modifications, and Mettl3 deficiency in intestinal epithelial cells results in increased resistance to rotavirus infection. (c) MS analysis of m6A level in ileum tissue from mice with different ages. (mean ± SEM), Statistical significance was determined by Student’s t-test (*P < 0.05, NS., not significant). (d) WT and Mettl3^△IEC mice were infected by rotavirus EW strain at 8 days post birth. m6A dot blot analysis of total RNA in ileum IEC at 2 dpi. Methylene blue (MB) staining was the loading control. (e) Quantitative analysis of (d) (mean ± SEM). Statistical significance was determined by Student’s t-test (*P < 0.05, ***P<0.001, NS., not significant). The quantitative m6A signals were normalized to quantitative MB staining signals.

Figure s3. MS analysis of total m6A level in mice ileum. (a) WT and Mettl3 △IEC mice were infected by rotavirus EW strain at 8 days post birth. MS analysis of m6A level in ileum tissue from mice at 2 dpi (mean ± SEM), Statistical significance was determined by Student’s t-test (**P < 0.005)

2) The authors show that Alkbh5 expression is increased when the mice grow up to 3 weeks old. However, the Alkbh5 protein expression changes are missing.

We thank the reviewer for raising this point. We have included the protein expression of ALKBH5 in intestine during the development (see below and Fig. s1). The ALKBH5 protein levels are increased in the intestine along with the age (Fig. s1a, s1b), which is consistent to the changes of mRNA levels of ALKBH5 during the development (Fig. 1d).

Figure s1. ALKBH5 regulate total m6A level in intestine. (a) Immunoblotting with antibodies target ALKBH5 and TUBULIN in ileum tissues from mice with different ages. (b) Quantitative analysis of (a) (mean ± SEM), Statistical significance was determined by Student’s t-test (*P < 0.05, NS., not significant).

3) The authors claim that m6A declined from 2 to 2 weeks post birth is caused by increased Alkbh5 (Line 110). However, it is not clear if the subtle increase in Alkbh5 mRNA leads to the change in global m6A levels. The author can use ALKBH5-deficient mouse cells to confirm this point.

We thank the reviewer for pointing out an important point. We have included the ALKBH5 over-expression or knock-down data in a mouse IEC cell line MODE-K, to test whether the regulation of Alkbh5 mRNA in IECs leads to the change in global m6A levels.

Over-expression of ALKBH5 in MODE-K cells largely reduced the global m6A level (see below and Fig. s1d). 1. Crispr-mediated knock down of ALKBH5 in MODE-K cells augmented the global m6A level while knock down of another m6A eraser FTO in MODE-K cells didn’t affect the global m6A level (see below and Fig. s10b).

Figure s1. ALKBH5 regulate total m6A level in intestine. (d) Immunoblotting with antibodies target ALKBH5 and TUBULIN in MODE-K cells transfected with pSIN-EV or pSIN-mAlkbh5-3xFlag for 24h. m6A dot blot analysis of total RNA in indicated samples. Methylene blue (MB) staining was the loading control.

Figure s10. Alkbh5 is the dominant m6A eraser in intestine. (b) m6A dot blot analysis of total RNA in different MODE-K cells. Methylene blue (MB) staining was the loading control.

4) The authors should describe the overall phenotype of IEC-specific METTL3-deficient mice at the steady state. It is important to clarify if the augmented expression of ISG upon METTL3 deficiency is dependent on rotavirus infection. Also, the authors should describe any detectable abnormalities or changes without stimulation.

We actually collaborated another group and found there is a defect in intestinal stem cells in IEC-specific METTL3-deficient mice. However, as RV normally infected IECs in the villi but not in the crypt, and stem cells are not the major producers of IFN/ISGs (Sue E. Crawford et al. Nature reviews disease primers, 2017). The defect in intestinal stem cells will less likely affect the RV infection phenotype. As it is another story that are under review, we tend to not include this part of the data in our manuscript. Moreover, we have crossed Irf7^−/− mice to Mettl3^ΔIEC mice and verified Irf7 mediated induction of ISGs is critical for the anti-viral phenotype in Mettl3^ΔIEC mice.

Our bulk RNA-seq data in IECs showed the augmented expression of ISGs upon METTL3 deficiency in steady state (Fig. 2a). We also found an augmented ISG expression in intestine of METTL3-deficient mice in steady state or early infection of RV (2d) by qPCR. However, as the RV loads in METTL3-deficient mice during the late infection stage are significantly lower than WT mice, thus the inducible ISGs expressions are consequently lower in intestine of METTL3-deficient mice than WT mice in day 4 post infection (Fig. 3f).

5) The finding that IRF7 is targeted by METTL3 is not convincing. First, the authors performed MeRIP-seq and -qPCR experiments only using RNAs from wild-type IECs not from METTL3-deficient cells. It is necessary to show that the modification levels on IRF7 mRNA is indeed reduced upon METTL3 deficiency. Second, it is unclear if MeRIP-seq is properly performed or not, because there is no quality checking figure shown. For instance, the authors can generate metagene plots or gene logos of m6A modified sites to see if there is any consistency with previous reports. Third, in Figure 2h, the authors should show that the change in luciferase activity between wild-type and mutant Irf7-3'UTR reporters is dependent on METTL3 activity by performing METTL3 knockdown or knockout. Also, the authors should describe how they mutagenize the sequences for clarification. Fourth, in Figures 2F and 3C, they showed that IRF7 is upregulated in METTL3-deficient IECs while in Figure 3F, IRF7 is conversely downregulated in METTL3-deficient IECs. This is apparently contradictory to each other.

We appreciate the valuable suggestion provided by the reviewer to improve our manuscript.

1. We have done RIP-qPCR in Mettl3 knock-down and WT MODE-K cells to verify the m6A modification on IRF7 mRNA, the modification levels on IRF7 mRNA is indeed reduced upon METTL3 deficiency (see below and Fig. s5c, s5d). We have added the description of the experiment in the manuscript.

Figure s5. Characterization of m6A modifications on Irf7 mRNA. (c) m6A-RIP-qPCR confirms Irf7 as an m6A-modified gene in IECs. Fragmented RNA of sgEV and sgMettl3 MODE-K cells was incubated with an anti-m6A antibody (Sigma Aldrich ABE572-I). The eluted RNA and input were processed as described in ‘RT-qPCR’section, the data were normalized to the input samples (n=3, mean ± SEM, Statistical significance was determined by Student’s t-test (*P < 0.05, **P < 0.005, NS., not significant). Tlr3 and Rps14 were measured with m6A sites specific qPCR primer as positive control and negative control, Irf7 was measured with predicted m6A sites specific qPCR primers. (d) Knock down efficiency of METTL3 in MODE-K cells.

1. We have performed metagene plots as suggested. As shown in figure s5b, the m6A peak is enriched near the stop codon and 3’UTR region, which is consistent with previously study (Xuan et al. 2018; Dominissini et al., 2012; Yang et al., 2019). We have added the description in the manuscript.

Figure s5. Characterization of m6A modfications on Irf7 mRNA. (b) Metagene plots of m6A modified sites.

1. We have performed the luciferase assay in WT and METTL3 knockdown 293t cell, and found increased luciferase activity in mutant Irf7-3'UTR reporters is dependent on METTL3 activity (see below and fig. 2h, s5e). We have added the description of the experiment into the manuscript.

Figure 2. Mettl3 deficiency in intestinal epithelial cells results in decreased m6A deposition on Irf7, and increased interferon responses. (h) Relative luciferase activity of sgEV and sgMettl3 HEK293T cells transfected with pmirGLO-Irf7-3’UTR (Irf7-WT) or pmirGLO-Irf7-3’UTR containing mutated m6A modification sites (Irf7-MUT). The firefly luciferase activity was normalized to Renilla luciferase activity (n=3, mean ± SEM). Statistical significance was determined by Student’s t-tests between genotypes (*P < 0.05, NS., not significant).

Figure s5. Characterization of m6A modifications on Irf7 mRNA. (e) Knock down efficiency of METTL3 in 293t cells used for luciferase assay.

1. IRF7 is an ISG. The expression of IRF7 is controlled by both PAMP (such as virus component)-induced transcription and post-transcriptional regulation like m6A modification mediated mRNA decay. In steady state or early stage (2d) of rotavirus infection, there is no virus or the viral loads is comparable in both Mettl3^△IEC mice and WT mice, thus, IRF7 expression is mainly regulated by m6A and is higher in IECs from Mettl3^△IEC mice in comparison with that from WT mice. However, as the RV loads in Mettl3^△IEC mice during the late infection stage are significantly lower than WT mice, in this case, IRF7 expression is mainly regulated by the PAMP from virus, thus the inducible IRF7 expressions is consequently lower in intestine of Mettl3^△IEC than WT mice in day 4 post infection (Fig. 3f).

6) It is unclear if the augmented expression of IRF7 per se upregulates IFN and ISG expression. Since IRF7 exerts its transcriptional activity upon phosphorylation, the authors should examine IRF7 phosphorylation and total protein levels in METTL3-deficient IECs. Also, it is interesting to see if the phosphorylation of TBK1 is augmented or not.

We have provided the phosphorylation and total protein levels of IRF7 and TBK1 in MODE-K cells treated with poly I:C. Both total IRF7 and phosphorylated IRF7 are upregulated in Mettl3-knock down cells compare to control cells (see below and Fig s5f). However, Both total TBK1 and phosphorylated TBK1 remain unchanged (Fig s5f), suggesting the augmented ISGs are less likely due to the activation of the upstream signal of IFN.

Figure s5. Characterization of m6A modifications on Irf7 mRNA. (f) Western blot analysis of sgEV and sgMettl3 MODE-K cells transfected by lipo3000 with 2ug/ml poly I:C at indicated hours post transfection, at least three replicate experiments were performed.

7) In Figure 3, the authors utilized METTL3 and IRF7 deficient mice to show the contribution of METTL3-mediated IRF7 regulation in rotavirus infection. However, if IRF7 is totally abrogated, IFN production should be greatly impaired as shown in Figure 3A. Thus, it is not surprising to see that the IFN response is diminished. The authors can use heterozygous IRF7 deficient mice instead to check if upregulation of IRF7 under METTL3 deficiency is critical to control rotavirus infection.

We thank the reviewer for pointing out an important issue. However, we checked the IRF7 expression levels in IECs from Irf7^+/+ , Irf7^+/- and Irf7^-/- mice and found that there is no difference between IRF7 levels in IECs from Irf7^+/- mice and that in IECs from Irf7^+/+ mice. Thus, it is not feasible to use heterozygous IRF7 deficient mice to test the idea (Supporting Figure 1).

Supporting Figure 1. WT and Irf7 Heterozygous mice show same IRF7 expression level in IECs. (a) IECs from 2-weeks-old Irf7^+/+ , Irf7^+/-, Irf7^-/- mice were isolated. Western blot analysis show IRF7 expression level in different mice. (b) Quantitative analysis of (a) (mean ± SEM), statistical significance was determined by Student’s t-test ( ***P < 0.001, NS., not significant).

8) Given no effect of ALKBH5 knockout on rotavirus infection as shown in Figure 4, it is questionable if ALKBH5 has a profound role in the regulation of m6A in IECs. The authors should determine if m6A modification levels are increased in IECs under ALKBH5 deficiency.

We performed the m6A dot blot assay to detect m6A modification levels in ALKBH5-knock down MODE-K cells and we do find an increase of m6A modification level under ALKBH5 deficiency (see above and Fig s10). No effect of ALKBH5 knockout on rotavirus infection actually puzzled us as well before (Fig.4c, 4d and 4e), until we found RV infection down-regulated ALKBH5 expression in the intestine of WT mice (Fig.4a).

Author Response

Reviewer #1 (Public Review):

This work raises the question of how in plane forces generated at the apical surface of an epithelial cell sheet cause out of plane motion, an important morphogenetic motif. To address this question, a new ontogenetic dominant negative rho1 tool, based on the cry2-CIBN system is presented. The authors use this tool to analyze the well studied biophysical process of ventral furrow formation, and dissect the spatiotemporal requirement of rho1 signaling to modulate myosin accumulation. They separate the effect on morphogenesis into an early phase that becomes significantly slowed down by myosin inhibition, and a late phase where the kinetics is comparable to wild type despite treatment. For interpretation of the data, an older model of cell mechanics treating tissue as a purely elastic material is presented. It fails to reproduce the observations. As a modification, in analogy to buckling of a thin beam under load, a compressive stress exerted by the adjacent ectoderm is introduced. Further analysis of cell behaviors in response to various laser mediated tissue manipulations is presented as support of the proposed mechanism.

Overall, the manuscript addresses an important aspect of morphogenesis. In particular the use of optogenetic tools promises new insights that might be more challenging to achieve with traditional mutant analysis. However, reservations remain with respect to (1) rigor of the analysis, and (2) interpretation and quality of the data in support of the proposed mechanism; this applies in particular to presentation of biophysical observations, including experiment and simulations.

The manuscript adds valuable quantitative data, in particular the findings described in Fig 2ab. However, insufficient analysis are performed to fully support the claims of the manuscript by the data presented.

(I) The manuscript proposes an elasticity based model of tissue mechanics, but provides no experimental evidence in support of this assumption. Many rheology studies performed in a wide range of specimen (including the Drosophila embryo) found a separation of time scales, that shows elasticity is a good approximation of tissue mechanics only for time scales short compared to the process studied here.

We agree with the reviewer that an elasticity-based model of tissue mechanics is a simplification for the actual tissue properties in the real embryos. To provide justification for this simplification, in the revised manuscript, we have cited a previous biophysical study measuring tissue viscoelasticity in early Drosophila embryos (Doubrovinski et al., 2017). Using a magnetic tweezers-based approach, Doubrovinski et al. shows that the lower bound of the decay time of the elastic response is four minutes (the lower limit on the timescales where tissue behaves elastically). In addition, when history dependence of the response is considered, the decay time increases to nine minutes, which is close to the duration of ventral furrow formation (~ 15 – 20 minutes). Therefore, we consider elasticity is a reasonable approximation of tissue mechanics during ventral furrow formation. The elasticity assumption has been widely used in the previously published modeling work to simulate ventral furrow formation (Allena et al., 2010; Conte et al., 2009; Gracia et al., 2019; Heer et al., 2017; Hocevar Brezavšček et al., 2012; Muñoz et al., 2007; Rauzi et al., 2015).The modeling framework used in our current study, which is initially described in Polyakov et al. 2014, successfully predicts the intermediate and final furrow morphologies with a minimal set of active and passive forces without prescribing individual cell shape changes. It is therefore advantageous to use this model to explore the main novel aspect of the folding mechanics underlying ventral furrow formation. We show that the model can recapitulate the binary tissue response to acute myosin inhibition. In addition, it accurately predicts the intermediate furrow morphology at the transitional state and several other morphological properties associated with myosin inhibition. We therefore believe that this minimalistic model captures the central aspect of the physical mechanism underlying mesoderm bistability observed in the experiments.

(II) The manuscript uses a method of micro-dissection to soften cells, but does not provide a clear definition of the concept softening, provides no rational for the methods functioning, and does not provide independent validation. The described treatment might affect cells in many alternative ways to the offered interpretation. This data is the central experimental evidence given in support of the proposed ectoderm compression mechanism, and therefore it is essential to provide a precise physical explanation of the method, and validation of measurements that bolster the conclusion.

We apologize for not explaining the meaning of “softening” clearly in our original manuscript and the rationale for using laser ablation to detect compression. By “softening”, we meant to describe the mechanical status of the cell when the subcellular structures that normally support the mechanical integrity (e.g., cortical actin) are disrupted. We reason that when such a change in mechanical properties happens in a specific region of a tissue that is under compression, the cells in this region should have an impaired ability to resist compression from outside of the region and thereby cause the region to shrink.

Laser ablation has been widely used to measure tensile stresses in cells and tissues by disruption of cells or subcellular structures. The method we used is adapted from previous described protocols, where a femtosecond near infrared laser is used to disrupt subcellular structures for detection of tissue tension (Rauzi et al., 2015; Rauzi et al., 2008).It has been shown that when laser intensity is properly controlled, the treatment can leave the plasma membrane intact but disrupt subcellular structures associated with the plasma membrane, such as adherens junctions and the cortical actomyosin networks (Rauzi et al., 2015; Rauzi et al., 2008).Using a femtosecond near infrared laser, we were able to ablate embryonic tissues that are under tension and observe tissue recoil after laser ablation, suggesting that our approach has disrupted the cortical cytoskeleton in the laser treated region (e.g., Figure 3 and Authors’ Response Figure 1). In these experiments, the lack of damage on the plasma membrane is indicated by the readily recovery of the plasma membrane signal after laser treatment, as well as the lack of bright burn marks on the tissue.

As we noted before, we reasoned that if tissue is compressive, similar laser treatment that generates tissue recoil in tissues under tension should result in tissue shrinking within the laser-treated region. The data presented in our original manuscript demonstrate that tissue shrinking is not a non-specific response to our laser treatment – we did not observe such a response when we treat the tissue during cellularization or within the first five minutes of gastrulation, although identical experimental conditions were used (Original Figure 4). We have also obtained additional evidence that supports the use of tissue shrinking as a readout of tissue compression. We tested our laser ablation approach in Stage 8 – 9 embryos at regions where cells are actively dividing/proliferating, which would expect to generate compressive stresses in the tissue. As we perform laser ablation in this region, we observed shrinking of the treated region, which was distinct from the tensile tissue response (Authors’ Response Figure 1). While this preliminary evidence is encouraging, we agree with the reviewer that further independent validations are needed given that the methods for detecting tissue compression have not been well established in the field. Following the editor’s suggestion, we have removed this experiment from the current manuscript and focus on the characterization of the optogenetic tool and the binary tissue response after acute actomyosin inhibition.

Authors’ Response Figure 1: Laser ablation in regions of tissues with active cell proliferation (a) or undergoing apical constriction (b). The movement of tissues is indicated by overlaying membrane signals (Ecadherin-GFP) at T = 0 sec and at T = 10 sec. T = 0 in the “After ablation” panels marks the time immediately after ablation. (a) Stage 8 – 9 embryos. Multiple cells are in the process of cell division, as indicated by mitotic rounding (yellow arrowheads) or the appearance of cleavage furrows (red arrowheads). Immediately after laser ablation, the surrounding cells moved towards the ablated region (cyan arrows). (b) An embryo undergoing ventral furrow formation. Ablation within the constriction domain results in recoil of the surrounding cells away from the ablated region (cyan arrows).

(III) Mechanical isolation of the mesoderm is a very exciting approach to test the possible involvement of adjacent tissues in folding. Indeed, the authors report a delay of ventral furrow formation. However, there is no evidence provided that (a) the mesoderm is mechanically uncoupled, and (b) that the treatment did not have undesired side effects. For example, a similar procedure (so-called cauterization, see Rauzi 2015) has been used to immobilize cells in the Drosophila embryo. Such an effect could account for the observed delay in furrow formation.

We agree with the reviewer that “mechanical uncoupling” is merely a prediction based on our observation but has not been directly demonstrated. On the other hand, since the purpose of this experiment is to ask whether the presence of the lateral ectoderm is important for the mesoderm to transition between apical constriction and invagination (and our result shows yes), whether the approach we used mechanically uncoupled mesoderm and the ectoderm is no longer an immediately relevant question. We apologize for the imprecise use of the term “mechanically uncoupling” in our original manuscript and we thank the reviewer for pointing this out.

As for the reviewer’s point (b), we have several pieces of evidence indicating that our approach did not cause anchoring of the tissue to the vitelline membrane. The major difference between the approach we used and that used by Rauzi et al. 2015 is the location of the tissue where the laser treatment was imposed. In order to anchor the tissue to the vitelline membrane, Rauzi et al. target the laser to the apical side of the tissue, adjacent to the vitelline membrane. The resulting cauterization of the tissue caused anchoring of the tissue to the vitelline membrane, presumably by fusion of the tissue with the vitelline membrane. In our approach, we used similar type of laser (femtosecond near infrared laser) to perform tissue disruption, but instead of targeting the apical side of the tissue, we targeted the basal region of the invaginating cleavage furrows during cellularization, with the goal to block cell formation. While the laser intensity we used is high enough to cause cauterization of the tissue as indicated by the appearance of bright autofluorescence in the laser treated region, these “burn marks” are not located at the apical side of the cells (Authors’ Response Figure 2a). The lack of “burn marks” on the vitelline membrane in our experiment is in sharp contrast to the result shown in Rauzi et al 2015 (see Authors’ Response Figure 2b for an example from Rauzi et al in comparison to our own data in 2a). Because of the difference in the location of cauterization, we do not expect that the tissue would be fused with the vitelline membrane after our treatment. This is further suggested by the observation that the burn marks can move before the onset of gastrulation, which again indicates that the tissue is not anchored to the vitelline membrane (Authors’ Response Figure 2c).

That being said, we acknowledge that we do not fully understand the impact of the laser treatment on the embryo (e.g., what causes the reduced rate of apical constriction), and more control experiments are required in order to fully describe the tissue response we observed. As suggested by the editor, we decided to remove the ectoderm-ablation experiment from the revised manuscript and focus on the characterization of the optogenetic tool and the binary tissue response after acute actomyosin inhibition.

Authors’ Response Figure 2: Laser disruption of cell formation in the lateral ectodermal region. (a) Cross-section and en face views showing the basal location of the “burn marks” after laser disruption in the lateral ectodermal region. No burn marks are observed at the level of the vitelline membrane. Blue and red curves in the cross-section views indicate the vitelline membrane and the position where the projections were made for the en face views. Magenta arrows: burn marks. (b) Figure 5a from Rauzi et al., 2015, clear bright burn marks can be seen from the apical surface view. (c) Overlay of the signal at T = -10 min and 0 min (onset of gastrulation) showing the movement of burn marks before gastrulation (yellow arrows).

(IV) Some panels show two distinct molecules tagged with the same or spectrally overlapping flurophores, that unfortunately localize in similar spatial patterns. This encumbers data validation.

We agree with the reviewer that having two distinct proteins tagged with the same fluorophore is not ideal for understanding the behavior of the tagged proteins, however, it usually does not affect the evaluation of the cell or tissue morphology, as far as the cell membrane is explicitly labeled. For example, in our original Figure 2 (new Figure 4), although GFP is tagged on both CIBN and Sqh, and mCherry is tagged on both CRY2-Rho1DN and Sqh, the cell and tissue morphology is clearly discernable by these markers, which allowed us to evaluate the progression of ventral furrow formation. In the cases where there was a need to evaluate the behavior of a particular molecule (e.g. Sph), we always repeated the experiments in a way such that the molecule of interest is tagged with a distinct fluorophore that does not spectrally overlap with other fluorophores – this often requires the use of an plasma membrane anchored CIBN that is not fluorescently tagged (e.g. Figure 1, Figure 4 – figure supplement 3).

(V) The physical model is a central part for data interpretation. In its current form it is very challenging to follow. It is also critical the system be studied with proper cell aspect ratio, as the elasticity of thin sheets has a well established non-linear thickness dependence.

These are valid critiques of our thin layer physical model (original Figure 5). The original purpose of this model is not to recapitulate the actual furrow morphology or cell shape change observed in the actual embryo, but rather to test the possibility of recapitulating the acceleration in tissue flow during the folding process by combining local constriction and global compression in a spherical (circular in 2D) elastic shell. Developing a dynamic vertex model that contains the realistic cell aspect ratio comparable to the actual cells in the embryo while displaying realistic cellular dynamics during the folding process is nontrivial and need substantial further development of the model. Since the manuscript is now focused on the bistable characteristics of the mesoderm during gastrulation rather than tissue dynamics during the folding process, we decide to leave the dynamics vertex model out of the revised manuscript, as suggested by the editor.

Reviewer #2 (Public Review):

Guo and colleagues aim to unravel the mechanisms driving the fast process of mesoderm invagination in the Drosophila early developing embryo. While cell apical constriction is known to drive ventral furrowing (1st phase), it is still not clear if apical constriction is necessary/sufficient to drive mesoderm internalization (2nd phase) and weather other mechanisms cooperate during this process. By using 1ph optogenetics, the authors cannot test specifically the role of apical constriction but can systematically affect the overall actomyosin network in ventral cells in a time specific fashion (1-minute resolution). In this way, they come to the conclusion that actomyosin contractility is necessary for the 1st phase but not for the 2nd phase of mesoderm invagination. Interestingly, they conclude that the system is bistable. In the second part of this study, the authors test the role of the coupling between mesoderm and ectoderm by using 2D computational modelling and infrared pulsed laser dissection. They propose that the ectoderm can generate compressive forces on the mesoderm facilitating mesoderm internalization (2nd phase).

This project is of interest since it tackles a key morphogenetic process that is necessary for the development of the embryo. The conclusion of 'bistability' resulting from the RhoDN optogenetic experiments (1st part of this study) are well supported and quite interesting. The IR laser experiments used to tackle the coupling between ectoderm and mesoderm (2nd part of the study) are key to support main conclusions, nevertheless their experimental design and results are puzzling. It is not clear what the authors are actually doing to the tissues. The experiments performed in the 2nd part of this study need to be revisited and conclusions eventually softened.

Major comments:

1) The 920 nm laser ablation of ectoderm cells is a key experiment in this study to support the ectoderm compression hypothesis. Nevertheless, this experiment is puzzling: the rationale of the experimental design, the effect of the laser on cells and the interpretation of the results are unclear.

The rationale for the laser ablation experiment designed to test tissue compression is analogous to the widely used laser ablation approach for detecting tissue tension (Rauzi et al., 2015; Rauzi et al., 2008). In typical experiments where laser ablation was used to measure tensile stresses in cells and tissues, ablation of cells or subcellular structures that are under tension results in recoil of surrounding cell/tissue structures. We reasoned that if the tissue is under compression, similar laser treatment should result in shrinking of the laser-treated region, as the cells in the laser-treated region are expected to have an impaired ability to resist compressive stresses from outside of the region.

In our experiment, we used the reduction of the width of the laser treated region within the first 10 sec after laser treatment as the measure for tissue shrinking, which we considered as an indication for the presence of compressive stresses. This tissue response, albeit mild, is not a non-specific tissue response to our laser treatment – we did not observe tissue shrinking when we treat the tissue during cellularization or within the first five minutes of gastrulation, although identical experimental conditions were used. The rate and magnitude of tissue shrinking after laser treatment is determined by multiple factors, including the level of compressive stresses, the difference in cell rigidity before and after laser treatment, and the overall viscosity of the tissue. We acknowledge that the knowledge on these factors is largely lacking, and therefore additional independent validations of our approach are needed to further strengthen our conclusion on the presence of tissue compression. Following the editor’s suggestion, we decided to remove the laser ablation experiment from the current manuscript and focus on the characterization of the optogenetic tool and the binary tissue response after acute actomyosin inhibition.

2) The authors propose to use again 920 nm laser ablation but this time to "physically separate" the two ectoderms from the ventral tissue. This is again a key experiment, but it raises some concerns:

a. "Physical separation" would need to be demonstrated (e.g., EM after laser ablation). From Fig. 6b it is clear that IR laser ablation results in prominent auto-fluorescent zones. This has been already reported in previous work (De Medeiros G. et al. Scientifc Reports 2020) showing that high power and sustained IR fs laser targeting produces auto-fluorescence and highly electron-dense structures in the early developing Drosophila embryo. This process is referred to laser cauterization that does not induce separation between tissues. This structures eventually displace together with the lateral tissue (also shown in Fig.6 b). b. This strong laser "treatment", that should be ectoderm specific, results in perturbation of other non-ectoderm related processes (e.g., mesoderm apical constriction as shown by the authors). This can support the idea that many other processes are affected and that in general this laser heating "treatment" has global effects. These results might invalidate the conclusion proposed by the authors.

These are both valid critiques. As for the reviewer’s point “a”, we agree with the reviewer that a “physical separation” of the mesoderm from the ectoderm has not been rigorously demonstrated in our original manuscript. As detailed in our response to reviewer #1 comment #3, since the purpose of this experiment is to ask whether the presence of the lateral ectoderm is important for the mesoderm to transition between apical constriction and invagination (and our result shows yes), whether the approach we used physically separated the mesoderm and the ectoderm is no longer an immediately relevant question. We apologize for the vague use of “physical separation” in our original manuscript and we thank the reviewer for pointing this out.

To address the reviewer’s point “b” and to ask whether the laser treatment used in our experiment has a global effect, we performed a control experiment where we treated the yolk region of the embryo with the identical approach. Despite the appearance of burn marks in the treated yolk region, mesoderm invagination proceeded largely normally under this condition, with a mild reduction in the rate of furrow invagination (Authors’ Response Figure 3). Therefore, the prominent delay in the transitional state we observed after disruption of lateral ectoderm (Original Figure 6) is not likely caused by non-specific laser heating effect. In addition, in both the yolk-ablation and the ectoderm-ablation experiments, cellularization occurred normally outside of the laser-treated regions, in further support of the lack of strong non-specific effect from our laser treatment. That being said, we acknowledge that we do not fully understand the impact of the laser treatment on the embryo (e.g., what causes the reduced rate of apical constriction), and more control experiments are required in order to fully describe the tissue response we observed. As suggested by the editor, we decided to remove the ectoderm-ablation experiment from the revised manuscript and focus on the characterization of the optogenetic tool and the binary tissue response after acute actomyosin inhibition.

Authors’ Response Figure 3. Laser treatment in the yolk region of the embryo. (a) Cartoon depicting the position of laser treatment. Similar laser condition was used as described in the original Figure 6. Laser ablation was performed during cellularization and the treated embryo was imaged during gastrulation. (b) An example control embryo without laser treatment. (d-e) Two examples showing ventral furrow formation after laser treatment in the yolk region. Only a mild delay in furrow invagination was observed. Red arrowheads indicate the invagination front. Scale bar: 25μm.

Reviewer #3 (Public Review):

The authors address how contractile forces near the apical surface of a cell sheet drive out-of-plane bending of the sheet. To determine whether actomyosin contractility is required throughout the folding process and to identify potential actomyosin independent contributions for invagination, they develop an optogenetic-mediated inhibition of myosin and show that myosin contractility is critical to prevent tissue relaxation during the early stage of folding but is dispensable for the deepening of the invagination. Their results support the idea that the mesoderm is mechanically bistable during gastrulation. They propose that this mechanical bistability arises from an in-plane compression from the surrounding ectoderm and that mesoderm invagination is achieved through the combination of apical constriction and tissue compression. Regarding global message of the manuscript, I have two main critics. The authors consider their work as the first to prove that there is a additional mechanism to apical constriction leading to invagination. This is not true. First, the fact that the ectoderm could exert a compressive force on the invaginating mesoderm is not new and has been not only proposed, but tested previously (Rauzi and Leptin, 2015). Second, several recent publications demonstrated that on top of apical constriction, lateral forces were also required for the invagination and the authors ignore these data (Gracia et al, 2019 ; John et al, 2021).

We thank the reviewer for this important comment. In the original Introduction, we have mentioned several previous studies that suggest the presence of additional mechanisms to apical constriction during ventral furrow formation. We stated: “The observation that the maximal rate of apical constriction and the maximal rate of tissue invagination occur at distinct times suggests that apical constriction does not directly cause tissue invagination (Polyakov et al., 2014; Rauzi et al., 2015). A number of computational models also predict that mesoderm invagination requires additional mechanical input, such as “pushing” forces from the surrounding ectodermal tissues, but experimental evidence for this additional mechanical input remains sparse (Munoz et al., 2007; Conte et al., 2009; Allena et al., 2010; Brodland et al., 2010).”

To address the reviewer’s comment, in the revised manuscript, we expanded this paragraph to further elaborate the previous contributions: “However, accumulating evidence suggests that apical constriction does not directly drive invagination during the shortening phase. First, it has been observed that the maximal rate of apical constriction (or cell lengthening) and the maximal rate of tissue invagination occur at distinct times (Polyakov et al., 2014; Rauzi et al., 2015). Second, it has been previously proposed, and more recently experimentally demonstrated, that myosin accumulated at the lateral membranes of constricting cells (‘lateral myosin’) facilitates furrow invagination by exerting tension along the apical-basal axis of the cell (Brodland et al., 2010; Conte et al., 2012; Gracia et al., 2019; John and Rauzi, 2021). Finally, a number of computational models predict that mesoderm invagination requires additional mechanical input from outside of the mesoderm, such as “pushing” forces from the surrounding ectodermal tissue (Munoz et al., 2007; Conte et al., 2009; Allena et al., 2010; Brodland et al., 2010). These models are in line with the finding that blocking the movement of the lateral ectoderm by laser cauterization inhibits mesoderm invagination (Rauzi et al., 2015). A similar disruption of ventral furrow formation can also be achieved by increasing actomyosin contractility in the lateral ectoderm (Perez-Mockus et al., 2017). While these pioneer studies highlight the importance of cross-tissue coordination during mesoderm invagination, the actual mechanical mechanism that drives the folding of the mesodermal epithelium and the potential role of the surrounding ectodermal tissue remain to be elucidated.”

One of the motivations for us to develop experimental approaches to detect compression in the ectoderm (original Figure 4) and to disrupt the ectoderm (original Figure 6) is the lack of direct evidence demonstrating the mechanical contribution of the ectoderm to mesoderm invagination. Several studies have shown that manipulations of the ectodermal tissue can impair ventral furrow formation. One study shows that preventing the movement of the lateral ectoderm, by anchoring ectodermal cell apices to the vitelline membrane, blocks ventral furrow invagination(Rauzi et al., 2015). Another study shows that upregulation of apical myosin contractility in the lateral ectodermal tissues can inhibit or even reverse the furrow invagination process (Perez-Mockus et al., 2017). These results indicate that an increase in the resistance to mesoderm movement can impair mesoderm invagination. However, this would be expected even if the ectoderm does not provide active mechanical input to facilitate mesoderm invagination. Therefore, these experiments, while very informative, did not provide direct evidence for a role of ectodermal compression in mesoderm invagination.

Another motivation for us to examine potential mechanisms outside of the mesoderm is the observation that ventral furrow invagination continues even when both apical myosin and lateral myosin are disrupted after Ttrans (Late Group embryos). This result indicates that factors other than apical or lateral myosin must be responsible for the invagination of the furrow in Late Group embryos. In the revised manuscript, we used a modeling approach to demonstrate that lateral myosin and ectodermal compression may function in parallel to promote the invagination of the ventral furrow (Figure 7). In the revised Discussion, we propose that “ventral furrow formation is mediated through a joint action of multiple mechanical inputs. Apical constriction drives initial indentation of ventral furrow, which primes the tissue for folding, whereas the subsequent rapid folding of the furrow is promoted by bistable characteristic of the mesoderm and by lateral myosin contractions in the constricting cells.”

They generated an optogenetic tool, "Opto-Rho1DN", to inhibit Rho1 through light-dependent plasma membrane recruitment of a dominant negative form of Rho1 (Rho1DN). The specificity of local inactivation of Myosin was tested on apical myosin before and during invagination. They observed a strong reduction of Myosin II recruitment and a phenotype that mimicks Rok inhibition. They found that acute loss of myosin contractility during most of the lengthening phase results in immediate relaxation of the constricted tissue, but similar treatment near or after the lengthening-shortening transition does not impede invagination. They conclude that the second part of furrow invagination is not due to myosin activities at the apical or lateral cortices of the mesodermal cells and that actomyosin contractility is required in the early but not the late phase of furrow formation. This part regarding the temporal requirement of Myosin during invagination brings novelty in the field since it has never been tested before.

We thank the reviewer for the comment on the novelty of our work.

They observe that ectodermal cells shorten their apico-basal axis prior to Ttrans, and that compression from the ectoderm is independent of ventral furrow formation since it still occurs even if invagination is inhibited.

They further develop two types of simulations to test theoretically the importance of compressive stress in the invagination process. The theoretical part would need to be further developed and discussed. They would need to integrate all the different components that have been shown to be essential for the invagination (not only apical constriction) and the dynamic aspect of the vertex model has to be clearly explained.

We thank the reviewer for the suggestions on the modeling parts. In the energy-based vertex model (the Polyakov model, original Figure 3), two previously identified mechanisms, apical constriction and basal relaxation, have been implemented in the model to drive lengthening-shortening cell shape change and furrow invagination. Following the reviewer’s suggestions, we have modified the Polyakov model to include additional mechanisms that have been shown to facilitate ventral furrow invagination. In particular, we focused our analysis on the role of lateral myosin in the constricting cells on furrow invagination (Figure 7). Please refer to our response to the combined comments for details (in the section “ Additional modeling analysis to test the known mechanisms for mesoderm invagination”).

As for the dynamic vertex model presented in our original manuscript (original Figure 5), as detailed in our response to Reviewer #1’s comment #5, since the revised manuscript is focused on the bistable characteristics of the mesoderm during gastrulation rather than tissue dynamics during the folding process, we decide to leave this part out of our revised manuscript as suggested by the editor.

Author Response

Reviewer #1 (Public Review):

This thorough study expands our understanding of BMP signaling, a conserved developmental pathway, involved in processes diverse such as body patterning and neurogenesis. The authors applied multiple, state-of-art strategies to the anthozoan Nematostella vectensis in order to first identify the direct BMP signaling targets - bound by the activated pSMAD1/5 protein - and then dissect the role of a novel pSMAD1/5 gradient modulator, zwim4-6. The list of target genes features multiple developmental regulators, many of which are bilaterally expressed, and which are notably shared between Drosophila and Xenopus. The analysis identified in particular zswim4-6 a novel nuclear modulator of the BMP pathway conserved also in vertebrates. A combination of both loss-of-function (injection of antisense morpholino oligonucleotide, CRISPR/Cas9 knockout, expression of dominant negative) and gain-of-function assays, and of transcriptome sequencing identified that zwim acts as a transcriptional repression of BMP signaling. Functional manipulation of zswim5 in zebrafish shows a conserved role in modulating BMP signaling in a vertebrate.

The particular strength of the study lies in the careful and thorough analysis performed. This is solid developmental work, where one clear biological question is progressively dissected, with the most appropriate tools. The functional results are further validated by alternative approaches. Data is clearly presented and methods are detailed. I have a couple of comments.

1) I was intrigued - as the authors - by the fact that the ChiP-Seq did not identify any known BMP ligand bound by pSMAD1/5. Are these genes found in the published ChiP-Seq data of the other species used for the comparative analysis? One hypothesis could be that there is a change in the regulatory interactions and that the initial set-up of the gradient requires indeed a feedback loop, which is then turned off at later gastrula. In this case, immunoprecipitation at early gastrula, prior to the set-up of the pSMAD1/5 gradient, could reveal a different scenario. Alternately, the regulation could be indirect, for example, through RGM, an additional regulator of BMP signaling expressed on the side of lower BMP activity, which is among the targets of the ChiP-Seq. This aspect could be discussed. Additionally, even if this is perhaps outside the scope of this study, I think it would be informative to further assess the effect of ZSWIM manipulation on RGM (and vice versa).

Indeed, BMP genes are direct BMP signaling targets in Drosophila (dpp) (Deignan et al., 2016, https://doi.org/10.1371/journal.pgen.1006164) and frog (bmp2, bmp4, bmp5, bmp7) (Stevens et al., 2021, https://doi.org/10.1242/dev.145789). Of all these ligands, only the dorsally expressed Xenopus bmp2 is repressed by BMP signaling, while another dorsally expressed Xenopus BMP gene admp is not among the direct targets. All other BMP genes listed here are expressed in the pMad/pSMAD1/5/8-positive domain and are activated by BMP signaling.

In Nematostella, we do not find BMP genes among the ChIP-Seq targets, but this is not that surprising considering the dynamics of the bmp2/4, bmp5-8 and chordin expression, as well as the location of the pSMAD1/5-positive cells. In late gastrulae/early planulae, Chordin appears to be shuttling BMP2/4 and BMP5-8 away from their production source and over to the gdf5-like side of the directive axis (Genikhovich et al., 2015; Leclere and Rentsch, 2014). By 4 dpf, chordin expression stops, and BMP2/4 and BMP5-8 start to be both expressed AND signal in the mesenteries. If bmp2/4 and bmp5-8 expression were directly suppressed by pSMAD1/5 (as is the case chordin or rgm expression), this mesenterial expression would not be possible. Therefore, in our opinion, it is most likely that at late gastrula and early planula the regulation of bmp2/4 and bmp5-8 expression by BMP signaling is indirect. We do not have an explanation for why gdf5-like (another BMP gene expressed on the “high pSMAD1/5” side) is not retrieved as a direct BMP target in our ChIP data. Since we do not understand well enough how BMP gene expression is regulated, we do not discuss this at length in the manuscript.

As the Reviewer suggested, we analyzed the effect of ZSWIM4-6 KD on the expression of rgm. Expectedly, since it is expressed on the “low BMP side”, its expression was strongly expanded (Figure 6 - Figure Supplement 4)

2) I do not fully understand the rationale behind the choice of performing the comparative assays in zebrafish: as the conservation was initially identified in Xenopus, I would have expected the experiment to be performed in frog. Furthermore, reading the phylogeny (Figure 4A), it is not obvious to me why ZSWIM5 was chosen for the assay (over the other paralog ZSWIM6). Could the Authors comment on this experiment further?

The comparison was done in zebrafish because we were planning to generate zswim5 mutants, whose analysis is currently in progress. ZSWIM6 is not expressed at the developmental stages we were interested in, while ZSWIM5 was, based on available zebrafish expression data (White et al., 2017):

Reviewer #2 (Public Review):

The authors provide a nice resource of putative direct BMP target genes in Nematostella vectensis by performing ChIP-seq with an anti-pSmad1/5 antibody, while also performing bulk RNA-seq with BMP2/4 or GDF5 knockdown embryos. Genes that exhibit pSmad1/5 binding and have changes in transcription levels after BMP signaling loss were further annotated to identify those with conserved BMP response elements (BREs). Further characterization of one of the direct BMP target genes (zswim4-6) was performed by examining how expression changed following BMP receptor or ligand loss of function, as well as how loss or gain of function of zswim4-6 affected development and BMP signaling. The authors concluded that zswim4-6 modulates BMP signaling activity and likely acts as a pSMAD1/5 dependent co-repressor. However, the mechanism by which zswim4-6 affects the BMP gradient or interacts with pSMAD1/5 to repress target genes is not clear. The authors test the activity of a zswim4-6 homologue in zebrafish (zswim5) by over-expressing mRNA and find that pSMAD1/5/9 labeling is reduced and that embryos have a phenotype suggesting loss of BMP signaling, and conclude that zswim4-6 is a conserved regulator of BMP signaling. This conclusion needs further support to confirm BMP loss of function phenotypes in zswim5 over-expression embryos.

Major comments

1) The BMP direct target comparison was performed between Nematostella, Drosophila, and Xenopus, but not with existing data from zebrafish (Greenfeld 2021, Plos Biol). Given the functional analysis with zebrafish later in the paper it would be nice to see if there are conserved direct target genes in zebrafish, and in particular, is zswim5 (or other zswim genes) are direct targets. Since conservation of zswim4-6 as a direct BMP target between Nematostella and Xenopus seemed to be part of the rationale for further functional analysis, it would also be nice to know if this is a conserved target in zebrafish.

Thank you for the suggestion. In the paper by Greenfeld et al., 2021, zebrafish zswim5 was downregulated approximately 2.4x in the bmp7 mutant at 6 hpf, while zswim6 was barely expressed and not affected at this stage. We added this information to the text of the manuscript. Expression of several other zebrafish zswim genes was also affected in the bmp7 mutant, but these genes do not appear relevant for our study since their corresponding orthologs are not identified as pSMAD1/5 ChIP-Seq targets in Nematostella. Notably, zebrafish zzswim5 is not clearly differentially expressed in BMP or Chd overexpression conditions (See Supplementary file 1 in Rogers et al. 2020). Importantly, in the paper, we wanted to compare ChiP-Seq data with ChIP-Seq data, however, unfortunately, no ChIP-Seq data for pSMAD1/5/8 is currently available for zebrafish, thus precluding comparisons.

Related to this, in the discussion it is mentioned that zswim4/6 is also a direct BMP target in mouse hair follicle cells, but it wasn't obvious from looking at the supplemental data in that paper where this was drawn from.

Please see Supplementary Table 1, second Excel sheet labeled “Mx ChIP_Seq” in Genander et al., 2014, https://doi.org/10.1016/j.stem.2014.09.009. Zswim4 has a single pSMAD1 peak associated with it, Zswim6 has two.

2) The loss of zswim4-6 function via MO injection results in changes to pSmad1/5 staining, including a reduction in intensity in the endoderm and gain of intensity in the ectoderm, while over-expression results in a loss of intensity in the ectoderm and no apparent change in the endoderm. While this is interesting, it is not clear how zswim4-6 is functioning to modify BMP signaling, and how this might explain differential effects in ectoderm vs. endoderm. Is the assumption that the mechanism involves repression of chordin? And if so one could test the double knockdown of zswim4-6 and chordin and look for the rescue of pSad1/5 levels or morphological phenotype.

We do not think that the mechanism of the ZSWIM4-6 action is via repression of Chordin. As loss of chordin leads to the loss of pSMAD1/5 in Nematostella (Genikhovich et al., 2015), the proposed experiment is, unfortunately, not feasible to test this hypothesis. Currently, we see two distinct effects of the modulation of zswim4-6 expression. First, it affects the pSMAD1/5 gradient, possibly by destabilizing nuclear SMAD1/5, as has been proposed by Wang et al., 2022 for the vertebrate Zswim4. This is in line with our results shown on Fig. 6C-F’ and Fig. 6-Figure supplement 3. In our opinion, the reaction of the genes expressed on the “high BMP” side of the directive axis to the overexpression or KD of ZSWIM4-6 (Fig. 6I-K’, 6N-P’) can be explained by these changes in the pSMAD1/5 signaling intensity. Secondly, zswim4-6 appears to promote pSMAD1/5-mediated gene repression. This is in line with the reaction of the genes expressed on the “low BMP” side of the directive axis (Fig. 6G-H’, 6L-M’, Fig. 6-Figure Supplement 4). These genes are repressed by BMP signaling, but they expand their expression upon zswim4-6 KD in spite of the increased pSMAD1/5. Our ChiP experiment (Fig. 6Q) supports this view.

3) Several experiments are done to determine how zswim4-6 expression responds to the loss of function of different BMP ligands and receptors, with the conclusion being that swim4-6 is a BMP2/4 target but not a GDF5 target, with a lot of the discussion dedicated to this as well. However, the authors show a binary response to the loss of BMP2/4 function, where zswim4-6 is expressed normally until pSmad1/5 levels drop low enough, at which point expression is lost. Since the authors also show that GDF5 morphants do not have as strong a reduction in pSmad1/5 levels compared to BMP2/4 morphants, perhaps GDF5 plays a positive but redundant role in swim4-6 expression. To test this possibility the authors could inject suboptimal doses of BMP2/4 MO with GDF5 MO and look for synergy in the loss of zswim4-6 expression.

Thanks for this great suggestion! We performed this experiment (Fig. 5H’’-L) and indeed, a suboptimal dose of BMP2/4MO + GDF5lMO results in a complete radialization of the embryo and abolished zswim4–6, similar to the effect of a high dose of BMP2/4. This result suggests that rather than being a ligand-specific signaling function, GDF5-like signaling alone still provides sufficiently high pSmad1/5 levels to activate zswim4-6 expression to apparent wildtype levels, demonstrating the sensitivity of this gene to even very low amounts of BMP signaling.

4) The zswim4-6 morphant embryos show increased expression of zswim4-6 mRNA, which is said to indicate that zswim4-6 negatively regulates its own expression. However in zebrafish translation blocking MOs can sometimes stabilize target transcripts, causing an artifact that can be mistakenly assumed to be increased transcription (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC7162184/). Some additional controls here would be warranted for making this conclusion.

Thanks for raising this important experimental consideration. To-date, we do not have any evidence for MO-mediated transcript stabilization in Nematostella, and we have not found such data in the literature on models other than zebrafish. mRNA stabilization by the MO also seemed unlikely because we were unable to KD zswim4-6 using several independent shRNAs - an effect we frequently observe with genes, whose activity negatively regulates their own expression. However, to test the possibility that zswim4-6MO binding stabilizes zswim4-6 mRNA, we injected mRNA containing the zswim4-6MO recognition sequence followed by the mCherry coding sequence (zswim4-6MO-mCherrry) with either zswim4-6MO or control MO. We could clearly detect mCherry fluorescence at 1 dpf if control MO was co-injected with the mRNA, but not if zswim4-6MO was coninjected with the mRNA. At 2 dpf (the stage at which we showed upregulation of zswim4-6 upon zswim4-6MO injection on Fig. 6I-I’), zswim4-6MO-mCherrry mRNA was undetectable by in situ hybridization with our standard FITC-labeled mCherry probe independent of whether zswim4-6MO-mCherrry mRNA was co-injected with the control MO or ZSWIM4-6MO, while hybridization with the FITC-labeled FoxA probe worked perfectly.

Author response image 1.

We are currently offering two alternative hypothesis for the observed increase in zswim4-6 levels in the paper rather than stating explicitly that ZSWIM4-6 negatively regulates its own expression: “The KD of zswim4-6 translation resulted in a strong upregulation of zswim4-6 transcription, especially in the ectoderm, suggesting that ZSWIM4-6 might either act as its own transcriptional repressor or that zswim4-6 transcription reacts to the increased ectodermal pSMAD1/5 (Fig. 6I-I’).” Given the sensitivity of zswim4-6 to even the weakest pSMAD1/5 signal (zswim4/6 is expressed upon GDF5-like KD, which drastically reduces pSMAD1/5 signaling intensity (see Fig. 1 and 2 in Genikhovich et al., 2015, http://doi.org/10.1016/j.celrep.2015.02.035 and Fig. 6-Figure supplement 3 of this paper), the latter option (that it reacts to the increased ectodermal pSMAD1/5) is, in our opinion, clearly the more probable one.

5) Zswim4-6 is proposed to be a co-repressor of pSmad1/5 targets based on the occupancy of zswim4-6 at the chordin BRE (which is normally repressed by BMP signaling) and lack of occupancy at the gremlin BRE (normally activated by BMP signaling). This is a promising preliminary result but is based only on the analysis of two genes. Since the authors identified BREs in other direct target genes, examining more genes would better support the model.

We suggest that ZSWIM4-6 may be a co-repressor of pSMAD1/5 targets because it is a nuclear protein (Fig. 4G), whose knockdown results in the expansion of the ectodermal expression of several genes repressed by pSMAD1/5 in spite of the expansion of pSMAD1/5 itself (Fig. 6G-H’, 6L-M’, Fig. 6-Figure Supplement 4). Our limited ChIP analysis supports this idea by showing that ZSWIM4-6 is bound to the pSMAD1/5 site of chordin (repressed by pSMAD1/5) but not on gremlin (activated by pSMAD1/5). We agree that adding the analysis of more targets in order to challenge our hypothesis would be good. However, given technical limitations (having to inject many thousands of eggs with the EF1a::ZSWIM4-6-GFP plasmid in order to get enough nuclei to extract sufficient immunoprecipitated chromatin for qPCR on 3 genes (chordin, gremlin, GAPDH) for each biological replicate, it is currently unfortunately not feasible to test more genes. It will be of great interest for follow up studies to generate a knock-in line with tagged zswim4-6 to analyze target binding on a genome-wide scale. We stress in the discussion that currently the power of our conclusion is low.

6) The rationale for further examination of zswim4-6 function in Nematostella was based in part on it being a conserved direct BMP target in Nematostella and Xenopus. The analysis of zebrafish zswim5 function however does not examine whether zswim5 is a BMP target gene (direct or indirect). BMP inhibition followed by an in situ hybridization for zswim5 would establish whether its expression is activated downstream of BMP.

In the paper by Greenfeld et al., 2021, zebrafish zswim5 was downregulated approximately 2.4x in the bmp7 mutant at 6 hpf. However, this gene was not among the 57 genes, which were considered to be direct BMP targets because their expression was affected by bmp7 mRNA injection into cycloheximide-treated bmp7 mutants (Greenfeld et al., 2021). We added this information to the text of the manuscript.

7) Although there is a reduction in pSmad1/5/9 staining in zebrafish injected with zswim5 mRNA, it is difficult to tell whether the resulting morphological phenotypes closely resemble zebrafish with BMP pathway mutations (such as bmp2b). More analysis is warranted here to determine whether stereotypical BMP loss of function phenotypes are observed, such as dorsalization of the mesoderm and loss of ventral tail fin.

We agree, and we have tuned down all zebrafish arguments. Analyses of zswim5 mutants are currently ongoing.

Author Response

Reviewer #3 (Public Review):

1) Validation of reagents: The authors generated a pY1230 Afadin antibody claiming that (page 6) "this new antibody is specific to tyrosine phosphorylated Afadin, and that pY1230 is targeted for dephosphorylation by PTPRK, in a D2-domain dependent manner". The WB in Fig 1B shows a lot of background, two main bands are visible which both diminish in intensity in ICT WT pervanadate-treated MCF10A cell lysates. The claim that the developed peptide antibody is selective for pY1230 in Afadin would need to be substantiated, for instance by pull down studies analysed by pY-MS to substantiate a claim of antibody specificity for this site. However, for the current study it would be sufficient to demonstrate that pY1230 is indeed the dephosphorylated site. I suggest therefore including a site directed mutant (Y1230F) that would confirm dephosphorylation at this site and the ability of the antibody recognizing the phosphorylation state at this position.

We would like this antibody to be a useful and freely accessible tool in the field and have taken on board the request for additional validation. To this end we have significantly expanded Supplementary Figure 2 (now Figure 1 - figure supplement 2) and included a dedicated section of the results as follows: 1. We have now included information about all of the Afadin antibodies used in this study, since Afadin(BD) appears to be sensitive to phosphorylation (Figure 1 - figure supplement 2A). 2. We have demonstrated that the Afadin pY1230 antibody detects an upregulated band in PTPRK KO MCF10A cells, consistent with our previous tyrosine phosphoproteomics (Figure 1 - figure supplement 2B). This indicates that the antibody can be used to detect endogenous Afadin phosphorylation. 3. We have included two new knock down experiments demonstrating the recognition of Afadin by our antibody (Figure 1 - figure supplement 2C). There appear to be two Afadin isoforms recognised in HEK293T cells by both the BD and pY1230 antibody, consistent with previous reports (Umeda et al. MBoC, 2015). We have highlighted these in the figure. 4. We have performed mutagenesis to demonstrate the specificity of the antibody. We tagged Afadin with a fluorescent protein tag, reasoning that it would cause a shift in molecular weight that could be resolved by SDS PAGE, as is the case. We noted that the phosphopeptide used spans an additional tyrosine, Y1226, which has been detected as phosphorylated (although to a much lower extent than Y1230) on Phosphosite plus. The data clearly show that Afadin cannot be phosphorylated when Y1230 is mutated to a phenylalanine (compared to CIP control), indicating that this is the predominant site recognised by the antibody. In addition, the endogenous pervanadate-stimulated signal is completely abolished by CIP treatment (Figure 1 - figure supplement 2D). 5. We have included densitometric quantification of the dephosphorylation assay shown in Figure 1B, which was part of a time course and shows preferential dephosphorylation by the PTPRK ICD compared to the PTPRK D1. The signal stops declining with time, which could indicate antibody background, or an inaccessible pool of Afadin-pY1230 (Figure 1 - figure supplement 2E). 6. To further demonstrate that this site is modulated by PTPRK in post-confluent cells, we have used doxycycline (dox)-inducible cell lines generated in Fearnley et al, 2019. Upon treatment with 500 ng/ml Dox for 48 hours PTPRK is induced to lower levels than wildtype, however, normalized quantification of the Afadin pY1230 against the Afadin (CST) signal clearly indicates downregulation by PTPRK WT, but not the catalytically inactive mutant (Figure 1 - figure supplement 2F and 2G). Together these data strengthen our assertion that this antibody recognises endogenously phosphorylated Afadin at site Y1230, which is modulated in vitro and in cells by PTPRK phosphatase activity. For clarity, we have highlighted and annotated the relevant bands in figures. We have also included identifiers for each Afadin total antibody was used in particular experiments.

2) The authors claim that a short, 63-residue predicted coiled coil (CC) region, is both necessary and sufficient for binding to the PTPRK-ICD. The region is predicted to have alpha-helical structure and as a consequence, a helical structure has been used in the docking model. Considering that the authors recombinantly expressed this region in bacteria, it would be experimentally simple confirming the alpha-helical structure of the segment by CD or NMR spectroscopy.

To clarify, the helical structure in the docking model was independently predicted by several sequence and structural analysis programmes including AlphaFold2, RobettaFold, NetSurfP and as annotated in Uniprot (as a coiled coil). We did not stipulate prior to the AF2 prediction that it was helical. Isolated short peptides frequently adopt helical structure, therefore prediction of a helix within the context of the full Afadin sequence is, in our opinion, stronger evidence than CD of an isolated fragment.

3) Only two mutants have been introduced into PTPRK-ICD to map the Afadin interaction site. One of the mutations changes a possibly structurally important residues (glycine) into a histidine. Even though this residue is present in PTPRM, it does not exclude that the D2 domain no longer functionally folds. Also the second mutation represents a large change in chemical properties and the other 2 predicted residues have not been investigated.

The residues that were selected for mutation are all localised to the protein surface and therefore are unlikely to be involved in stable folding of PTPRK. In support of the correct folding of the mutated PTPRK, we include in Figure 1 below SEC elution traces for wild-type and mutant D2 showing that they elute as single symmetric peaks at the same elution volume as the WT protein. This is consistent with them having a similar shape and size, and not being aggregated or unfolded.

Figure 1. PTPRK-D2 wild-type and mutant preparative SEC elution profiles. A280nm has been normalised to help illustrate that the different proteins elute at the same volume. The main peak from these samples was used for binding assays in the main paper.

Furthermore, the yield for the double mutant was very high (4 mg of pure protein from a 2 L culture, see A280 value in graph below), whereas poorly folded proteins tend to have significantly reduced yields. This protein was also very stable over time whereas unfolded proteins tend to degrade during or following purification.

Figure 2. Analytical SEC elution profile for the PTPRK-D2 DM construct showing the very high yield consistent with a well-folded, stable protein.

Finally, we have carried out thermal melt curves of the WT and mutant PTPRK D2 domains showing that they all possess melting temperatures between 39.3°C and 41.7°C, supporting that they are all equivalently folded. We include these data as an additional Supplementary Figure (Figure 4 - figure supplement 3) in the paper.

4) The interface on the Afadin substrate has not been investigated apart from deleting the entire CC or a central charge cluster. Based on the docking model the authors must have identified key positions of this interaction that could be mutated to confirm the proposed interaction site.

We have now made and tested several additional mutations within both the Afadin-CC and PTPRK-D2 domains to further validate the AF2 predicted model of the complex.

For Afadin-CC we introduced several single and double mutations along the helix including residues predicted to be in the interface and residues distal from the interface. These mutations and the pulldown with PTPRK are described in the text and are included as additional panels to a modified Figure 3. All mutations have the expected effect on the interaction based on the predicted complex structure. To help illustrate the positions of these mutations we have also included a figure of the interface with the residues highlighted.

For the PTPRK-D2 we have also introduced two new mutations, one buried in the interface (F1225A) and one on the edge of the interface encompassing a loop that is different in PTPRM (labelled the M-loop). GST-Afadin WT protein was bound to GSH beads and tested for their ability to pulldown WT and mutated PTPRK. These new mutations (illustrated in the new Figure 4 – figure supplement 2) further support the model prediction. F1225A almost completely abolishes binding as predicted, while the M-loop retains binding. These mutations and their effects are now described in the main text and the pull-down data, including controls and retesting of the original DM mutant, are included as panel H in a newly modified Figure 4 focussed solely on the PTPRK interface.

5) A minor point is that ITC experiments have not been run long enough to determine the baseline of interaction heats. In addition, as large and polar proteins were used in this experiment, a blank titration would be required to rule out that dilution heats effect the determined affinities.

All control experiments including buffer into buffer, Afadin into buffer and buffer into PTPRK were carried out at the same time as the main binding experiment and are shown below overlaid with the binding curve. These demonstrate the very small dilution heats consistent with excellent buffer matching of the samples.

We were able to obtain excellent fits to the titration curves by fitting 1:1 binding with a calculated linear baseline (see Figure 2B,D). Very similar results were obtained by fitting to the sum (‘composite’) of fitted linear baselines obtained for the three control experiments for each titration.

Author Response:

Reviewer #2 (Public Review):

There is now a considerable body of knowledge about the genetic and cellular mechanisms driving the growth, morphogenesis and differentiation of organs in experimental organisms such as mouse and zebrafish. However, much less is known about the corresponding processes in developing human organ systems. One powerful strategy to achieve this important goal is to use organoids derived from self-renewing, bona fide progenitor cells present in the fetal organ. The Rawlins' lab has pioneered the long-term culture of organoids derived from multipotent epithelial progenitors located in the distal tips of the early human lung. They have shown that clonal cell "lines" can be derived from the organoids and that they capable of not only long-term self-renewal but also limited differentiation in vitro or after grafting under the kidney capsule of mice. Here, they now report a strategy to efficiently test the function of genes in the embryonic human lung, regardless of whether the genes are actively transcribed in the progenitor cells. The strengths of the paper are that the authors describe a number of different protocols (work-flows), based on Crisper/Cas9 and homology directed repair, for making fluorescent reporter alleles (suitable for cell selection) and for inducible over-expression or knockout of specific genes. The so-called "Easytag" protocols and results are carefully described, with controls. The work will be of significant interest to scientists using organoids as models of many human organ systems, not just the lung. The weaknesses are that they authors do not show that their lines can undergo differentiation after genetic manipulation, and therefore do not provide proof of principle that they can determine the function in human lung development of genes known to control mouse lung epithelial differentiation. It would also be of general interest to know whether their methods based on homologous recombination are more accurate (fewer incorrect targeting events or off target effects) than methods recently described for organoid gene targeting using non homologous repair.

We thank Reviewer #2 for capturing the key advances of our toolbox for understanding gene function using a tissue organoid system and the constructive suggestions for the manuscript.

We agree with the Reviewer that it would strengthen the current manuscript if we could differentiate the genetically targeted organoids. Therefore, as a proof of concept, we have successfully differentiated the SOX9 reporter organoids into the alveolar lineage (New figure: Figure 2-figure supplement 1g, shown above). We have also tested the dual SMAD inhibition approach recently reported for basal cell differentiation (Miller et al., 2020). However, this has led to massive cell death even in WT organoids (data not shown). We reason that this might be because our organoids are ~8 pcw, whereas in the literature ~12 pcw organoids were used. We believe that efficient airway differentiation will take a long time to optimise for our organoids and is therefore beyond the scope of this manuscript.

In regard to the Easytag workflow in comparison with the recent CRISPR-HOT method using non-homologous end joining (Artegiani et al., 2020), we consider our approach as a complement to the CRISPR-HOT approach. This can be reflected in the following points: (1) The Organoid Easytag workflow allows precise N-terminal tagging of endogenous genes, exemplified by N-terminal tagging of ACTB. This is not possible using CRISPR-HOT as large pieces of plasmid DNA would disrupt the targeted gene; (2) The Organoid Easytag workflow is based on HDR and the efficient insertion sites for exogenous genes are within a ~30-bp window of the gRNA cleavage sites (Kwart et al., 2017), which gives more flexibility for choosing gRNAs compared with CRISPR-HOT tagging; (3) The Organoid Easytag workflow gives researchers more control of where and how the targeted sites can be modified, and offers a minimal change to the targeted genomic region, whereas CRISPR-HOT introduces large pieces of backbone plasmids, which potentially increases the risk of gene dysregulation. However, HDR requires cells to be at the G2/M phase of the cell cycle, therefore heavily relying on fast cycling cells to gain the most efficient targeting. CRISPR-HOT has the great advantage of not depending on a specific cell cycle stage and therefore being more efficient in slow cycling cells. With this said, we do believe that the efficiency would very much rely on the context, including the cell type used and locus targeted, as a recent report suggested targeting efficiency is influenced also by genomic context (Schep et al., 2021).

In summary, when N-terminal tagging, minimal changes and precise control of targeting is desired, Organoid Easytag is more favourable; whereas when targeting slowly cycling cells, CRISPR-HOT has its strength. Therefore, we consider these two methods as complementary approaches that will both be of benefit to organoid-based research. We have summarised this comparison into a simple table (New table: Figure 2-figure supplement 5f)

Figure 2-figure supplement 5(f). A comparison of Organoid Easytag and CRISPR-HOT methods (Artegiani et al., 2020).

Reviewer #3 (Public Review):

Sun et al have assembled, modified, and applied a series of existing gene editing tools to tissue-derived human fetal lung organoids in a workflow they have termed "Organoid Easytag". Using approaches that have previously been applied in iPSCs and other cell models in some cases including organoids, the authors demonstrate: 1) endogenous loci can be targeted with fluorochromes to generate reporter lines; 2) the same approach can be applied to genes not expressed at baseline in combination with an excisable, constitutively active promoter to simplify identification of targeted clones; 3) that a gene of interest could be knocked-out by replacing the coding sequence with a fluorescent reporter; 4) that knockdown or overexpression can be achieved via inducible CRISPR interference (CRISPRi) or activation (CRISPRa). In the case of CRISPRi, the authors alter existing technology to lessen unwanted leaky expression of dCas9-KRAB. While these tools have previously been applied in other models, their assembly and demonstrated application to tissue-derived organoids here could facilitate their use in tissue-derived organoids by other groups.

Limitations of the study include:

1) is demonstrated application of these technologies to a limited set of gene targets;

2) a lack of detail demonstrating the efficiency and/or kinetics of the approaches demonstrated.

While access to human fetal lung organoids is likely not available to many or most researchers, it is probable that the principles applied here could carry over to other organoid models.

We thank the Reviewer for accurately summarising the details of our manuscript and positive comments on its potential to facilitate tissue-derived organoid related research. We are very grateful for the Reviewer’s detailed and constructive comments to help strengthen our manuscript.

In regard to the limitations pointed out by Reviewer #3, we have systematically tested the kinetics of the inducible CRISPRi knockdown effect and its reversibility using CD71 and SOX2 (New figure: Figure 3-figure supplement 2). At the same time, we have generated SOX9 reporter human foetal intestinal organoids using the Easytag workflow to further demonstrate it can be applied to another organoid system. As suggested by Reviewer #3, we also attempted to implement the inducible CRISPRi system in HBECs. However, due to their sensitivity to lentiviral transduction, infected HBECs died shortly after transduction with gRNA lentivirus. We believe that further optimisation of DNA delivery approach is required for implementation of the inducible CRISPRi/CRISPRa systems in HBECs (perhaps nucleofection and PiggyBac-based vectors).

Author Response:

Reviewer #1:

After infection, new HIV-particles assemble at the host cell plasma membrane in a process that requires the viral protein Gag. Here, Inamdar et al. showed that a component of the host cell, the membrane curvature-inducing protein IRSp53, contributes to efficiently promote the formation of viral particles in synergy with the viral Gag protein.

In cells depleted of IRSp53, the formation of HIV-1 Gag viral-like particles (VLPs) was compromised. The authors showed in compelling electron micrographs that the formation of VLPs was arrested at about half stage of particle budding. Biochemical data (co-IPs and analysis of VLPs and HIV particle content), super-resolution nanoscopy (single molecule localization microscopy) data, and in vitro biophysics measurements (in GUVs), all seem to indicate a functional connection between Gag and the iBAR-domain containing protein IRSp53. The combination of the different techniques and approaches is a clear strength of this manuscript. However, to my opinion, the interpretation of some of the experimental data is somehow limited by the lack of some appropriate controls (that are lacking for different reasons, as the authors state in some parts of the text). These are:

1) Specificity of the IRSp53 siRNA. Although the authors showed that the siRNA used can deplete the expression of the protein (both endogenous and ectopic), they did not presented any rescue experiments of the phenotypes (or corroboration with different siRNA oligoes).

We have tried several different commercial and home-designed siRNA targeting IRSp53 from different companies (providing single siRNA and multiple siRNA mix): we have summarizing all in the Figure R1 (see below). One can see that indeed only 2 siRNA were effective in extinguishing IRSp53 gene: one from Invitrogen on endogenous IRSp53 and ectopic IRSp53-GFP and one from Dharmacon that was only effective on ectopic IRSp53-GFP, as revealed by Western Blot (Fig R1A). Furthermore, the specificity of the siRNA was challenge by testing siRNA IRSp53 on human IRSp53-GFP and on mouse I-BAR-GFP in HEK293T transfected cells and visualized by fluorescence microscopy. Results show in figure R1B that only siIRSp53 is able to extinguished human IRSp53-GFP and not mouse I- BAR-GFP. SiIRTKS and siCtrl are not extinguishing any of these genes. Overall these results confirm the specificity of IRSp53 siRNA-mediated knockdowns.

Figure R1: Specificity of siRNA-mediated knockdowns: (A) Western blots of HEK293T cells lysates probed with anti-IRSp53 antibody (and house-keeping gene GAPDH) showing a series of different siRNA IRSp53 (and siRNA Control, CTRL from Invitrogen, Dharmacon or Sigma) on endogenous and ectopic IRp53 genes in human HEK293T cells and their efficacy in specifically down regulating IRSp53. (B) siRNA IRSp53 from Invitrogen was tested for its specificity in extinguishing human IRSp53-GFP protein expressed in transfected HEK293T cells, but not mouse I-BAR-GFP, and as compare to siRNA control and IRTKS, revealed by fluorescence imaging (GFP).

To further answer the reviewers’ comments, we also perform one rescue experiment of the phenotype as shown in Figure R2 below. We observed that, upon co-transfection of pGag+pIRSp53- GFP+siRNA IRSp53 (lane 2), about 50% of the ectopic IRSp53-GFP was extinguished (since this construct is not siRNA resistant), leaving 50% of this ectopic protein expressed in the cells. In this context, one can observe that Gag-VLP release is ~50% (lane 2), similar to the condition pGag+siCTRL (lane 3). When we compare this to pGag+siIRSp53 (lane 4) which is reduced by 2-3 fold (data from Figure 1b of the manuscript), we can say that the remaining IRSp53-GFP in the Lane 2 seems to rescue the defect caused by extinction of the endogenous IRSp53. In the condition pGag+pIRSp53- GFP +siCTRL, VLP-Gag release was slightly reduced. This is an atypical rescue experiment since we do not have an IRSp53-GFP that is resistant to the siRNA IRSp53 used in this study (Figure R1B), but it suggests that if IRSp53-GFP is overexpressed in the presence of Gag and the siRNA IRSp53, VLP-Gag release is at a normal 50% level in contrast to the absence of IRSp53-GFP (compare lane 2 with lane 4). Unfortunately, due to limited time and by the siRNA IRSp53 out of stock, and the delay in supply, we could only provide one experiment. We thus decided to show it for answering the reviewers but not as part of a figure in the final manuscript.

Figure R2: Rescue of siRNA IRSp53 knock-down with overexpression of IRSp53-GFP: 293T cell were transfected with pGag, pIRSp53 and siRNA control (siCTRL, lane 1) or siRNA IRSp53 (lane 2); cell lysat and VLP wre loaded on SDS-PAGE gels and immunoblots were revealed with anti-GFP (for IRSp53-GFP) and anti-CAp24 (for HIV-1 Gag). One graph on the left shows the percentage of IRSp53-GFP expression upon siRNA IRSp53 cell treatment (lane 2) as compare to the siRNA CTRL (lane 1). The graph on the right shows the resulting gel quantification for the % of Gag-VLP release upon siRNA IRSp53 cell treatment (lane 2) as compare to the siRNA CTRL (lane 1) in the presence of IRSp53-GFP over-expression, or without (lane 3 and 4, as in Figure 1b). N=1 rescue experiment.

2) In the co-IPs (IRSp53 IP + Gag co-IP) there is no assessment of the IRSp53 IP efficiency in the different conditions. The authors argued that IgG signal masking precluded them from doing that.

See the new figure 2. In the new figure 2b, we have assess the IP/co-IP of IRSp53-GFP/Gag efficiency by adding a complete experiment showing that an anti-GFP is able to pull down IRSp53- GFP very efficiently (lanes 2 and 3) and co-IP Gag efficiently (lane 3) accordingly to the input and remaining flowthrough. Using IRSp53-GFP and an anti-GFP antibody, we could bypass the IgG signal masking the endogenous IRSp53 with the IRSp53 antibody’s IP.

3) The authors observed an increase in the membrane-bound pool of IRSp53 when Gag is present (Fig. 2c). It is not clear whether this is specific for IRSp53 or other IBAR proteins can also be more membrane-bound as a result of Gag expression.

See the new figure 2. In the new figure 2d, we have re-loaded all the gel fractions on new SDS- PAGE gels and probed the corresponding immunoblots for Gag, IRSp53, IRTKS, Tsg101 and the cellular markers, Lamp2 (for membrane fractions) and ribosomal S6 protein (for cytosolic fractions). One can see that after quantification of the IRSp53 versus IRTKS bands in the HEK293T cell control and in the Gag expressing cells, only IRSp53 is increasing at the cell membranes upon Gag expression and not IRTKS.

Reviewer #3:

Inamdar et al. used biochemical and microscopy assays to investigate the role of I-BAR domain host proteins on HIV-1 assembly and release from HEK 293T and Jurkat cells. They show that siRNA knockdown of IRSp53, but not a similar I-BAR domain protein IRTKS, inhibits HIV-1 particle release from 293T cells after transfection of the HIV-1 provirus or HIV-1 Gag in cells. The authors then show that HIV-1 Gag associates with IRSp53 in the host cell membrane and cytoplasm, using biochemical assays and super resolution microscopy. In addition, IRSp53 is incorporated into HIV-1 particles along with other previously identified host proteins. Then using in vitro-derived membrane vesicles ("giant unilamellar vesicles" or GUVs), the authors indicate that HIV-1 Gag can associate with IRSp53, particularly on highly curved structures.

The conclusions are largely supported data, with the virology and biochemical results being particularly strong, but the mechanistic studies in GUVs appear somewhat preliminary and are not entirely clear. The GUV experiments would benefit from better quantification of measurements and manipulation to simulate actual cellular scenarios. In addition, while it is appreciated that the HEK 293T cell line is convenient for biochemical and imaging studies, they are not biologically relevant HIV-1 target cells. While the authors present examples of reproducibility of their results in a CD4+ T cell line, these data are buried in the supplemental figures, whilst it would have been better to highlight them and perhaps include primary CD4+ T cells.

1) Immortalized cell lines do not always recapitulate primary cells. It is unclear what the role of IRSp53 is in the membrane curvature of CD4+ T cells and whether expression levels and localization are consistent with Jurkat T cells.

Please consider the general responses to the Editors, which is:

We have published that IRSp53 (using siRNA) is involved in HIV-1 particle release on primary T cells (PBMC derived T cells) in Thomas et al, JVI 2015, so high probability is that it would be the same in different cell type, transfected HEK293T cells, transfected or infected Jurkat T cells and infected primary T cells. But we have not done the extensive super-resolution microscopy on infected primary T cells because this would require time overconsuming study. We are currently proceeding in setting up condition with an infectious HIV-1 virus carrying mEOS2 photoactivable protein for being able to infect primary T cells and go on for further research using infectious relevant system and super- resolution microscopy, but it is not ready for this current manuscript as it would require months of extra work and experiments.

Although, we agree with the reviewer #3 that the localization of Gag in Jurkat T cells and in primary CD4 Tc cells is different at the cell level (in primary T cells HIV-1 Gag is more polarized at uropods, as referred in the literature – see for an example Bedi et al/Ono’s Lab), but at the nanoscopic level of the budding sites, chances are that it would be similar but it need to be checked in future studies.

2) Description of some of the microscopy measurements could be improved. In lines 204-206 of the text and Figure S5, it is unclear how the localization of precision was determined to be approximately 16 nm for PALM-STORM.

These lines have been changed in the main text as they were not mandatory to understand how we determine the size of the VLP clusters. However, we have now detailed in figure S5 how we measure localisation precision.

The following text has been added to the legend of the figS5:

“Distribution of localisation precisions for PALM (in green) or STORM (in red) as given by Thunderstorm analysis in Fiji : Localisation precision distribution exhibit maxima at 16 nm and a mean±sd value of 20±5 nm for PALM, and a maxima of 26 nm, corresponding to a mean±sd value of 27±10 nm for STORM. The localization precision is obtained by eq 17 of (Thompson et al., 2002).”

As well as the reference of the original paper (Thompson et al. 2002, Biophysical Journal).

In Figure 4b, it is understood from the text (lines 252-256) that the red bars denote the Mander's coefficient for colocalization of the GFP-tagged proteins with Gag-mCherry (presumably the average of multiple experiments with standard deviations or errors of the mean, although this is not stated in the figure legend), it is unclear what the green bars are showing.

Yes, the red bars denote the Mander's coefficient for colocalization of the Gag-mCherry with the GFP-proteins, and the green bar denote for colocalization of the GFP-tagged proteins with Gag- mCherry, showing for more than 300 green and red vesicles, thant indeed all the Gag-VLP are green in the case of IRSp53-GFP (red bar) but that not all the GFP-IRSp53-GFP “green” vesicles are (+) for Gag: this indicates that vesicles produced by transfected HEK cells produced GAG/IRSp53 VLP but also IRSp53-GFP vesicles. Thanks to the reviewer to point this out. We added the explanation in the main text (page 12, lanes 272-282) and in the figure legend of Figure 4b.

Also, the histograms for IRSp53 and IRTKS colocalized with Gag look similar in Figure S10, suggesting that they are not different in Jurkat cells, but this is not addressed.

Yes. We have now addressed this particular point in the global response to the reviewers. Indeed, the figure 3 and 4 were remodelled into new figure 3 showing, in the same figure, HEK and Jurkat cells results and in figure 4 the simulations results. Overall, the PALM/STORM microscopy analysis results on Gag/IRSp53 colocalization are very similar in both cell types.

3) GUVs are first referenced on page 7 after description of Figure 2, the significance of which is confusing to the reader. However, the actual experimental data are described on pages 12-13 and Figures 5 and S11. A better description of these structures would be warranted for an audience that is unfamiliar with them. In addition, the biologic concentrations of I-BAR proteins at cell membranes are not provided and it is unclear what conditions used in Figures 5 and S11 represent a "normal CD4+ T cell" situation. It appears that the advantage of this in vitro system is that different factors can be provided or removed to simulate different cellular scenarios. For example, relatively low IRSp53 concentrations may simulate siRNA knockdown experiments in Figure 1, which could recapitulate those results that less viral particles are released from the membrane. In addition, the authors state that HIV-1 Gag preferentially colocalizes with IRSp53 as the tips of the GUV tubular structures (Figure 5b,c), but this is not actually shown or quantified. Similar quantification as shown in Figure 1e could be performed to strengthen this argument.

We thank the review for pointing this out. We now described all the GUV result in section 5.

Considering the biological concentrations of I-BAR proteins in cells, to the best of our knowledge, there is no measurement of it. We thus could not relate concentrations used in the GUV experiments with those in cells.

We could not perform quantification as in Figure 1e because the majority of the tubes in GUVs were moving too rapidly, preventing us from acquiring images with higher spatial resolution (see Fig. S11, and Movie 2 and 3). However, we would like to point out that the Gag signals appeared dotty inside GUVs (see Fig. S11, and Movie 2 and 3), which is very different from the signals of I-BAR that are clearly along the tubes (see Fig. S10c). Moreover, for tubes that were not moving too fast, we found that for all the tubes (17 tubes), Gag signals are exclusively located at the tips of the tubes (see new Fig. 6d). Also, the sorting maps shown in Fig. 6c and Fig. S10 d indicate the relative accumulations of Gag at the tips of the tubes. To make it clearer that the Gag signals were located at the tips of the tubes, in the current manuscript, we have added the new Fig. S11, Movie 1, 2 and 3, and included zoom-in images in Fig. 6b, 6c and a new Fig. 6d. Also, we have included the quantitation results (17 tubes) in the manuscript.

Author Response:

Reviewer #1 (Public Review):

The lateral entorhinal cortex (LEC) receives direct inputs from the olfactory bulb (OB) but their odor response properties have not been well characterized despite a recent increase in interests in the role of LEC in olfactory behaviors. In this study, Bitzenhofer and colleagues provide unprecedented details of odor response properties of layer 2 cells in LEC. The authors first show that LEC neurons respond to odors with a rapid burst of activity time-locked to inhalation onset, similarly to the piriform cortex (PCx), but distinct from the OB. Firing rates of LEC ensembles conveyed information about odor identify whereas timing of spikes odor intensity. The authors then examined the difference between two major cell types in LEC layer 2 - fan cells and pyramidal neurons, and found that, on average, fan cells responded earlier than pyramidal neurons, and pyramidal neurons, but not fan cells, changed their peak timing in response to changes in concentrations, providing a basis for temporal coding of odor concentrations. Additionally, the authors show that inactivation of LEC impairs odor discrimination based on either identify or intensity, and demonstrate different cellular properties of fan cells and pyramidal neurons. Finally, the authors also examined the odor response properties of hippocampal CA1 neurons, and showed that odor identify can be decoded by firing rate responses, while decoding of odor concentration depended on spike timing.

The authors performed a large amount of experiments, and provide an impressive set of data regarding odor response properties of LEC layer 2 neurons in a cell type specific manner. The results reported are very interesting, and will be a point of reference for future studies on odor coding and processing in the LEC. The manuscript is clearly written, and data are well analyzed and presented clearly. I have only relatively minor concerns or suggestions.

1. The authors infer the time at which "mice could discriminate odors" from the time at which d-prime becomes significantly different between baseline and odor stimulation conditions (line 111 and line 121). However, the statistical test applied to these data does not guarantee that an observer can accurately discriminate odors. For example, a small p-value can be obtained even when discrimination accuracy is only slightly above chance if there are many trials. The statement such as "mice could discriminate two odors by as early as 225 ms after inhalation onset" (line 111) can be misleading because this might sound as if mice can accurately discriminate odors at this timepoint, while this is not necessarily the case (as indicated by the d-prime value).

We have added plots of performance accuracy over time under control conditions (LED off) to Figure 2-supplement 1. These plots of fraction of correct responses (binned every 50 ms) show that mice (n = 6) are making choices significantly different from chance within 200 ms of odor inhalation. We changed the wording in the Results to now say: “Moreover, by analyzing lick timing, we determined that the discriminability measure d’ became significantly different under control conditions as early as 225 ms after inhalation onset and performance accuracy increased within 200 ms of inhalation (Fig. 2b, Figure 2-supplement 1).”

1. Optogenetic identification can be a little tricky when identifying excitatory neurons as in this study. Please discuss some rational or difficulty regarding how to distinguish those that are activated directly by light from those activated indirectly (i.e. synaptically). Do the results hold if the authors use only those that the authors are more confident about identification?

We only used the cells that were confidently identified using a combination of two criteria. First, tagged cells had to show a significant increase in firing (p_Rate <0.01) during the 5 ms LED illumination period versus 100 randomly selected time windows before LED stimulation. Cells also had to respond with a fixed latency to reduce the chance of including cells recruited by polysynaptic excitation. Further, we used the stimulus associated spike latency test (SALT) as detailed in Kvitsiani et al., 2013. To be judged as tagged, units had to show significantly less spike jitter during the 5 ms LED illumination than 100 randomly selected time windows before LED stimulation (p_SALT<0.01). Only those cells with BOTH p_Rate<0.01 and p_Salt<0.01 were considered as tagged (both methods typically agreed for most cells). Moreover, slice work testing synaptic connections between LEC layer 2 cells found extremely low levels of connectivity between fan and pyramidal cells Nilssen et al., J. Neuroscience, 2018. This makes it unlikely that LED-induced firing of fan or pyramidal cells would recruit indirectly (synaptically) excited cells.

1. The authors sort odor response profiles by peak timing, and indicate that odor responses peak at different timing that tiles respiration cycles. However, this analysis does not indicate the reliability of peak timing. Sorting random activity by "peak timing" could generate similar figure. One way to show the reliability or significance of peaks is to cross-validate. For instance, one can use a half of the trials to sort, and plot the rest of the trials. If the peak timing is reliable, the original pattern will be replicated by the other half, and those neurons that are not reliable will lose their peaks. Please use such a method so that we can evaluate the reliability of peaks.

We analyzed the data as suggested by this reviewer as shown below (Author response image 1). Plotting only the odd trials sorted by the odd trials in the dataset (top) looked identical to the data from all trails used in Figure 1g. More importantly, plotting only the even trials sorted by the odd trials (bottom), though noisier due to trial-by-trial variation, showed the same general structure of tiling throughout the respiration cycle for OB cells.

Author response image 1

Reviewer #2 (Public Review):

In this study, Bitzenhofer et al recorded odor-evoked activity in the LEC and examined the coding of odor identity and intensity using extracellular recordings in head-fixed mice, and used the standard suite of quantitative tools to interpret these data (decoding analyses, dimensionality reduction, etc). In addition, they performed behavioral experiments to show the necessity of LEC in odor identity and intensity discrimination, and deploy some elegant and straightforward 'circuit-busting' slice physiology experiments to characterize this circuit. Importantly, they performed some of their experiments in Ntng1-cre and Calb-cre mice, which allowed them to differentiate between the two major classes of LEC principal neurons, fan cells and pyramidal cells, respectively. Many of their results are contrasted with what has previously been observed in the piriform cortex (PCx), where odor coding has been studied much more extensively.

Their major conclusions are:

Cells in the LEC respond rapidly to odor stimuli. Within the first 300 ms after inhalation, odor identity is encoded by the ensemble of active neurons, while odor intensity (more specifically, responses to different concentrations) is encoded by the timing of the LEC response; specifically, the synchrony of the response. These coding strategies have been described in the PCx by Bolding & Franks. Bolding also found two populations of responses to different concentrations: one population of responses was rapid and barely changed with concentration and the second population of responses had onset latencies that decreased with increasing concentration. Roland et al also found two populations of responses using calcium imaging in anesthetized mice: one population of responses was concentration-dependent and another population was 'concentration-invariant'. However, neither Bolding nor Roland were able to determine whether these populations of responses emerged from distinct populations of cells. Here, the authors elegantly register these two response types in LEC to different cell types: fan cells respond early and stably, and pyramidal cells response latencies decrease with concentration. This is a novel and important finding. They also showed that, unlike PCx or LEC where concentration primarily affects timing rather than rate/number, odor concentration in CA1 is only reflected in the timing of responses.

Using optogenetic suppression of LEC in a 2AFC task, the authors purport to show that LEC is required for both the discrimination of odor identity and odor intensity. If true, this is an important result, but see below.

In slice experiments, the authors characterize the differential connectivity of fan and pyramidal cells to direct olfactory bulb input, input from PCx, and inhibitory inputs from SOM and PV cells. This work is elegant, novel, and important, although it is a little out of place in this manuscript. As such, their findings are irrelevant/orthogonal to the rest of the results in this study. But fine.

The simultaneous recordings from three different stations along the olfactory pathway are impressive.

Major concern

My major concern with this manuscript regards the behavioral experiments. The authors show that blue light over the LEC in GAD2-Cre/Ai32 mice completely abolishes (i.e. to chance) the mouse's ability to perform a 2AFC task discriminating between either two different odorants or one odorant at different concentrations. Their interpretation is that LEC is required for rapid odor-driven behavior. The sensory component of the task is so easy, and the effect is so striking that I find this result surprising and almost too good to be true. The authors do control for a blue-light distraction effect by repeating the experiments in mice that don't express ChR2, but do not control for the effect of rapidly shutting down a large part of the sensory/limbic system. If they did this experiment in the bulb I would be impressed with how clean the result was but not conceptually surprised by the outcome. I think a different negative control is needed here to convince me that the LEC is necessary for this simple sensory discrimination task. For example, the authors could activate all the interneurons (i.e. use this protocol) in another part of the brain, ideally in the olfactory pathway not immediately upstream of the LEC, and show that the behavior is not affected.

This reviewer suggests a negative control experiment for the effects we observe on behavior when optogenetically silencing LEC. However, we disagree that it would be informative to silence other olfactory pathways in search of those that do not affect behavior. Our strong effects on behavior are also in complete agreement with recent findings that muscimol inactivation of LEC abolishes discrimination of learned odor associations (Extended Data Figure 8, Lee et. al., Nature, 2021).

More specifically, both the presentation and the interpretation of the data are confusing. First, there is a lack of detail about the behavioral task. I was not sure exactly when the light comes on and goes off, when the cue was presented, and when the reward was presented. In the manuscript they say (line 108) "…used to suppress activity during odor delivery on a random subset…". There is nothing more about this in the figure legend or Methods. The only clue to this is the dotted line in the 'LED On' example at the bottom of Fig. 2a. The authors also say that (line 660) "Trials were initiated with a 50 ms tone." When exactly was the tone presented? In the absence of any other information, I assume it was presented at odor onset. When was the reward presented? Lines 106-7 say "Mice were free to report their choice (left or right lick) at any time within 2 s of odor onset." Presumably this means the reward was presented to one of the ports for 2 seconds, starting at odor onset.

The LED is applied during odor delivery, the 50 ms tone immediately precedes odor delivery, and water reward is dispensed after the first lick at the correct lick port during the choice period. The choice period begins with the odor onset and odor delivery is terminated by the first lick at either the correct or incorrect port. If there is no lick at either port, odor delivery lasts 1s and is followed by an extended choice period (terminated by correct or incorrect lick) lasting 1s. To clarify the behavior protocol, we have included a schematic of the trial structure in Figure 2-supplement 1.

These details matter because the authors want to claim that "LEC is essential for rapid odor-driven behavior." The data presented in support of this claim are (1) that mice perform this task at chance levels in LED On trials, presumably based on which port the mouse licked first (this is the 'essential' part), and (2) that in control in LED Off trials, d' becomes statistically different from baseline after ~200 ms (this is the 'rapid' part).

To further support the argument that LEC is required for rapid odor-driven behavior, we now show a plot of % correct responses over time from first odor inhalation.

On first reading, these suggested that shutting off LEC makes odor discrimination worse and/or slower. However, the supplementary data clarifies several things. First, the mice never Miss (Fig.2S.2a & c), meaning then they always lick. Second, in LED Off trials (F2S2 & e), the mice make few mistakes, and these only occur immediately after inhalation, presumably meaning the mice occasionally guess, possibly in response to the auditory cue. Thus, the mean time to lick is much shorter for Error trials than Correct trials. To state the obvious, the mice often wait >300 ms before they lick, and when they do wait, they never make mistakes. Now, in the LED On trials, the mice almost always lick within the first 300 ms and perform at chance levels, with the distribution of lick times for Correct and Error trials almost overlapping. In fact, although the authors claim LEC is required for rapid odor discrimination, the mean time to lick on Correct trials appears to decrease in LED On trials. This makes me think that the mice are making ballistic guesses in response to the tone in LED On cases, which doesn't necessarily implicate a dependence on LEC for odor discrimination.

We do not believe that mice are making ballistic guesses in response to the tone for LED on trials. First, although a 50 ms tone immediately precedes odor delivery, all data in Figure 2-supplement 1 shows lick times aligned to the first inhalation of odor. Thus, time 0 ms is not the tone or subsequent odor onset but rather a variable time point coinciding with the first odor inhalation (the delay from odor onset to first inhalation is ~300 ms, the average respiration interval under our conditions). In fact, we excluded trials if mice made premature licks between the time of odor onset and first odor inhalation. We re-analyzed these trials to test the reviewer’s idea that mice were more likely to make fast ballistic guesses when the LEC was silenced. However, we saw no evidence that mice made more premature licks in trials with LED on (Author response image 2).

Author response image 2

The authors' interpretation of their data would be more solid if, for example, there were a delay between the auditory cue and odor delivery and/or if the reward was only available with some delay after the odor offset. Here, however, it seems just as likely as not that the mice are making ballistic guesses in response to the tone in LED On cases, which doesn't necessarily involve dependence on LEC for odor discrimination. Here, the divergence of d' from baseline in the control (i.e LED Off) condition seems mostly because mice take longer to correctly discriminate under control conditions. While this is not formally contradictory to LEC is essential for rapid odor-driven behavior", it is nevertheless a bit contrived and misleading. An interesting (thought) experiment is what would happen if the authors presented a tone but no odor. I would guess that the mice would continue licking randomly in Light On trials.

While a delay between odor delivery and reward would have been useful for some aspects of interpreting the behavior, we would have lost the ability to examine the role of LEC in response timing. To address this reviewer’s concern, we have added a section to the Discussion mentioning caveats related to the interpretation of experiments using acute optogenetic silencing to understand behavior.

Author Response

Reviewer #1 (Public Review):

We thank the reviewer for carefully reading of the manuscript and for the insightful criticisms and comments. In the following we address them point by point.

The community assembly process is modelled in a very specific way, and the manuscript would benefit from an expanded ecological motivation of the processes that are being mimicked, and thereby explain more clearly what taxonomic level of organization is being considered.

We follow the more recent trait-based approach that shifts the focus from species (and the many traits by which they differ from one another) to groups of species that share the same values of selected functional traits. Since the general context is ecosystem response to drier climates, we choose the functional traits to include a response trait associated with stress tolerance and an effect trait associated with biomass production. We further assume a tradeoff between the two traits which is well supported by earlier studies (see e.g. Angert et al. 2009, https://doi.org/10.1073/pnas.0904512106). So, indeed, the choice we make in characterizing the community is quite specific, but it is highly relevant to the ecological context considered of dryland plant communities where plants compete primarily for water and light. The taxonomic level we consider is species except that we group them in a manner that is more transparent to questions of ecosystem function, ignoring differences between species that are not significant to these questions.

We expanded considerably the text in the section “Modeling spatial assembly of dryland plant communities” to clarify the ecological motivation of the processes we model.

In addition, it would be useful if the authors could provide further clarification as to what extent the community diversity dynamics can be separated from total biomass dynamics of patterned water-limited ecosystems given the current approach. These points are explained in further detail below.

The model describes the dynamics of all functional groups, which provides the biomass distribution 𝐵 = 𝐵(𝜒) in trait space (in the case of patterned states we first integrate over space). That distribution contains information about various community-level properties, including functional diversity (richness, evenness) as figure 3 in the revised manuscript illustrates, and total biomass, which is the area below the distribution curve. The two types of dynamics are tightly connected and cannot be separated, but in principle the approach can be used to study the relationships between diversity and total biomass by calculating biomass distributions along the rainfall gradient and extracting the two properties from the distributions.

We added in the section “Modeling spatial assembly of dryland plant communities” the information that the biomass distribution also contains information about the total biomass.

First, it was not entirely clear to this reviewer how the reaction parts of the model equations determine the optimal trait value χ, and how this value varies as a function of precipitation.

The ‘optimal’ trait value 𝜒𝑚𝑎𝑥 is determined by the interspecific interactions that the model captures, which divide into ‘direct’ and ‘indirect’ interactions. The direct interactions are captured by the dependence of the growth rate Λ𝑖 of the ith functional group (see Eq. (1a)) on the aboveground biomass values of all functional groups, Λ𝑖 = Λ𝑖(𝐵1,𝐵2,… , 𝐵𝑁) (see Eq. (2)). This dependence represents competition for light (taller plants are better competitors) and includes the effect of self-shading. The indirect interactions are through the water uptake term in the soil-water equation (1b) (2nd term from right) and the water dependence of the biomass growth term in Eq. (1a). These terms represent competition for water. For a given precipitation value 𝑃 the net effect of these interspecific interactions result in a particular functional group 𝜒𝑚𝑎𝑥 which is most abundant. For spatially uniform vegetation, as 𝑃 is increased 𝜒𝑚𝑎𝑥 moves to lower values. The precipitation increases surface water (Eq. (1c)) and consequently the amount of water 𝐼𝐻 infiltrating into the soil. The increased soil water gives competitive advantage to species investing in growth, mainly because they better compete for light as they grow taller, and therefore 𝜒𝑚𝑎𝑥 decreases.

… it is then not immediately clear why the most successful trait class is not outcompeting the other classes.

With the current model and parameters set the most successful trait does eventually outcompete all other traits, when trait diffusion is set to zero, 𝐷𝜒 = 0. This is, however, a very long process because the most successful trait suffers from self-shading at late growth stages, which slows down its growth and allows nearby traits to survive for a long time. Choosing a finite but very small 𝐷𝜒 values that represent mutations occurring on evolutionarily long times counteracts the exclusion process and results in a stationary asymptotic community, as Fig. 3 in the revised manuscript shows (this behavior is reminiscent of optical solitons, where self-focusing instability is balanced by dispersion). We note that modeling stronger growth-inhibiting factors, such as pathogens, by including a factor of the form (1 − 𝐵𝑖/𝐾) to the growth rate, results in an asymptotic stationary community also for 𝐷𝜒 = 0 (see also earlier studies Nathan et al. 2016, Yizhaq et al. 2020).

We revised original Fig. 4 (now Fig. 3) by adding a new part (Fig. 3a) that shows the exclusion process for 𝐷𝜒 = 0, and the effect of the counter-acting process of trait diffusion, which results in an asymptotic distribution of finite width (Fig. 3b) from which community level properties such as functional diversity can be derived. We also extended the text in section “Modeling spatial assembly of dryland plant communities” (last paragraph) to clarify the two counter-acting processes of exclusion because of interspecific competition for water and light, and trait diffusion driven by mutations, which together culminate in an asymptotic biomass distribution along the 𝜒 axis of finite width.

The authors model trait adaptation through a diffusion approximation between trait classes. That is, every timestep, a small amount of biomass flows from the class with higher biomass to the neighboring trait class with lower biomass. From an ecological point of view, it seems that this process is describing adaptation of vegetation that is already present, so this process seems to be limited to intraspecific phenotypic plasticity. From the text, however, it seems that the trait classes correspond to higher taxonomic levels of organization, when describing shifts from fast growing to stress-tolerant species, for example. It is not entirely clear, however, how biomass flows as assumed in the model could occur at these higher levels of organization.

We do not study in this work adaptation through diffusion in trait space. That kind of adaptive dynamics can indeed be studied with the current model, but with different initial conditions, namely, initial conditions corresponding to a single resident trait where the biomass of all other traits is zero. The resulting dynamics of mutations and succession are then very slow, occurring on evolutionarily long time scales set by the small value of 𝐷𝜒 (e.g. 10−6). In this study the initial conditions represent the presence of all traits, even if at very low biomass values that may represent a pool of seeds that germinate once environmental conditions allow. For a given precipitation value 𝑃, the functional traits we consider determine which functional groups (of species) overcome environmental filtering and grow, and which of the growing traits survive the competition for water and light. These are relatively fast processes, occurring on ecological time scales, which determine the emerging community. At longer times this community is further shaped by slow processes of interspecific competition among species of similar traits and by trait diffusion (mutations). A final remark about phenotypic changes: although in general 𝜒 can be interpreted as representing different phenotypes, the choice of very small values for 𝐷𝜒 cannot represent relatively fast phenotypic changes and restricts the context to mutations at the taxonomic level of species.

We added an explanation in the 3rd paragraph of the section “Modeling spatial assembly of dryland plant communities” of the need to consider mutations and the role they play in our study.

Combining the observations from the previous two points, there is a concern that for a given level of precipitation, there is a single trait class with optimal biomass/lowest soil water level that is dominant, with the neighboring trait classes being sustained by the diffusion of biomass from the optimal class to neighboring inferior classes. This would seem a bit problematic, as it would mean that most classes are not a true fit for the environment, and only persist due to the continuous inflow of biomass. Taking a clue from the previous papers of the authors, it seems this may not be the case, though. Specifically, in the paper by Nathan et al. (2016) it seems that all trait classes are started at low initial biomass density, and the resulting steady state (in the absence of biomass flows between classes) seems to show similar biomass profiles as shown in Figs. 4,5 and 7 of the current paper. While the current model formulation seems slightly different, similar results may apply here. Indeed, keeping all trait classes at non-zero (but low) density, and when the (abiotic and biotic) environment permits, let each class increase in biomass seems like the most straightforward approach to model community assembly dynamics. Given the above discussion about these trait classes competing for a single resource (soil water), and one trait class being able to drive this resource availability to the lowest level, it would then be useful to readers to explain why multiple trait classes can coexist here, and how(for spatial uniform solutions) the equilibrium soil water level with multiple trait classes present compares to the equilibrium soil water level when only the optimal trait class is present. Furthermore, if results as presented in Nathan et al. (2016) indeed hold in the current case, perhaps it means that the biomass profile responses as shown in e.g. Fig. 5 would also occur if there was no biomass flow between trait classes included, but that the time needed to adjust the profile would take much longer as compared to when the drift term/second trait derivative is included. In summary, further clarification of what the biomass flows between classes represent, and the role it plays in driving the presented results would be useful for readers.

As explained in the reply to previous comments the asymptotic community is tuned by a balance between two slow counter-acting processes, interspecific competition among similar traits and mutations over evolutionarily long time scales. However, the community structure is largely determined by much faster processes of environmental filtering and interspecific competition among widely distinct traits, as all traits are initially present. Indeed, comparing the biomass distributions in new Fig. 3, with and without trait diffusion indicates that the community composition, as measured by 𝜒𝑚𝑎𝑥, is the same. Trait diffusion, however, does affect functional diversity, along with environmental factors. In that sense the emerging community is a true fit for the environment.

We thank the reviewer for these thoughtful comments, which helped us realize that our presentation of these issues was too concise and unclear. We believe that the new extended section on modeling spatial assembly of dryland plant communities, and the new figure 3a clarify these issues.

In addition, it would be useful for readers to understand to what extent the shifts in average trait values and functional diversity can be decoupled from the biomass and soil water responses to changes in precipitation that would occur in a model with only a single biomass variable. For example, early studies on self-organization in semi-arid ecosystems already showed that the shift toward a patterned state involved the formation of patches with higher biomass, and higher soil water availability, as compared to the preceding spatially uniform state, and that the biomass in these patches remains relatively stable under decreasing rainfall, while their geometry changes (e.g. Rietkerket al. 2002). It has also been observed that for a given environmental condition, biomass in vegetation patches tends to increase with pattern wavelength (e.g. Bastiaansen and Doelman 2018; Bastiaansen et al. 2018). Given the model formulation, one wonders whether higher biomass in the single variable model is not automatically corresponding to higher abundance of faster growing species and a higher functional diversity (as the diffusion of biomass can cover a broader range when starting from higher mass in the optimal trait class). There are some indications in the current work that the linkage is more complicated, for example, the biomass peak in Fig. 7c is lower, but also broader as compared to the distribution of Fig. 7b, but it is currently not entirely clear how this result can be explained (for example, it might be the case that in the spatially patterned states, the biomass profiles also vary in space).

We are not sure we understand what the reviewer means by “decoupled”, but much insight indeed can be gained from a study of a model for a single functional group (trait) and observing the behaviors described by the reviewer. In fact, these behaviors, which some of us are familiar with from numerical studies, motivated parts of the current study. Higher biomass in vegetation patches (compared to uniform vegetation) in the single trait model does not automatically imply a shift to faster growing species; in principle the stress-tolerant species that already reside in the system when uniform vegetation destabilizes to a periodic pattern can simply grow denser. To answer this and additional questions we need to take into account interspecific interactions by studying the full community model. As to Fig. 7b,c, the behavior appears to be opposite to that described by the reviewer: the biomass pick in Fig. 7c is higher and narrower than that in Fig. 7b, not lower and broader. This is because of the much larger domain of the patterned state as compared with that of the uniform state, which increases the abundance of low-𝜒 species, i.e. species investing in growth.

The increase of biomass in vegetation patches with pattern wavelength for given environmental conditions, as observed by Bastiaansen et al. 2018, is actually another mechanism for increasing functional diversity. This is because the water stress at the patch center is higher than that in the outer patch areas and thus forms favorable conditions for stress tolerant species while the outer areas form favorable conditions for fast growing species.

We added a new paragraph in the Discussion and Conclusion section (last paragraph in the subsection Insight III) where we discuss the effect of coexisting periodic patterns of different wavelengths on functional diversity and ecosystem management. We also added citations to the references the reviewer mentioned.

The possibility of hybrid states, where part of the landscape is in a spatially uniform state, while the other part of the landscape is in a patterned state, is quite interesting. To better understand how such states could be leveraged in management strategies, it would be useful if a bit more information could be provided on how these hybrid states emerge, and whether one can anticipate whether a perturbation will grow until a fully patterned state, or whether the expansion will halt at some point, yielding the hybrid state. It seems that being able to distinguish this case would be necessary in the design of planning and management strategies

The hybrid states appear in the bistability range of the uniform and patterned vegetation states, and typically occupy most of this range. Their appearance is related to the behavior of ‘front pinning’ in bistability ranges of uniform and patterned states in general. Front pinning refers to fronts that separate a uniform domain and a periodic-pattern domain, which remain stationary in a range of a control parameter (precipitation in our case). This is unlike fronts that separate two uniform states, which always propagate in one direction or another and can be stationary only at a single parameter value – the Maxwell point. Thus, an indication that a given landscape may have the whole multitude of hybrid states is the presence of a front (ecotones) that separates uniform and patterned vegetation. If that front appears stationary over long period of times (on average), this is a strong indication.

We added a new paragraph in the subsection Insight III of the Discussion and conclusion section to clarify this point.

Also, in Fig. 3a, the region of parameter space in which hybrid states occur is not very large; it is not entirely clear whether the full range of hybrid states is left out here for visual considerations, or whether these states only occur within this narrow range in the vicinity of the Turing instability point.

As pointed out in the reply to the previous comment the hybrid states are limited to the bistability range of uniform and patterned vegetation, which is not wide. However, this should not necessarily restrictma nagement of ecosystem services by nonuniform biomass removal, as such management will have similar effects on community structure also outside the bistability range where front propagate slowly.

The new paragraph we added also addresses this point.

Reviewer #2 (Public Review):

We thank the reviewer for carefully reading the manuscript and for the constructive criticisms and comments. In the following we address them point by point.

1) Model presentation.

It would be better to explain the model in ecological terms first, clarifying parameter biological meaning and justifying their choice. In doing so, creating a specific 'Methods' section, which now is lacking, would be of help too. Authors should clarify whether and how the model follows the conservation of mass principle involving precipitation and evapotranspiration. Are root growth and seed dispersal included for this purpose? Why they are not referred to any further in the analysis and discussion? Why a specific term for plant transpiration is not included, or is to somehow phenomenologically incorporated into the growth-tolerance tradeoff? In doing so, authors should also pay attention to water balance as above (H) and below (W) ground water are not independent from each other.

We added a Methods section, which in eLife is placed at the end of the manuscript. The section includes the model equations and more detailed explanations in ecological terms of various parts of the model. We also added Table 1 with a list of all model parameters, their descriptions, units and numerical values used in the simulations. Presenting the model at the end of the manuscript suits more technical information about the model, but not essential information that is needed for understanding the results. We therefore kept the subsection “A model for spatial assembly of dryland plant communities” in the Results section, where we present that information.

There is no conservation of mass in the model (and all other models of this kind) simply because the system that we consider is open. In particular, it does not include the atmosphere, which constitute part of the system’s environment. Including the atmosphere as additional state variables in the model, capturing the feedback of evapotranspiration on the atmosphere, would make the model too complicated for the kind of analysis we perform. So, although the model contains parts that represent mass conservation such as the terms describing below- and above-ground water transport, water mass is not conserved. The biomass variables represent aboveground biomass of living plants or plant parts and are not conserved either as biomass production involve biochemical reactions that convert inorganic substances coming from the system’s environment (atmosphere and the soil) into organic ones, while plant mortality involves organic matter that leaves the system.

Roots in the model platform we consider are modeled indirectly through their relation to aboveground biomass. That relation constitutes one of the scale-dependent feedbacks that produce a Turing instability to vegetation patterns, the so-called root-augmentation feedback (see Meron 2019, Physics Today), but in this particular study we eliminate this feedback for simplicity. The scale-dependent feedback that we do consider is the so-called infiltration feedback, associated with biomass-dependent infiltration rate that produces overland water flow towards vegetation patches, as explained in the subsection “A model for spatial assembly of dryland plant communities”. It will be interesting indeed to extend the study in the future to include also the root-augmentation feedback.

We assume short-range seed dispersal and take it into account through biomass “diffusion” terms (obtained as approximations of dispersal kernels assuming narrow kernels). These terms play important roles in the scale-dependent feedback that induces the Turing instability, as is explained in earlier papers which we cite. Plant transpiration is modeled through the water uptake term in the equation for the soilwater 𝑊. Indeed above-ground water 𝐻 and below-ground water 𝑊 are not independent; the infiltration term IH in the equations for both state variables account for this dependence in a unidirectional manner (loss of 𝐻 and gain of 𝑊). As we do not include the atmosphere in the model the other direction, namely, evapotranspiration that increases air humidity and affects rainfall, is not accounted for. The neglect of this effect can be justified for sparse dryland vegetation.

These good points have already been discussed in many earlier papers as well as in the book Nonlinear Physics of Ecosystems (Meron 2015), and we cannot address them all in this paper. We did however add several clarifications in the section Modeling spatial assembly of dryland plant communities and in the new Methods section, including the consideration of the atmosphere as the system’s environment quantified by the precipitation parameter 𝑃.

Another unclear point is that growth rates for the same plant functional groups are assumed to be constant among different species within the same group and are confounded by biomass production. Why is that the case? Furthermore, how many different species are characterizing each functional group? How are interspecific interactions accounted for (more specifically, see comment below)?

In the trait-based approach we focus on just two functional traits, related to growth rate and tolerance to water stress, ignoring differences in other traits that distinguish species. That is, a given functional group consists of species that share the same values of the two selected functional traits (to a given precision determined by 𝑁), taking all other traits represented in the model to be equal. In this approach we do not care about how many species belong to each functional group, only their total biomass. We wish to add that simplifying assumptions of this kind are necessary if we want the model to be mathematically tractable and capable of providing deep insights by mathematical analysis.

We expanded the discussion of the trait-based approach in the section Modeling spatial assembly of dryland plant communities and added relevant references (second paragraph).

Finally, stress tolerance is purely phenomenological. There is no actual mechanism/parameter describing it. Rather, it "simply" appears as low/high mortality, which in turn is said to be due to high/low tolerance. This leads to a sort of circularity between mortality and tolerance. Yet, mortality can occur due to other biophysical factors (e.g. disturbance, fire, herbivory, pathogens). A drawback of this assumption is that a mechanism of drought tolerance is often to invest in belowground organs, including roots. However, according to the proposed model, it turns out that fast growing species with low investment in tolerance also have high investment in roots; vice versa, tolerant species have low investment in roots. This is a bit counterintuitive and not well biologically supported.

First, we agree with the reviewer that our approach is purely phenomenological, as we model tolerance to water stress by a single parameter that lumps together the effects of various physiological mechanisms. That parameter can be distinguished from other factors affecting mortality by regarding the constant 𝑀𝑚𝑎𝑥 in Eq. (3) as representing several contributions. Since we do not study the effects of these other factors we can absorb them in 𝑀𝑚𝑎𝑥 for mathematical simplicity. Tolerance to water stress is not necessarily associated with roots. Plants can better tolerate water stress by reducing transpiration through stomatal closure, regulating leaf water potential, or develop hydraulically independent multiple stems that lead to a redundancy of independent conduits and higher resistance to drought (see Schenk et al. 2008 - https://doi.org/10.1073/pnas.0804294105).

We added a discussion in the Methods section (5th paragraph, “Tolerance to water stess …”) of the simple form by which we model tolerance to water stress through the mortality parameter.

2) Parameter choice.

N = 128 is an extremely high number for plant functional groups. It is even quite unrealistic to have 128 species per square meter, so this value is not very reasonable. Please run the model and report results with more realistic N (e.g from 4-64) as well as with different sets of N values keeping all other parameters constant.

We wish to clarify two points: 1) N=128 does not imply 128 functional groups per square meter; the emerging community has much lower functional richness (FR) as the average FR is around 0.25, meaning only 128 × 0.25 = 32 functional groups. 2) The model results, as reflected by the key metrics 𝜒𝑚𝑎𝑥, 𝐹𝑅, and 𝐹𝐸, are independent of the particular value of N (for N values sufficiently large), as Figures IA and IB below show. The biomass 𝐵𝑖 of each functional group, however, does change (Figure IA) because by changing N we change the range of traits Δ𝜒 = 1/𝑁 that belong to a given functional group. But if we look at the biomass density in trait space 𝑏𝑖, related to 𝐵𝑖 through the relation 𝐵𝑖 = 𝑏𝑖Δ𝜒, then also the biomass density is independent of 𝑁 as Figure IB shows. So, even if in practice there are less functional groups and thus species as considered in the model studies, the results are not affected by that. On the other hand, choosing higher 𝑁 values provides smoother curves and nicer presentation of our results.

Figure IA

Figure IB

We added a discussion of this issue in the Methods section after Eq. (2).

Gamma (rate of water uptake by plants' roots): why is it in that unit of m^2/kg * y? Why are you now considering the area (and not the volume) per biomass unit?

The vegetation pattern formation model we study, like most other models of this kind, does not explicitly capture the soil depth dimension. Accordingly, W is interpreted as the soil-water content in the soil volume below a unit ground area within the reach of the plant roots. In practice W has units kg/m2, like B, and since Γ𝑊𝐵 should have the same units as 𝜕𝑊/𝜕𝑡 (see Eq. 1b), Γ must have the units of (𝐵𝑡)−1.

A is not defined in the text.

We now define it in Table 1 (see Methods section).

M min: why 0.5 mortality? Having M max set to 0.9, please consider a lower mortality value set to 0.1, and please report evidence(hopefully) demonstrating the robustness of results to such change.

The results are robust to the particular values of 𝑀𝑚𝑖𝑛 and 𝑀𝑚𝑎𝑥, except that there are combinations of these two parameters for which the biomass distributions are pushed towards the edge of the 𝜒 domain, which make the presentation of the results less clear. Figure II shows results of recalculations of the distribution 𝐵 = 𝐵(𝜒) for 𝑀𝑚𝑖𝑛 = 0.1, as requested (using 𝑀𝑚𝑎𝑥 = 0.15) for 3 different precipitation values. As the reviewer can see there’s no qualitative change in the results: lower precipitation push a uniform community to stress tolerant species (higher 𝜒), while the formation of patterns at yet lower precipitation push the community back to fast growing species (low 𝜒).

Figure II

K_min and K_max are in two different units, and should both be kg/m^2.

Thanks, we fixed this typo in Table 1.

Values of precipitation (P, mean annual precipitation) are not reported.

The precipitation parameter is variable, as is now stated in Table 1, and therefore was not include it in the list of parameters’ values used. Whenever a particular precipitation value has been used our intention was to state it in the caption of the corresponding figure. This was done in Figs. 5,6,7, but indeed not in Fig. 4 (Fig. 3 in revised ms.). The insets on the right side of Fig. 3 (Fig. 4 in revised ms.) where also calculated for particular precipitation values, but that information is not essential as the intention is to show typical forms of the various solution branches, which do not qualitatively change along the branches (i.e. at different P values).

We added the precipitation value (P=180mm/y) at which all the biomass distributions shown in new Fig. 3 (Fig. 4 in original ms) were calculated.

3) Results presentation and interpretation.

Parameter range of precipitation in figure 3 is odd. Why in one case precipitation ranges from 0 to 160 while in another it is only 60-120? Furthermore, in paragraph 198-213 and associated results in fig. 5. the Choice of precipitation values is somehow discordant from the previous model. Please provide motivation for this choice, clarify and uniformize it.

In Fig. 3b (Fig. 4b in revised ms) we restricted the precipitation range to 60-120 as the curves, which are limited to 0 < 𝜒 < 1 (by the definition of 𝜒), do not extend to 𝑃 < 60 and to 𝑃 > 120. Extending the range to 0 < 𝑃 < 160 would make the figure less compact and nice as it will contain blank parts with no information.

We are not sure we understand what the reviewer means by “is somehow discordant from the previous model”. The motivation of the choices we made for the precipitation values P=150, 100 and 80 was to show the shift of a spatially uniform community to a higher 𝜒 value as the precipitation is decreased to a lower value (from 150 to 100), and the shift back to a lower 𝜒 value at yet lower precipitation (80) past the Turing instability.

Finally, authors seem to create confusion around community composition, which is defined as the (taxonomic) identity of all different species inhabiting a community. Notably, it is remarkably different from the x_max parameter used in the model, which as a matter of fact is just the value of the most productive (notably, not necessarily the most abundant) functional group.

We thank the reviewer for this comment. Since all the emerging communities in the model studies are pretty localized around the value of 𝜒𝑚𝑎𝑥, that value does contain information about the identity of other functional groups in the community when complemented by FR (functional richness) and FE (functional evenness). More significantly to our study, shifts in 𝜒𝑚𝑎𝑥 represent the shifts in community composition we focus on in this study, i.e. shifts towards fast growing species or towards stress-tolerant species.

We modified the description of the community-level properties that can be derived from the biomass distribution in trait space (see modified text towards the end of the section “Modeling spatial assembly …” and also the caption of Fig. 3b), explaining that both functional diversity and community composition can be described by several metrics, and clarifying the significance of 𝜒𝑚𝑎𝑥 in describing community-composition shifts.

Author Response

Reviewer #1 (Public Review):

The authors convincingly show in this study the effects of the fas5 gene on changes in the CHC profile and the importance of these changes toward sexual attractiveness.

The main strength of this study lies in its holistic approach (from genes to behaviour) showing a full and convincing picture of the stated conclusions. The authors succeeded in putting a very interdisciplinary set of experiments together to support the main claims of this manuscript.

We appreciate the kind comments from the reviewer.

The main weakness stems from the lack of transparency behind the statistical analyses conducted in the study. Detailed statistical results are never mentioned in the text, nor is it always clear what was compared to what. I also believe that some tests that were conducted are not adequate for the given data. I am therefore unable to properly assess the significance of the results from the presented information. Nevertheless, the graphical representations are convincing enough for me to believe that a revision of the statistics would not significantly affect the main conclusions of this manuscript.

We apologize for neglecting a detailed description of statistical tests that were performed. We wrote additional paragraphs in the method part specifically explaining the statistical analyses (line 435-445; 489-502; 559-561; 586-591).

The second major problem I had with the study was how it brushes over the somewhat contradicting results they found in males (Fig S2). These are only mentioned twice in the main text and in both cases as being "similarly affected", even though their own stats seem to indicate otherwise for many of the analysed compound groups. This also should affect the main conclusion concerning the effects of fas5 genes in the discussion, a more careful wording when interpreting the results is therefore necessary.

Thank you for pointing this out. Though our focus clearly lay on the female CHC profiles as a function in sexual signaling has only been described thus far for them, we now elaborated the result and discussion for the fas5 RNAi male part (line 167-178; 258-268).

Reviewer #2 (Public Review):

Insects have long been known to use cuticular hydrocarbons for communication. While the general pathways for hydrocarbon synthesis have been worked out, their specificity and in particular the specificity of the different enzymes involved is surprisingly little understood. Here, the authors convincingly demonstrate that a single fatty acid synthase gene is responsible for a shift in the positions of methyl groups across the entire alkane spectrum of a wasp, and that the wasps males recognize females specifically based on these methyl group positions. The strength of the study is the combination of gene expression manipulations with behavioural observations evaluating the effect of the associated changes in the cuticular hydrocarbon profiles. The authors make sure that the behavioural effect is indeed due to the chemical changes by not only testing life animals, but also dead animals and corpses with manipulated cuticular hydrocarbons.

I find the evidence that the hydrocarbon changes do not affect survival and desiccation resistance less convincing (due to the limited set of conditions and relatively small sample size), but the data presented are certainly congruent with the idea that the methyl alkane changes do not have large effects on desiccation.

We appreciate the kind comments from the reviewer.

Reviewer #3 (Public Review):

In this manuscript, the authors are aiming to demonstrate that a fatty-acyl synthase gene (fas5) is involved in the composition of the blend of surface hydrocarbons of a parasitoid wasp and that it affects the sexual attractiveness of females for males. Overall, the manuscript reads very well, it is very streamlined, and the authors' claims are mostly supported by their experiments and observations.

We appreciate the kind comments from the reviewer.

However, I find that some experiments, information and/or discussion are absent to assess how the effects they observe are, at least in part, not due to other factors than fas5 and the methyl-branched (MB) alkanes. I'm also wondering if what the authors observe is only a change in the sexual attractiveness of females and not related to species recognition as well.

We appreciate the interesting point that the reviewer raises in sexual attractiveness and species recognition and now expand upon this potential aspect in the discussion (lines 327-330). However, in this manuscript, we very much focused on the effect of fas5 knockdown on the conveyance of female sexual attractiveness in a single species (Nasonia vitripennis). Therefore, we argue that species recognition constitutes a different communication modality here, and we currently cannot infer whether and how species recognition is exactly encoded in Nasonia CHC profiles despite some circumstantial evidence for species-specificity (Buellesbach et al. 2013; Mair et al. 2017). Thus, we would like to refrain from any further speculation on species recognition before this can be unambiguously demonstrated, and remain within the mechanism of sexual attractiveness within a single species which we clearly show is mediated by the female MB-alkane fraction governed by the fatty acid synthase genes. We however still consider potential alternative explanations (e.g., n-alkenes acting as a deterrent of homosexual mating attempts).

The authors explore the function of cuticular hydrocarbons (CHCs) and a fatty-acyl synthase in Nasonia vitripennis, a parasitic wasp. Using RNAi, they successfully knockdown the expression of the fas5 gene in wasps. The authors do not justify their choice of fatty-acyl synthase candidate gene. It would have been interesting to know if that is one of many genes they studied or if there was some evidence that drove them to focus their interest in fas5.

In a previous study, 5 fas candidate genes orthologous to Drosophila melanogaster fas genes were identified and mapped in the genome of Nasonia vitripennis (Buellesbach et al. 2022). We actually investigated the effects of all of these fas genes on CHC variation, but only fas5 led to such a striking, traceable pattern shift. We are currently preparing another manuscript discussing the effects of the other fas genes, but decided to focus exclusively on fas5 here, due to its significance for revealing how sexual attractiveness can be encoded and conveyed in complex chemical profiles, maintained and governed by a surprisingly simple genetic basis.

The authors observe large changes in the cuticular hydrocarbons (CHC) profile of male and females. These changes are mostly a reduction of some MB alkanes and an increase in others as well as an increase of n-alkene in fas5 knockdown females. For males fas5 knockdowns, the overall quantity of CHC is increased and consequently, multiple types of compounds are increased compared to wild-type, with only one compound appearing to decrease compared to wild-type. Insects are known to rely on ratios of compounds in blends to recognize odors. Authors address this by showing a plot of the relative ratios, but it seems to me that they do show statistical tests of those changes in the proportions of the different types of compounds. In the results section, the authors give percentages while referring to figures showing the absolute amount of CHCs. They should also test if the ratios are significantly different or not between experimental conditions. Similar data should be displayed for the males as well.

We appreciate your suggestions. We kindly refer you to our response to reviewer 1, where we addressed the statistical tests. Specifically, we generated separate subplots to display the proportions of different compound classes and performed statistical tests to compare these proportions between different treatments for both males and females. Additionally, we have revised the results section to replace relative abundances with absolute quantity, as depicted in Figure 2C-G.

Furthermore, the authors didn't use an internal standard to measure the quantity of CHCs in the extracts, which, to me, is the gold standard in the field. If I understood correctly, the authors check the abundance measured for known quantities of n-alkanes. I'm sure this method is fine, but I would have liked to be reassured that the quantities measured through this method are good by either testing some samples with an internal standard, or referring to work that demonstrates that this method is always accurate to assess the quantities of CHC in extracts of known volumes.

We actually did include 7,5 ng/μl dodecane (C12) as an “internal” standard in the hexane resuspensions of all of our processed samples (line 456, Materials and Methods). This was primarily done to allow for visually inspecting and comparing the congruence of all chromatograms in the subsequent data analysis and immediately detect any variation from sample preparation, injection process and instrument fluctuation. In our study, we have a very elaborate and standardized CHC extraction method that the volume of solvent and duration for extraction are strictly controlled to minimize the variation from sample preparation steps. Furthermore, we calibrated each individual CHC compound quantity with a dilution series of external standards (C21-C40) of known concentration. By constructing a calibration curve based on this dilution series, we achieved the most accurate compound quantification, also taking into account and counteracting the generally diminishing quantities of compounds with higher chain lengths.

The authors provide a sensible control for their RNAi experiments: targeting an unrelated gene, absent in N. vitripennis (the GFP). This allows us to see if the injection of RNAi might affect CHC profiles, which it appears to do in some cases in males, but not in females. The authors also show to the reader that their RNAi experiments do reduce the expression of the target gene. However, one of the caveats of their experiments, is that the authors don't provide evidence or information to allow the (non-expert) reader to assess whether the fas5 RNAi experiments did affect the expression of other fatty-acyl synthase genes. I'm not an expert in RNAi, so maybe this suggestion is not relevant, but it should, at least, be addressed somewhere in the manuscript that such off-target effects are very unlikely or impossible, in that case, or more generally.

We acknowledge the reviewer’s concern about potential off-target effect of the fas5 knockdown. We actually did check initially for off-target effects on the other four previously published fas genes in N. vitripennis (Lammers et al. 2019; Buellesbach et al. 2022) and did not find any effects on their respective expressions. We now include these results as supplementary data (Figure 2-figure supplement 1). However, as mentioned in the cover letter to the editor, we discovered a previously uncharacterized fas gene in the most recent N. vitripennis genome assembly (NC_045761.1), fas6, most likely constituting a tandem gene duplication of fas5. These two genes turned out to have such high sequence similarity (> 90 %, Figure 2-figure supplement 2) that both were simultaneously downregulated by our fas5 dsRNAi construct, which we confirmed with qPCR and now incorporated into our manuscript (Fig. 2H). Therefore, we now explicitly mention that the knockdown affects both genes, and either one or both could have the observed phenotypic effects. Recognizing this RNAi off-target effect, we have now also incorporated a discussion of this issue in the appropriate section of the manuscript (line 364-377), as well as the potential off-target effects of our GFP dsRNAi controls (line 262-274).

The authors observe that the modified CHCs profiles of RNAi females reduce courtship and copulation attempts, but not antennation, by males toward live and (dead) dummy females. They show that the MB alkanes of the CHC profile are sufficient to elicit sexual behaviors from males towards dummy females and that the same fraction from extracts of fas5 knockdown females does so significantly less. From the previous data, it seems that dummy females with fas5 female's MB alkanes profile elicit more antennation than CHC-cleared dummy females, but the authors do not display data for this type of target on the figure for MB alkane behavioral experiments.

Actually similar proportions of males performed antennation behavior towards female dummies with MB alkane fraction of fas5 RNAi females and CHC-cleared female dummies (55% and 50%, respectively, see Author response image 1 for the corresponding parts of the sub-figures 3 E and 4 D). We did not deem it necessary to show the same data on CHC-cleared female dummies in Figure 3 as well.

Author response image 1.

Unfortunately, the authors don't present experiments testing the effect of the non-MB alkanes fractions of the CHC extracts on male behavior toward females. As such, they are not able to (and didn't) conclude that the MB-alkane is necessary to trigger the sexual behaviors of males. I believe testing this would have significantly enhanced the significance of this work. I would also have found it interesting for the authors to comment on whether they observe aggressive behavior of males towards females (live or dead) and/or whether such behavior is expected or not in inter-individual interactions in parasitoids wasps.

In our experiment, we focus on the function of the MB-alkane fraction in female CHC profiles, and we comprehensibly demonstrate in figure 4 that the MB-alkane fraction from WT females alone is sufficient to trigger mating behavior coherent with that on alive and untreated female dummies. Therefore, we do not completely understand the reviewer’s concern about us not being ” able to (and didn't) conclude that the MB-alkane is necessary to trigger the sexual behaviors of males”. We appreciate the suggestion from the reviewer of testing the non-MB alkanes (n-alkanes and n-alkenes). However, due to the experimental procedure of separating the CHC compound class fractions through elution with molecular sieves, it was not possible for us to retrieve either the whole n-alkane or n-alkene fraction remaining bound to the sieves after separation). The role of n-alkenes in N. vitripennis is however considered in the discussion, as a deterrent for homosexual interactions between males (Wang et al. 2022a). Moreover, we did not observe aggressive behavior of males towards live or dead females.

CHCs are used by insects to signal and/or recognize various traits of targets of interest, including species or groups of origin, fertility, etc. The authors claim that their experiments show the sexual attractiveness of females can be encoded in the specific ratio of MB alkanes. While I understand how they come to this conclusion, I am somewhat concerned. The authors very quickly discuss their results in light of the literature about the role of CHCs (and notably MB alkanes) in various recognition behaviors in Hymenoptera, including conspecific recognition. Previous work (cited by the authors) has shown that males recognize males from females using an alkene (Z9C31). As such, it remains possible that the "sexual attractiveness" of N. vitripennis females for males relies on them not being males and being from the right species as well. The authors do not address the question of whether the CHCs (and the MB alkanes in particular) of females signal their sex or their species. While I acknowledge that responding to this question is beyond the scope of this work, I also strongly believe that it should be discussed in the manuscript. Otherwise, non-specialist readers would not be able to understand what I believe is one of the points that could temper the conclusions from this work.

We acknowledge the reviewer’s insight about the MB alkanes in signaling sex or species in N. vitripennis, and now include this aspect in our revised discussion (line 324-330). Moreover, we clearly demonstrate that n-alkenes have been reduced to minute trace components after our compound class separation, and the males still do not display courtship and copulation behaviors similar to WT females, thus strongly indicating that the n-alkenes do not play a role when relying solely on the changed MB-alkane patterns, further strengthening our main argument.

References

Benjamini, Y. and D. Yekutieli. 2001. The control of the false discovery rate in multiple testing under dependency. Ann. Stat. 29:1165-1188.

Buellesbach, J., J. Gadau, L. W. Beukeboom, F. Echinger, R. Raychoudhury, J. H. Werren, and T. Schmitt. 2013. Cuticular hydrocarbon divergence in the jewel wasp Nasonia: Evolutionary shifts in chemical communication channels? J. Evol. Biol. 26:2467-2478.

Buellesbach, J., C. Greim, and T. Schmitt. 2014. Asymmetric interspecific mating behavior reflects incomplete prezygotic isolation in the jewel wasp genus Nasonia. Ethology 120:834-843.

Buellesbach, J., H. Holze, L. Schrader, J. Liebig, T. Schmitt, J. Gadau, and O. Niehuis. 2022. Genetic and genomic architecture of species-specific cuticular hydrocarbon variation in parasitoid wasps. Proc. R. Soc. B 289:20220336.

Engl, T., N. Eberl, C. Gorse, T. Krüger, T. H. P. Schmidt, R. Plarre, C. Adler, and M. Kaltenpoth. 2018. Ancient symbiosis confers desiccation resistance to stored grain pest beetles. Mol. Ecol. 27:2095-2108.

Ferveur, J. F., J. Cortot, K. Rihani, M. Cobb, and C. Everaerts. 2018. Desiccation resistance: effect of cuticular hydrocarbons and water content in Drosophila melanogaster adults. Peerj 6.

Lammers, M., K. Kraaijeveld, J. Mariën, and J. Ellers. 2019. Gene expression changes associated with the evolutionary loss of a metabolic trait: lack of lipogenesis in parasitoids. BMC Genom. 20:309.

Mair, M. M., V. Kmezic, S. Huber, B. A. Pannebakker, and J. Ruther. 2017. The chemical basis of mate recognition in two parasitoid wasp species of the genus Nasonia. Entomol. Exp. Appl. 164:1-15.

Wang, Y., W. Sun, S. Fleischmann, J. G. Millar, J. Ruther, and E. C. Verhulst. 2022a. Silencing Doublesex expression triggers three-level pheromonal feminization in Nasonia vitripennis males. Proc. R. Soc. B 289:20212002.

Wang, Z., J. P. Receveur, J. Pu, H. Cong, C. Richards, M. Liang, and H. Chung. 2022b. Desiccation resistance differences in Drosophila species can be largely explained by variations in cuticular hydrocarbons. eLife 11:e80859.

Author Response

Reviewer #1 (Public Review):

In this manuscript, the authors investigate the genes involved in the retention of eggs in Aedes aegypti females. They do so by identifying two candidate genes that are differentially expressed across the different reproductive phases and also show that the transcripts of those two genes are present in ovaries and in the proteome. Overall, I think this is interesting and impressive work that characterizes the function of those two specific protein-coding genes thoroughly. I also really enjoyed the figures. Although they were a bit packed, the visuals made it easy to follow the authors' arguments. I have a few concerns and suggested changes, listed below.

1) These two genes/loci are definitely rapidly evolving. However, that does not automatically imply that positive selection has occurred in these genes. Clearly, you have demonstrated that these gene sequences might be important for fitness in Aedes aegypti. However, if these happen to be disordered proteins, then they would evolve rapidly, i.e., under fewer sequence constraints. In such a scenario, dN/dS values are likely to be high. Another possibility is that as these are expressed only in one tissue and most likely not expressed constitutively, they could be under relaxed constraints relative to all other genes in the genome. For instance, we know that average expression levels of protein-coding genes are highly correlated with their rate of molecular evolution (Drummond et al., 2005). Moreover, there have clearly been genome rearrangements and/or insertion/deletions in the studied gene sequences between closely- related species (as you have nicely shown), thus again dN/dS values will naturally be high. Thus, high values of dN/dS are neither surprising nor do they directly imply positive selection in this case. If the authors really want to investigate this further, they can use the McDonald Kreitman test (McDonald and Kreitman 1991) to ask if non- synonymous divergence is higher than expected. However, this test would require population-level data. Alternatively, the authors can simply discuss adaptation as a possibility along with the others suggested above. A discussion of alternative hypotheses is extremely important and must be clearly laid out.

We agree with the reviewer’s point that rapid evolution is not the same as positive selection. We also agree with the reviewer’s point that McDonald-Kreitman test (MK test) is more powerful than dN/dS analysis. We took advantage of a large population dataset from Rose et al. 2020. After filtering the data, we kept 454 genomes for MK tests. We found both genes are marginally significant or insignificant (tweedledee p = 0.068; tweedledum p = 0.048), despite that these are small genes and have low Pn values. This suggests that it is likely the genes evolve under positive selection.

In line with the reviewer’s suggestion, we performed another analysis using a large amount of population data. We asked if the SNP frequencies of tweedledee and tweedledum are correlated with environmental variables. We found that when compared to a distribution of 10,000 simulated genes with randomly-sampled genetic variants, both tweedledee and tweedledum showed significant correlation to multiple ecological variables reflecting climate variability, such as mean diurnal range, temperature seasonality, and precipitation seasonality (p<0.05). These results are now incorporated into the manuscript in Figure 5 and Figure 5 – Figure supplement 1.

2) The authors show that the two genes under study are important for the retention of viable eggs. However, as these genes are close to two other conserved genes (scratch and peritrophin-like gene), it is unclear to me how it is possible to rule out the contribution of the conserved genes to the same phenotype. Is it possible that the CRISPR deletion leads to the disruption of expression of one of the other important genes nearby (i.e., in a scratch or peritrophin-like gene) as the deleted region could have included a promoter region for instance, which is causing the phenotype you observe? Since all of these genes are so close to each other, it is possible that they are co-regulated and that tweedledee and tweedledum and expressed and translated along with the scratch and peritrophin-like gene. Do we know whether their expression patterns diverge and that scratch and peritrophin-like genes do not play a role in the retention of viable eggs?

This is a fair criticism; however, we think the chance that the phenotypes are caused by interrupting nearby genes is very low. First, peritrophin-like acts in the immune response, and scratch is a brain-biased transcription factor. Neither of the genes show expression in the ovary before or after blood feeding (TPM <1 or 2 are generally considered unexpressed, while scratch and peritrophin-like expression levels are overall lower than 0.1 TPM).

This suggests that peritrophin-like and scratch are not likely to function in the ovary. Thus, although we cannot completely rule out the gene knockout impacts regulation of very distant genes, it is unlikely. Since the mounting evidence we show in this manuscript that tweedledee and tweedledum are highly translated in the ovary after blooding feeding, under the principle of parsimony, we expect the phenotypes came from knocking out the highly expressed and translated genes.

Reviewer #2 (Public Review):

This manuscript is overall quite convincing, presenting a well- thought-out approach to candidate gene detection and systemic follow- ups on two genes that meet their candidate gene criteria. There are several major claims made by the authors, and some have more compelling evidence than others, but in general, the conclusions are quite sound. My main issues stem from how the strategy to identify genes playing a role in egg retention success has led to very particular genes being examined, and so I question some of the elements of the discussion focusing on the rapid evolution and taxon- uniqueness of the identified genes. In short, while I believe the authors have demonstrated that tweedledee and tweedledum play an important role in egg retention, I'm not sure whether this study should be taken as evidence that taxon-specific or rapidly evolving genes, in general, are responsible for this adaptation, or simply play an important role in it.

We have revised the paper to make it clearer that the focus is indeed on these two genes on not on the greater question of taxon-specific or rapidly-evolving genes.

First, the authors present evidence that Aedes aegypti females can retain eggs when a source of fresh water is lacking, confirming that females are not attracted to human forearms while retaining eggs and that up to 70% of the retained eggs hatch after retaining them for nearly a week. This ability is likely an important adaptation that allows Aedes aegypti to thrive in a broad range of conditions. The data here seem fairly compelling.

Based on this observation, the authors reason that genes responsible for the ability to retain eggs must: 1) be highly expressed in ovaries during retention, but not before or after. 2) be taxon-specific (as this behavior seems limited to Aedes aegypti). While this approach to enriching candidate genes has proven fruitful in this particular case, I'm not sure I agree with the authors' rationale. First, even genes at a low expression in the ovaries may be crucial to egg retention. Second, while egg-laying behavior is vastly varied in insects, I'm not sure focusing on taxon-restricted genes is necessary. It is entirely possible that many of the genes identified in Figure 2E play a crucial role in egg retention evolution. These are minor issues, but they are relevant to some later points made by the authors.

We regret framing the discovery of tweedledee and tweedledum in the original submission using this somewhat artificial set of filtering criteria. The reality is that the genes caught our attention for their novel sequence, tight genetic linkage, and interesting expression profile. That really is the focus of the paper, not these other peripheral questions that have been the focus of attention of the reviews. We really do apologize for all of the confusion about what this paper is about.

Nonetheless, the authors provide very compelling evidence that the two genes meeting their criteria - tweedledee and tweedledum, play an important role in egg retention. The genes seem to be expressed primarily in ovaries during egg retention (some observed expression in brain/testes is expected for any gene), and the proteins they code seem to be found in elevated quantities in both ovaries and hemolymph during and immediately after egg retention. RNA for the genes is detected in follicles within the ovary, and CRISPR knockouts of both the genes lead to a large decrease in egg viability post retention.

My earlier qualms about their search strategy relay into some issues with Figure 4, which describes how the two genes are 1) taxon- restricted and 2) have evolved very rapidly. Neither of the two statements is unexpected given the authors' search strategy. Of course, the genes examined precisely for their lack of homologs do not have any homologs. Similarly, by limiting themselves to genes that show a lack of homology (i.e. low sequence similarity) to other genes as well as genes with high expression levels in the ovaries, a higher rate of evolution is almost inevitable to infer (as ovary expressed genes tend to evolve more rapidly in mosquitoes). I agree with the authors that inferences of the evolutionary history of these genes are quite difficult because of their uniqueness, and I especially appreciate their attempts to identify homologs (although I really dislike the term "conceptualog").

We have removed our term “conceptualog” and replaced with the mor conventional “putative ortholog”

This leads to my main (fairly minor) issue of the paper - the discussion on the evolutionary history of these genes and its implications (sections "Taxon-restricted genes underlie tailored adaptations in a diverse world" and "Evolutionary histories and catering to different natural histories"). As noted, inferring this history is very difficult because the authors have focused on two rapidly evolving, taxon-restricted genes. The analyses they have performed here definitely demonstrate that the genes play an important role in egg retention, however, they do not show that taxon-restricted genes play a disproportionate role in egg retention evolution. Indeed, the only data relevant to this point would be the proportion of genes in Figure 2E that are taxon-restricted (3/9), but I'm not sure what the null expectation for this proportion for highly expressed ovary genes is to begin with. Furthermore, the extremely rapid evolution of this gene makes it hard to judge how truly taxon-restricted it is. My own search of tweedle homologs identified multiple as previously having been predicted to be "Knr4/Smi1-like", and while no similar genes are located in a similar location in melanogaster, there is generally little synteny conservation in Drosophila (for instance Bhutkar et al 2008), so I'm unsure what can really be said about their evolutionary origins/lack of homologs in Drosophila.

In short - the manuscript makes clear that tweedledee and tweedledum play an important role in egg retention in A. aegypti, nonetheless, it is not clear that this is a demonstration of how important taxon- restricted genes are to understanding the evolution of life-history strategies.

Again, we should have never framed the paper the way we did in the original version. We make no claims whatsoever that taxon-restricted genes in general should play a role in this biology, only that the two candidate genes under study influence egg viability after extended retention. We hope that the framing is clearer in this revision.

Author Response:

Reviewer #1 (Public Review):

This study sought to systematically identify the components and driving forces of transcriptome evolution in fungi that exhibit complex multicellularity (CM). The authors examined a series of parameters or expression signatures (i.e. natural antisense transcripts, allele-specific expression, RNA-editing) concluding that the best predictor of a gene behavior in the CM transcriptome was evolutionary age.

Thus, the transcriptomes of fruiting bodies showed a distinct gene-age-related stratification, where it was possible to sort out genes related to general sexual processes from those likely linked to morphogenetic aspects of the CM fruiting bodies. Notably, their results did not support a developmental hourglass, which is the rather predominant hypothesis in metazoans, including some analysis in fungi.

The studies involved analyses of new transcriptomic datasets for different developmental stages (and tissue types in some cases) of Pleurotus ostreatus and Pterula gracilis, as well as the analyses of existing datasets for other fungi.

There are diverse interesting observations such as ones regarding Allele Specific Expression (ASE), suggesting that in P. ostreatus ASE mainly occurs due to cis-regulatory allele divergence, possibly in fast evolving genes that are not under strong selection constraints, such as ones grouped in youngest gene ages categories. In addition, a large number of conserved unannotated genes among CM-specific orthogroups highlights the rather cryptic nature of CM in fungi and raises as an important area for future research.

Some of the key aspects of the analyses would need to be better exemplified such as:

– Providing a better description of the developmentally expressed TFs only in CM species

– Providing clear examples of the promoter divergence that could be the underlying mechanism behind ASE. In particular, for some cases, there may be enough information in the literature/databases to predict the appearance or disappearance of relevant cis-elements in the promoters showing the highest divergence in genes depicting the highest levels of ASE.

We appreciate the constructive comments of the Reviewer and have revised the ms in accordance with the suggestions. In particular, we link different parts of the ms better to each other, provided a more detailed discussion of developmentally expressed TFs (lines 615-621). We also provide case studies of ASE genes with cis-regulatory divergence (Figure 5 and see below), although we note that these analyses are based on inferred and not directly determined motifs, so they should be considered as preliminary.

We had considered using TF binding motifs previously, and now we gave a try to analyzing potential transcription factor binding sites in divergent promoters. We find that there are no P. ostreatus transcription factors for which motifs based on direct evidence are available; rather, all P. ostreatus motifs are based on extrapolations from experimentally determined motifs (typically in Neurospora crassa). Therefore, to avoid too general motifs, we used only those where at least 5 nucleotides show at least 80% expected frequency in the PWM-s. This left us with 158 motifs (126 excluded). High motif binding score (>=4) and self-rate (>=0.9) were also required to ignore false positive hits. Different binding ability and lack of binding in one of the parental genomes were counted for each promoter. We found that genes with allele specific expression (ASE S2 and S4) show significantly higher differences in motif binding (lacking motifs, or different binding ability) than non-ASE genes (Fig. A1). These observations show that, not only promoter divergence, but differential predicted TF binding ability is also more common among ASE genes than among non-ASE genes. This supports our conjecture that ASE arises from cis-regulatory divergence.

Fig A1: The left plot below shows the number of cases when the promoter of one allele of an allele pair in the two parent genomes has, but the other lacks a motif. The right plot shows the same in terms of difference in binding score.

We could find examples, such as the allele specific expression of PleosPC15_2_1031042, a Hemerythrin-like (IPR012312) protein which might be regulated by the conserved c2h2 transcription factor, containing zinc finger domain of the C2H2 type (Fig. A2). C2h2 has already been proved to be important during the initiation of primordia formation with targeted gene inactivation (Ohm et al 2011, https://pubmed.ncbi.nlm.nih.gov/21815946/). A binding site of c2h2 was detected in the upstream region of PleosPC15_2_1031042. There is a mismatch in the inferred binding motif which causes a reduced binding score in PC15 (Fig. A2/c). Indeed the PC9 nuclei contribute better to the total expression of this gene.

Despite this, and other (not shown) examples that we have found, we were not convinced about the reliability of this approach. There are many assumptions in this analysis, the positional weight matrices (PWM) that we used, are all based on indirect evidence, high number of loci these PWMs identify, uncertainty in the position of binding site from transcriptional start site, relation of difference in binding motif and expressional changes. We consider these factors to potentially contribute too much noise to the analyses for these to be robust, therefore, we are hesitant to include these results in the ms.

Fig A2: An example for promoter divergence a) expression of c2h2 transcription factor (TF) in P. ostreatus. b) allele-specific expression pattern of PleosPC15_2_1031042 from the two parental genomes. c) inferred binding motif of c2h2 TF and a detected potential binding site in the upstream region of PleosPC15_2_1031042 gene.

Reviewer #2 (Public Review):

The evolution of complex multicellularity represents a major developmental reprogramming, and comparing related species which differ in multicellular structures may shed light on the mechanisms involved. Here, the authors compare species of Basidiomycete fungi and focus on analyzing developmental transcriptomes to identify patterns across species. Deep RNA-Seq data is generated for two species, P. ostreatus and Pt. gracilis, sampling different developmental stages. The authors report conflicting evidence for a "developmental hourglass" using a weighted transcription index vs gene age categories. There is substantial allele-specific expression in P. ostreatus, and these genes tend to have a more recent origin, have more divergent upstream regions and coding sequences, and are enriched for developmentally regulated transcripts. Antisense transcripts have low overlap with coding regions and low conservation, and a subset show a positive or negative correlation with the overlapping gene. Comparison to a species without complex multicellular development is used to further classify the developmental program.

Overall the new transcriptional data and extensive analysis provide a thorough view of the types of transcripts that appear differentially regulated, their age, and associated gene function enrichment. The gene sets identified from this analysis as well as the potential to re-analyze this data will be useful to the community studying multicellularity in fungi. The primary insights drawn in this study relate to the dating of the developmental transcriptome, however some patterns observed with young genes and noncoding transcripts are primarily reflective of expected patterns of evolutionary time.

We appreciate the Reviewer’s nice words on our ms, we think the revised version has substantial improvements in many aspects listed above.

Reviewer #3 (Public Review):

Fungi are unique in forming complex 3D multicellular reproductive structures from 2D mycelium filaments, a property used in this paper to study the genetic changes associated with the evolution of complex 3D multicellularity. The manuscript by Merenyi et al. investigates the evolution of gene expression and genome regulation during the formation of reproductive structures (fruiting bodies) in the Agaricomycetes lineage of Fungi. Transcriptome and multicellularity evolution are very exciting fundamental questions in biology that only become accessible with recent technological developments and the appropriate analysis framework. Important perspectives include understanding how genes acquire new functions and what role plays transcriptional regulation in adaptation. The study gathers a very useful dataset to this end, and relies on generally relevant hypotheses-driven analyses.

Analysis of fruiting body transcriptome in nine species revealed that prediction from the development hourglass model (that young genes are expressed in early and late but not intermediate phases of development) verified only in a few species, including Pleurotus ostreatus. An allele-specific expression (ASE) analysis in P. ostreatus showed that young genes frequently show ASE during fruiting body development. A comparative analysis with C. neoformans, which reproduces sexually without forming fruiting body, indicates that young and old (but not intermediate) genes are likely involved specifically in fruiting body morphogenesis. A number of underlying hypothesis could be presented better, and importantly the connection between the various analyses did not appear obvious to me. Some hypotheses and reasoning therefore need clarification. Some important results from the analyses are not provided and not commented, although they are required to fully meet the manuscript's objectives.

We appreciate the Reviewer’s suggestions and have revised the ms as explained below.

1. I do not clearly see the connection between the developmental hourglass model studied in the first part of the ms, and the allele-specific expression patterns in the second half of the ms. Which "phase" of the hourglass is expected to contain true CM-related genes (by contrast to general sexual processes)? Was P. ostreatus chosen for the ASE analysis because evidence for a developmental hourglass pattern was detected in this species? The conclusion that "evolutionary age predicts, to a large extent, the behaviour of a gene in the CM transcriptome" was established thanks to ASE in P. ostreatus, which was also found to be rather an exception for conforming to the hourglass model of developmental evolution. To what extent is this conclusion transferable to other Agaricomycete/fungal species?

We chose P. ostreatus because this is the only species for which the genomes of both parental strains (PC9 and PC15) are available. Although the hourglass concept is indeed a central hypothesis in animal developmental biology (though see recent critiques some (Piasecka et al 2013), our results suggest that it simply does not generally apply to fungal development. This may be due to the unique developmental mechanisms of fungi, or the independent origin(s) of CM in fungi. Our ms might have been misleading in this respect, in the revision we clarify that the ASE and hourglass analyses are independent of each other. Our interpretation of the hourglass results is that this model is not or hardly applicable for fungal development and the fact that P. ostreatus was the only species that in fact showed an hourglass did not drive our selection of this species. We inserted a note on this in the ms.

1. The authors acknowledge that fruiting body-expressed genes may relate either to CM or to more general sexual functions, and that disentangling these functions is a major challenge in their study. An overview of which gene was assigned to which function is not explicit in the ms (proposed to be described in a separate publication). Do these functional gene classes show distinct transcriptome evolution patterns (hourglass model, ASE...)?

We made accessible the complete list of CM-related genes and genes with more general sexual functions in Table S2/b-c. Due to length restrictions, we do not discuss many or each of these genes here, but provided gene ontology-based overviews (Fig 8/c-d, from lines 631). To answer the question whether CM vs shared genes show distinct transcriptomic patterns, we analyzed ASE, NATs and the hourglass model separately for CM-specific and shared genes. as follows:

-hourglass: We calculated and visualised the TAI for CM-specific and Shared gene sets of P. ostreatus separately. The average value of TAI decreased a lot in Shared genes possibly due to the overrepresentation of ancient genes here, but the patterns remained similar to the original, which imply that not simply one or the other gene set drives these patterns (Fig A3).

Fig A3: Transcriptome Age Index for CM-specific and Shared gene sets of P. ostreatus separately

-ASE: As we detailed in the ms, allele specific expression occurs mainly in young genes. Indeed, only 13.1% of ASE genes belong to the conserved gene sets (CMspecific: 200 and Shared: 144). Although there are more ASE genes (>2FC) among CM-specific genes, they are still underrepresented compared to young genes that are neither shared, nor CM-specific. This indicates that ASE is generally a feature of non-conserved genes and is not particularly characteristic for either conserved or CM-specific genes.

-NAT: We found that 17.3% of CM-specific (141 genes) and 18.3% of Shared genes (165 genes) overlap with antisense transcripts. Since these numbers don't differ substantially from 17.6%, which is the proportion of NATs corresponding to all protein coding genes, it implies an independent occurrence between NATs and these gene conservation groups.

3.) As far as I understand, major functions of the fruiting body transcriptome are either CM or general sexual functions. Could these genes, notably those showing ASE, play a role in general processes other than sexual development (hyphal growth, environment sensing, cell homeostasis, pathogenicity)?

Certainly, ASE might also occur in genes related to these processes. However, the processes mentioned by the Reviewer are likely associated with very conserved genes (except pathogenicity, which we can’t examine here) and our results suggest that ASE is more typical of young genes that are under weak selection. We detected ASE in 931/343 (S2/S4 genes) genes expressed in the vegetative mycelium stage of P. ostreatus. We also note that by the definition of developmentally regulated genes, we do not expect very basic fungal processes, like hyphal growth to be among the functions of the genes we identified. Genes related to such basic (housekeeping) processes usually (exceptions exist) show flat expression profiles (because they are equally important in mycelia and all fruiting body stages) and will not be picked up by our pipelines for identifying shared developmentally regulated genes.

1. As stated by the authors, "the goal of this study was to systematically tease apart the components and driving forces of transcriptome evolution in CM fungi". What drives the interesting ASE pattern discovered however remains an open question at the end of the ms. The authors appropriately discuss that these patterns could be either adaptive or neutral but there is no direct evidence for any scenario in P. ostreatus. Is the expression of (some of) the young genes showing ASE required for CM? one or two case studies would allow providing support for such scenarios.

We respectfully disagree. We provide evidence that the driving force of ASE is promoter divergence (and consequently differential transcription factor binding) in genes in which it is tolerated (see conclusions, lines 708-712). Our results suggest that ASE is mostly a neutrally arising phenomenon. To get to the mechanistic bases of how promoter divergence can cause ASE (following the suggestion of Reviewer 1), we analysed putative, inferred transcription factor binding motifs in P. ostreatus and found that ASE genes had more divergence in putative TF binding sites. However, it is important to emphasise that all TF motifs we analyzed are inferred motifs and therefore these results are indicative at best.

Reviewer #4 (Public Review):

This work develops a comparative framework to test genes which support complex morphological structures and complex multicelluarity. This expands beyond simple gene sharing and phylogenomics by incorporating comparison of gene expression profiling of development of multicellular structures during sexual reproduction. This approach tests the hypothesis that genes underlying sexual reproductive structure formation are homologous and the molecular evolutionary processes that control transcriptome evolution which underlie complex multicellularity.

The approaches used are appropriate and employ modern comparative and transcriptome analyses to example allele specific expression, and evaluate an age of the evolutionary ages of genes. This work produced additional new RNAseq to examine developmental processes and combined it with existing published data to contrast fungi with either complex morphologies or yeast forms.

The strengths of work are well selected comparison organisms and efforts to have developmental stages which are appropriate comparisons.

We appreciate the Reviewer’s positive comments.

Weakness could be pointed to in how the NAT descriptions are interesting it isn't clear how they link directly to morphology variation or development. I am unclear if these are arising from new de novo promotors, are ferried by transposable elements, or if any other understanding of their genesis indicates they are more than very recent gains in a species for the most part and not part of any conserved developmental process (outside a few exemplars).

Originally, we assayed natural antisense transcripts (NAT) based on the assumption that they regulate developmental processes (e.g. Kim et al 2018 https://doi.org/10.1128/mBio.01292-18). Our analyses showed that although NATs are abundant in CM transcriptomes of fungi, they show no homology across species and so are unlikely to drive conserved developmental processes, which we are after in this ms. Rather, our data are compatible with most (but likely not all) NATs being transcriptional noise, arising from novel or random promoters. We therefore shortened this section and moved much of it to the Appendix 1.

The impact of this work will reside in how gene age intersects with variability and relative importance in CM. it will be interesting to see future work examine the functions of these genes and test how allele specific expression and specific alleles are contributing to the formation of these tissues and growth forms. I am still not sure if molecular mechanisms of how high variability in gene expression is still producing relatively uniform morphologies, or if it isn't quantification of morphological variation would be nice to link to whether ASE underlie that.

We agree that allele specific expression could influence morphologies significantly, but investigating that is beyond the scope of the current work (it would require a population genomics project). More direct evidence on allelic differences can be seen in monokaryon phenotypes, which only express one of the parental alleles. Phenotypic differences are obvious in the mycelium of the two parental monokaryons : the mycelium of PC9 is more fluffy and grows faster than that of PC15. This was reported recently by Lee et al 2021 (https://doi.org/10.1093/g3journal/jkaa008). We agree with the Reviewer that this is a very exciting future research direction.

To my read of the work, the authors achieved their goals and confirmed hypothesis about the age of genes and the variability of gene expression. I still feel there is some clarity lost in whether the findings across the large number of species compared here help inform predictions or classifications of types of genes which either have ASE or are implicated in CM. This is really work for the future as the authors have provided a detailed analysis and approach that can fuel further direction in this research area.

To address this issue we reworked the ms to make connections between ASE and CM clearer. Because ASE appears based on our results to (mostly) arise neutrally, predictions for other species are expected to be hard. On the other hand, we think we can make confident predictions on what types of genes are implicated in CM in other species, at least for conserved aspects of fruiting body development.

Author Response

Reviewer #1 (Public Review):

In this study, the authors set out to clarify the relationship between brain oscillations and different levels of speech (syllables, words, phrases) using MEG. They presented word lists and sentences and used task instructions to attempt to focus listeners' attention on different levels of linguistic analysis (syllables, words, phrases).

1) I came away with mixed feelings about the task design: following each stimulus (sentence or word list), participants were asked to (a) press a button (i.e. nothing related to what they heard, (b) indicate which of two syllables was heard, (c) indicate which of two words was heard, (d) indicate which pair of words was present in the correct order. This task is the critical manipulation in the study, as it is intended to encourage (or in the authors' words, "require") participants to focus on different timescales of speech (syllable, word, and phrase, respectively). I very much like the idea of keeping the physical stimuli unchanged, and manipulating attention through task demands - an elegant and effective approach. At the same time, I have reservations about the degree to which these task instructions altered attention during listening. My intuition is that, if I were a participant, I would just listen attentively, and then answer the question about the specific level. For example, I don't know that knowing I would be doing a "word pair" task, I would be attending at a slower rate than a "word" task, as in both cases I would be motivated to understand all of the words in the sentence. I fully acknowledge my introspection (n=1) may be flawed here, but nevertheless, any additional support validating the effect of these instructions would help the interpretation of the MEG results.

The reviewer points out that to do any task on sentences (such as a word task and a syllable task) participants’ strategy could be to understand the full meaning of the sentence and infer the lower level properties based on the understanding of the full sentence. We fully share this introspection, which would suggest that extracting sentence meaning is partly automatic (or at least a default mode of processing) and independent of the behavioral relevance. While the reviewer sees this as a downside of the design, this is part of what our study tried to disentangle (automatic versus task-dependent processing at lower frequency time-scales). If, as the reviewer points out, all processing of sentences would be automatic we should not find any effect of task (as the task should not affect the tracking response at all). We found that overall the tracking response is robust to task-induced manipulation of attention – the main effect that MI to phrases is higher for sentences than for word lists is robust across passive and task conditions. But that is not the whole story on the source level, where we do find some task effects, which indicates that task instructions do matter. This means that participants changed their strategy depending on the instructions, but that overall, tracking of linguistic structures such as phrases is automatic. We show that for the IFG MI phrasal time scales are tracked stronger during the phrase task versus the other tasks. This is also reflected in stronger STG-IFG connectivity during the phrasal versus passive task. These results speak against the interpretation of the reviewer that “task instructions“ do not “ altered attention during listening”. While there are these subtle task differences, especially in IFG, overall our findings do speak for an automatic tracking of phrasal rate structure in sentences independent of task. We therefore concluded that “automatic understanding of linguistic information, and all the processing that this entails, cannot be countered to substantially change the consequences for neural readout, even when explicitly instructing participants to pay attention to particular time-scales” (line 548-549).

The analysis steps generally seem sensible and well-suited to answering the main claims of the study. Controlling for power differences between conditions through matching was a nice feature.

2) I had a concern about accuracy differences (as seen in Figure 1) across stimulus materials and tasks. In particular, for the phrase task, participants were more accurate for sentence stimuli than word list stimuli. I think this makes a lot of sense, as a coherent sentence will be easier to remember in order than a list of words. But, I did not see accuracy taken into account in any of the analyses. These behavioral differences raise the possibility that the MEG results related to the sentence > word list contrast in phrases (which seems one of the most interesting findings in IFG) simply reflect differences in accuracy.

With the caveat of the concern regarding accuracy differences, the research goals were clear and the conclusions were generally supported by the analyses.

Thank you for pointing this out. We have now taken accuracy into account in our analysis. It did not change any of our main findings or conclusions, and strengthened the argument that tracking of phrases in sentences vs. word lists is stronger. The influence of task difficulty is a relevant point to investigate (also see point 1 of reviewer 2 and point 4 of reviewer 3). To do so we added accuracy (per participant per condition) as a factor in the mixed model (as well as all interactions with task and condition) for the MI, power, and connectivity analyses at the phrasal rate/delta band. Note that as for the passive task there is no accuracy, we removed the passive task from the analyses. We could also only run models with random intercepts (not random slopes), due to the reduced number of degrees of freedom when adding the factor accuracy to the models.

For the MI analysis we only found an effect in MTG. Specifically, there was a three-way interaction between task, condition and accuracy (F(2, 91.9) = 3.4591, p = 0.036). To follow up on this three-way interaction we split the data per task. The condition*accuracy interaction was only (uncorrected) significant for the word combination task (F(1,24.8) = 5.296, p = 0.03 (uncorrected)) and not for any other task (p>0.1). In the word combination task, we found that the difference between sentences and word lists was the strongest at high accuracies (see below figure the predicted values of the model). One way to interpret this finding is that stronger phrasal-rate MI tracking in MTG promotes phrasal-rate processing (as indicated by accuracy) more in sentences than in word lists.

MEG – behavioral performance relation. A) Predicted values for the phrasal band MI in the MTG for the word combination task separately for the two conditions. B) Predicted values for the delta band WPLI in the STG-MTG connection separately for the two conditions. Error bars indicate the 95% confidence interval of the fit. Colored lines at the bottom indicate individual datapoints.

For power we did not find any effect of accuracy. For the connectivity analysis we found in the STG-MTG connectivity a significant conditionaccuracy interaction (F(1, 80.23)=5.19, p = 0.025). The conditionaccuracy interaction showed that lower accuracies were generally associated with stronger differences between the sentences and word lists (see figure; the opposite of the MI analysis). Thus, functional connections in the delta band are stronger during sentence processing when participants have difficulty with the task (independent of the task performed). This could indicate that low-frequency connections are more relevant for the sentence than the word list condition (as the reviewer also indicated in point 1).

After correcting for accuracy there was also a significant task condition interaction (F(2,80.01) = 3.348, p = 0.040) and a main effect of condition (F(1,80.361) = 5.809, p = 0.018). While overall there was a stronger WPLI for the sentence compared to the word list condition, the interaction seemed to indicate that this was especially the case during the word task (p = 0.005 corrected), but not for the other tasks (p>0.1).

We added the results of the accuracy analyses in the main manuscript as well as adding a dedicated section in our discussion section (page 21-22). Adding accuracy did not remove any of the effects we report in the original analyses. Therefore, none of these finding change the interpretation of the results as the task still had an influence on the MI responses of MTG and IFG. The effect of accuracy in the MTG refined the results showing that the effect was strongest there for participants with high accuracies. This relationship suggests a functional role of tracking through phase alignment for understanding phrasal structure.

The methods now read: “MEG-behavioural performance analysis: To investigate the relation between the MEG measures and the behavioural performance we repeated the analyses (MI, power, and connectivity) but added accuracy as a factor (together with the interactions with the task and condition factor). As there is no accuracy for the passive task, we removed this task from the analysis. We then followed the same analyse steps as before. Since we reduced our degree of freedom, we could however only create random intercept and not random slope models”.

The results now read: “MEG-behavioural performance relation. We found for the MI analysis a significant effect of accuracy only in the MTG. Here, we found a three-way interaction between accuracy task condition (F(2, 91.9) = 3.459, p = 0.036). Splitting up for the three different tasks we found only an uncorrected significant effect for the condition accuracy interaction for the phrasal task (F(1, 24.8) = 5.296, p = 0.03) and not for the other two tasks (p>0.1). In the phrasal task, we found that when accuracy was high, there was a stronger difference between the sentence and the word list condition compared to when accuracy was low, with stronger accuracy for the sentence condition (Figure 7A).

No relation between accuracy and power was found. For the connectivity analysis we found a significant condition accuracy interaction for the STG-MTG connection (F(1,80.23) = 5.19, p = 0.025; Figure 7B). Independent of task, when accuracy was low the difference between sentence and word lists was stronger with higher WPLI fits for the sentence condition. After correcting for accuracy there was also a significant task condition interaction (F(2,80.01) = 3.348, p = 0.040) and a main effect of condition (F(1,80.361) = 5.809, p = 0.018). While overall there was a stronger WPLI for the sentence compared to the word list condition, the interaction seemed to indicate that this was especially the case during the word task (p = 0.005), but not for the other tasks (p>0.1).”

The discussion now reads: “We found that across participants both the MI and the connectivity in temporal cortex influenced behavioural performance. Specifically, MTG-STG connections were, independent of task, related to accuracy. There was higher connectivity between MTG and STG for sentences compared to word lists at low accuracies. At high accuracies, we found that stronger MTG tracking at phrasal rates (measured with MI) for sentences compared to word lists during the word combination task. These results suggest that indeed tracking of phrasal structure in MTG is relevant to understand sentences compared to word lists. This was reflected in a general increase in delta connectivity differences when the task was difficult (Figure 7B). Participants might compensate for the difficulty using phrasal structure present in the sentence condition. When phrasal structure in sentences are accurately tracked (as measured with MI) performance is better when these rates are relevant (Figure 7A). These results point to a role for phrasal tracking for accurately understanding the higher order linguistic structure in sentences even though more research is needed to verify this. It is evident that the connectivity and tracking correlations to behaviour do not explain all variation in the behavioural performance (compare Figure 1 with 3). Plainly, temporal tracking does not explain everything in language processing. Besides tracking there are many other components important for our designated tasks, such as memory load and semantic context which are not captured by our current analyses.”

Reviewer #2 (Public Review):

In a MEG study, the authors investigate as their main question whether neural tracking at the phrasal time scale reflects linguistic structure building (testing different conditions: sentences vs. word-lists) or an attentional focus on the phrasal time scale (testing different tasks, passive listening, syllable task, word task, word combination/phrasal scale task). They perform the following analyses at brain areas (ROIs: STG, IFG, MTG) of the language network: (1) Mutual information (MI) between the acoustic envelope and the delta band neuronal signals is analyzed. (2) Power in the delta band is analyzed. (3) Connectivity is analyzed using debiased WPLI. For all analyses, linear mixed-models are separately conducted for each ROI. The main finding is that the sentence compared to the word-list condition is more strongly tracked at the phrasal scale (MI). In STG the effect was task-independent; in MTG the effect only occurred for active tasks; and in IFG additionally, the word-combining/phrasal scale task resulted in higher tracking compared to all other tasks. The authors conclude that phrasal scale neural tracking reflects linguistic processing which takes place automatically, while task-related attention contributes additionally at IFG (interpreted as combinatorial hub involved in language and non-language processing). The findings are stable when power differences are controlled. The connectivity analysis showed increased connectivity in the delta band (phrasal time scale) between IFG-STG in the phrasal-scale compared to the passive task (adding to the IFG MI findings). (Additionally, they separately analyze neural tracking at the syllabic and word time scale, which however is not in the main focus).

Major strength/weaknesses of the methods and results:

1) A major strength of the results is that part of them replicate the authors' earlier findings (i.e. higher tracking at the phrasal time scale for sentences compared to word-lists; Kaufeld et al., 2020), while they complement this earlier work by showing that the effects are due to linguistic processing and not to an attentional focus on the phrasal time scale due to the task (at least in STG and MTG; while the task plays a role for the IFG tracking). Another strength is that a power control analysis is applied, which allows excluding spurious results due to condition differences in power. A weakness of the method is that analyses were applied separately per ROI, and combined across correct/incorrect trials (if I understood correctly), no trial-based analysis was conducted (which is related to how MI is computed). Furthermore, several methodological details could be clarified in the manuscript.

The authors achieved their aims by providing evidence that neuronal tracking at the phrasal time scale in STG and MTG depends on the presence of linguistic information at this scale rather than indicating an attentional focus on this time scale due to a specific task. Their results support the conclusion. Results would be strengthened by showing that these effects are not impacted by different amounts of correct/incorrect trials across conditions (if I understood that correctly).

We thank the reviewer for her comments. It is correct that we collapsed across the correct and incorrect trials. This had various reasons (also see point 2 and 9 of reviewer 1 and point 4 of reviewer 3). First, our tasks function solely to direct participants’ attention to the various linguistic representations (syllables, words, phrases) and the timescales that they occur on. The three tasks are in a sense more control tasks to study the tracking response, and manipulate attention as tracking during spoken language comprehension occurs, rather than a case where the neural response to the tasks is itself to be studied. For example, in a typical working memory paradigm, it is only during correct trials that the relevant cognitive process occurs. In contrast, in our paradigm, it is likely that that spoken stimuli are heard and processing, in other words, sentence comprehension and word list perception occur, even during incorrect trials in the syllable condition. As such, we do not expect MI tracking responses to explain the behavioral data. However, we agree it is crucially important to show that MI differences are not a function of task performance differences.

Second, there are clear differences in difficulty level of the trials within conditions. For example, if the target question was related to the last part of the audio fragment, the task was much easier than when it was at the beginning of the audio fragment. In the syllable task, if syllables also were (by chance) a part-word, the trial was also much easier. If we were to split up in correct and incorrect we would not really infer solely processes due to accurately processing the speech fragments, but also confounded the analysis by the individual difficulty level of the trials.

To acknowledge this, we added this limitation to the methods. The methods now reads: “Note that different trials within a task were not matched for task difficulty. For example, in the syllable task syllables that make a word are much easier to recognize than syllables that do not make a word. Additionally, trials pertaining to the beginning of the sentence are more difficult than ones related to the end of the sentence due to recency effects.”.

To still investigate if overall accuracy influenced the results we did add accuracy (across participants) to the mixed models. Note that as for the passive task there is no accuracy, we removed the passive task from the analyses. We could also only run models with random intercepts (not random slopes), due to the reduced number of degrees of freedom when adding the factor accuracy to the models.

For the MI analysis we only found an effect in MTG. Specifically, there was a three-way interaction between task, condition and accuracy (F(2, 91.9) = 3.4591, p = 0.036). To follow up on this three-way interaction we split the data per task. The condition*accuracy interaction was only (uncorrected) significant for the word combination task (F(1,24.8) = 5.296, p = 0.03 (uncorrected)) and not for any other task (p>0.1). In the word combination task, we found that the difference between sentences and word lists was the strongest at high accuracies (see on the right attached figure the predicted values of the model). One way to interpret this finding is that stronger phrasal-rate MI tracking in MTG promotes phrasal-rate processing (as indicated by accuracy) more in sentences than in word lists.

For power we did not find any effect of accuracy. For the connectivity analysis we found in the STG-MTG connectivity a significant conditionaccuracy interaction (F(1, 80.23)=5.19, p = 0.025). The conditionaccuracy interaction showed that lower accuracies were generally associated with stronger differences between the sentences and word lists (see figure below; the opposite of the MI analysis). Thus, functional connections in the delta band are stronger during sentence processing when participants have difficulty with the task (independent of the task performed). This could indicate that low-frequency connections are more relevant for the sentence than the word list condition.

MEG – behavioral performance relation. A) Predicted values for the phrasal band MI in the MTG for the word combination task separately for the two conditions. B) Predicted values for the delta band WPLI in the STG-MTG connection separately for the two conditions. Error bars indicate the 95% confidence interval of the fit. Colored lines at the bottom indicate individual datapoints.

After correcting for accuracy there was also a significant task*condition interaction (F(2,80.01) = 3.348, p = 0.040) and a main effect of condition (F(1,80.361) = 5.809, p = 0.018). While overall there was a stronger WPLI for the sentence compared to the word list condition, the interaction seemed to indicate that this was especially the case during the word task (p = 0.005 corrected), but not for the other tasks (p>0.1).

We added the results of the accuracy analyses in the main manuscript as well as adding a dedicated section in our discussion section (page 21-22). Adding accuracy did not remove any of the effects we report in the original analyses. Therefore, none of these finding change the interpretation of the results as the task still had an influence on the MI responses of MTG and IFG. The effect of accuracy in the MTG refined the results showing that the effect was strongest there for participants with high accuracies. This relationship suggests a functional role of tracking through phase alignment for understanding phrasal structure.

The methods now read: “MEG-behavioural performance analysis: To investigate the relation between the MEG measures and the behavioural performance we repeated the analyses (MI, power, and connectivity) but added accuracy as a factor (together with the interactions with the task and condition factor). As there is no accuracy for the passive task, we removed this task from the analysis. We then followed the same analyse steps as before. Since we reduced our degree of freedom, we could however only create random intercept and not random slope models”.

The results now read: “MEG-behavioural performance relation. We found for the MI analysis a significant effect of accuracy only in the MTG. Here, we found a three-way interaction between accuracytaskcondition (F(2, 91.9) = 3.459, p = 0.036). Splitting up for the three different tasks we found only an uncorrected significant effect for the condition*accuracy interaction for the phrasal task (F(1, 24.8) = 5.296, p = 0.03) and not for the other two tasks (p>0.1). In the phrasal task, we found that when accuracy was high, there was a stronger difference between the sentence and the word list condition compared to when accuracy was low, with stronger accuracy for the sentence condition (Figure 7A).

No relation between accuracy and power was found. For the connectivity analysis we found a significant conditionaccuracy interaction for the STG-MTG connection (F(1,80.23) = 5.19, p = 0.025; Figure 7B). Independent of task, when accuracy was low the difference between sentence and word lists was stronger with higher WPLI fits for the sentence condition. After correcting for accuracy there was also a significant taskcondition interaction (F(2,80.01) = 3.348, p = 0.040) and a main effect of condition (F(1,80.361) = 5.809, p = 0.018). While overall there was a stronger WPLI for the sentence compared to the word list condition, the interaction seemed to indicate that this was especially the case during the word task (p = 0.005), but not for the other tasks (p>0.1).”

The discussion now reads: “We found that across participants both the MI and the connectivity in temporal cortex influenced behavioural performance. Specifically, MTG-STG connections were, independent of task, related to accuracy. There was higher connectivity between MTG and STG for sentences compared to word lists at low accuracies. At high accuracies, we found that stronger MTG tracking at phrasal rates (measured with MI) for sentences compared to word lists during the word combination task. These results suggest that indeed tracking of phrasal structure in MTG is relevant to understand sentences compared to word lists. This was reflected in a general increase in delta connectivity differences when the task was difficult (Figure 7B). Participants might compensate for the difficulty using phrasal structure present in the sentence condition. When phrasal structure in sentences are accurately tracked (as measured with MI) performance is better when these rates are relevant (Figure 7A). These results point to a role for phrasal tracking for accurately understanding the higher order linguistic structure in sentences even though more research is needed to verify this. It is evident that the connectivity and tracking correlations to behaviour do not explain all variation in the behavioural performance (compare Figure 1 with 3). Plainly, temporal tracking does not explain everything in language processing. Besides tracking there are many other components important for our designated tasks, such as memory load and semantic context which are not captured by our current analyses.”

The findings are an important contribution to the ongoing debate in the field whether neuronal tracking at the phrasal time scale indicates linguistic structure processing or more general processes (e.g. chunking).

Reviewer #3 (Public Review):

This manuscript presents a MEG study aiming to investigate whether neural tracking of phrasal timescales depends on automatic language processing or specific tasks related to temporal attention. The authors collected MEG data of 20 participants as they listened to naturally spoken sentences or word lists during four different tasks (passive listening vs. syllable task vs. word tasks vs. phrase task). Based on mutual information and Connectivity analysis, the authors found that (1) neural tracking at the phrasal band (0.8-1.1 Hz) was significantly stronger for the sentence condition compared to the word list condition across the classical language network, i.e., STG, MTG, and IFG; (2) neural tracking at the phrasal band was (at least tend significantly) stronger for phrase task than other tasks in the IFG; (3) the IFG-STG connectivity was increased in the delta-band for the phrase task. Ultimately, the authors concluded that neural tracking of phrasal timescales relied on both automatic language processing and specific tasks.

Overall, this study is trying to tackle an interesting question related to the contributing factors for neural tracking of linguistic structures. The study procedure and analyses are well executed, and the conclusions of this paper are mostly well supported by data. However, I do have several major concerns.

1. The title of the manuscript uses the description "tracking of hierarchical linguistic structure". In general, hierarchical linguistic structures involve multiple linguistic units with different timescales, such as syllables, words, phrases, and sentences. In this study, however, the main analysis only focused on the phrasal band (0.8-1.1 Hz). It seemed that there was no significant stimulus- or task-effect on the word band or syllabic band (supplementary figures). Therefore, it is highly recommended that the authors modify the related descriptions, or explain why neural tracking of phrases can represent neural tracking of hierarchical linguistic structures in the current study.

We thank the reviewer for this comment. We meant to refer to the task manipulation directing attention to different levels of representation across the linguistic hierarchy. We have changed the title to “Neural tracking of phrases during spoken language comprehension is automatic and task-dependent.” We hope this resolves any inadvertent confusion we created. Furthermore, throughout the manuscript we ensure to talk about effect occurring for phrasal tracking at low frequency bands at not across any hierarchical linguistic structure. We agree that our findings cannot speak for any task-dependent effects along the hierarchy, only that at the phrasal level there is a difference between sentences and word lists.

1. In Methods, the authors employed MI analyses on three frequency bands: 0.8-1.1 Hz for the phrasal band, 1.9-2.8 Hz for the word band, and 3.5-5.0 Hz for the syllabic band (line 191-192). As the timescales of linguistic units are various and overlapped in natural speech, I wonder how the authors define the boundaries of these frequency bands, and whether these bands are proper for the naturally spoken stimuli in the current study. These important details should be clarified.

The frequency bands of the MI analysis were based on the stimuli, or in other words, are data driven. They reflect the syllabic, word, and phrasal rates in our stimulus set (calculated in Kaufeld et al., 2020). They were calculated by annotating the sentences by syllables, words, and phrasal and converting the rate of the linguistic units to frequency ranges. The information has been added to the manuscript. We acknowledge that unlike our stimulus set in natural speech the boundaries of these bands can overlap and now also state this (“While in our stimulus set the boundaries of the linguistic levels did not overlap, in natural speech the brain has an even more difficult task as there is no one-to-one match between band and linguistic unit [26]”, line number 211-213).

1. What is missing in the manuscript are the explanations of the correlation between behavioral performance and neural tracking. In Results, the behavioral performance shows significant differences across the active tasks (Figure 1), but the MI differences across the tasks are relatively weak in IFG (Figure 3). In addition, the behavioral performance only shows significant differences between the sentence and word list conditions during the phrasal task, but the MI differences between the conditions are significant in MTG during the syllabic, word, and phrasal tasks. Explanations for these inconsistent results are expected.

We answer this point together with point 4 below where we analyze the behavioral performance and the MEG responses.

1. Since the behavioral performance of these active tasks is likely related to the temporal attention to relevant timescales of different linguistic units, I wonder whether there exist underlying neural correlates of behavioral performance (e.g., significant correlation between performance and mutual information). If so, it may be interesting and bring a new bright spot for the current study.

The influence of task difficulty is a relevant point to investigate (also see point 1 of reviewer 2 and point 4 of reviewer 3). To do so we added accuracy (per participant per condition) as a factor in the mixed model (as well as all interactions with task and condition) for the MI, power, and connectivity analyses at the phrasal rate/delta band. Note that as for the passive task there is no accuracy, we removed the passive task from the analyses. We could also only run models with random intercepts (not random slopes), due to the reduced number of degrees of freedom when adding the factor accuracy to the models.

For the MI analysis we only found an effect in MTG. Specifically, there was a three-way interaction between task, condition and accuracy (F(2, 91.9) = 3.4591, p = 0.036). To follow up on this three-way interaction we split the data per task. The condition*accuracy interaction was only (uncorrected) significant for the word combination task (F(1,24.8) = 5.296, p = 0.03 (uncorrected)) and not for any other task (p>0.1). In the word combination task, we found that the difference between sentences and word lists was the strongest at high accuracies (see the below figure the predicted values of the model). One way to interpret this finding is that stronger phrasal-rate MI tracking in MTG promotes phrasal-rate processing (as indicated by accuracy) more in sentences than in word lists.

MEG – behavioral performance relation. A) Predicted values for the phrasal band MI in the MTG for the word combination task separately for the two conditions. B) Predicted values for the delta band WPLI in the STG-MTG connection separately for the two conditions. Error bars indicate the 95% confidence interval of the fit. Colored lines at the bottom indicate individual datapoints.

For power we did not find any effect of accuracy. For the connectivity analysis we found in the STG-MTG connectivity a significant conditionaccuracy interaction (F(1, 80.23)=5.19, p = 0.025). The conditionaccuracy interaction showed that lower accuracies were generally associated with stronger differences between the sentences and word lists (see figure attached; the opposite of the MI analysis). Thus, functional connections in the delta band are stronger during sentence processing when participants have difficulty with the task (independent of the task performed). This could indicate that low-frequency connections are more relevant for the sentence than the word list condition.

After correcting for accuracy there was also a significant task*condition interaction (F(2,80.01) = 3.348, p = 0.040) and a main effect of condition (F(1,80.361) = 5.809, p = 0.018). While overall there was a stronger WPLI for the sentence compared to the word list condition, the interaction seemed to indicate that this was especially the case during the word task (p = 0.005 corrected), but not for the other tasks (p>0.1).

We added the results of the accuracy analyses in the main manuscript as well as adding a dedicated section in our discussion section (page 21-22). Adding accuracy did not remove any of the effects we report in the original analyses. Therefore, none of these finding change the interpretation of the results as the task still had an influence on the MI responses of MTG and IFG. The effect of accuracy in the MTG refined the results showing that the effect was strongest there for participants with high accuracies. This relationship suggests a functional role of tracking through phase alignment for understanding phrasal structure.

While the findings can explain some behavioral effects, we agree with the reviewer that the behavioral results and the MI results don’t align. We note that our use of tasks to guide attention to different timescales and linguistic representations differs from the use of, for example, a working memory task where only the correct trials contain the relevant cognitive process. In working memory type paradigms, the MEG data should indeed explain the behavioral response. Our study was designed to test for effects of task demands on the neural tracking response to speech and language. As we are only using the tasks to control attention, we do not attempt to explain behavior through the MEG data or differences in MI.

Thus, the phrasal tracking cannot explain all of the behavioral results (point 3). It is at this point unclear what could have caused this effect, but it quite likely that neural sources outside the speech and language ROIs we selected are in play. We discuss this now.

The methods now read: “MEG-behavioural performance analysis: To investigate the relation between the MEG measures and the behavioural performance we repeated the analyses (MI, power, and connectivity) but added accuracy as a factor (together with the interactions with the task and condition factor). As there is no accuracy for the passive task, we removed this task from the analysis. We then followed the same analyse steps as before. Since we reduced our degree of freedom, we could however only create random intercept and not random slope models”.

The results now read: “MEG-behavioural performance relation. We found for the MI analysis a significant effect of accuracy only in the MTG. Here, we found a three-way interaction between accuracytaskcondition (F(2, 91.9) = 3.459, p = 0.036). Splitting up for the three different tasks we found only an uncorrected significant effect for the condition*accuracy interaction for the phrasal task (F(1, 24.8) = 5.296, p = 0.03) and not for the other two tasks (p>0.1). In the phrasal task, we found that when accuracy was high, there was a stronger difference between the sentence and the word list condition compared to when accuracy was low, with stronger accuracy for the sentence condition (Figure 7A).

No relation between accuracy and power was found. For the connectivity analysis we found a significant conditionaccuracy interaction for the STG-MTG connection (F(1,80.23) = 5.19, p = 0.025; Figure 7B). Independent of task, when accuracy was low the difference between sentence and word lists was stronger with higher WPLI fits for the sentence condition. After correcting for accuracy there was also a significant taskcondition interaction (F(2,80.01) = 3.348, p = 0.040) and a main effect of condition (F(1,80.361) = 5.809, p = 0.018). While overall there was a stronger WPLI for the sentence compared to the word list condition, the interaction seemed to indicate that this was especially the case during the word task (p = 0.005), but not for the other tasks (p>0.1).”

The discussion now reads: “We found that across participants both the MI and the connectivity in temporal cortex influenced behavioural performance. Specifically, MTG-STG connections were, independent of task, related to accuracy. There was higher connectivity between MTG and STG for sentences compared to word lists at low accuracies. At high accuracies, we found that stronger MTG tracking at phrasal rates (measured with MI) for sentences compared to word lists during the word combination task. These results suggest that indeed tracking of phrasal structure in MTG is relevant to understand sentences compared to word lists. This was reflected in a general increase in delta connectivity differences when the task was difficult (Figure 7B). Participants might compensate for the difficulty using phrasal structure present in the sentence condition. When phrasal structure in sentences are accurately tracked (as measured with MI) performance is better when these rates are relevant (Figure 7A). These results point to a role for phrasal tracking for accurately understanding the higher order linguistic structure in sentences even though more research is needed to verify this. It is evident that the connectivity and tracking correlations to behaviour do not explain all variation in the behavioural performance (compare Figure 1 with 3). Plainly, temporal tracking does not explain everything in language processing. Besides tracking there are many other components important for our designated tasks, such as memory load and semantic context which are not captured by our current analyses.”

Author Response*

Reviewer #3 (Public Review):

AAA protein are involved in a variety of cellular activity. They all share the same structural fold and still they are all incredibly specialised. This study works towards the direction of understanding the unique specialisation of the AAA protein ATAD1. While the general mechanism of substrate threading by AAA proteins is by now fairly well-elucidated, it remains to describe and understand the finer structural protein details that make each specific AAA perform unfolding (threading) of certain substrate rather than others. Additionally, regulation and stabilisation of each AAA is also finely regulated by specific subdomain.

This work is definitively strong in addressing these two points for ATAD1.

The structural data are solid and the analysis of the pore loops residues and the role of a11 overall convincing.

1) The cell fluorescence microscopy assay is a very good tool for checking in the cell the hypothesis risen by analysing of the structure. However, the assay is currently only based on the localisation of the Gos28 substrate, which leaves open the possibility that ATAD1 a11 mutants will have a different phenotype on different substrates.

We agree with the reviewer that it would be interesting to test ATAD1’s activity on other known substrates. To do that, we picked Pex26, an established tail-anchored protein substrate of ATAD1. We stably expressed EGFP-Pex26 in ATAD1-/- cells and tested the effect of ATAD1 expression on Pex26 mislocalization. As shown in the figure below, we found that although the general trend observed for Gos28 also holds true for Pex26, the measured PCC values clearly have a bimodal distribution, with some cells showing the complete mislocalization (PCC = 1.0) of Pex26. One exciting possibility to explain this result is that Pex26 is important in peroxisome biogenesis. Once enough Pex26 is mislocalized to the mitochondria, peroxisomal biogenesis becomes impaired, thus causing less Pex26 to be correctly inserted. A partial impairment in Pex26 peroxisomal insertion in turn creates a vicious cycle that leads to the complete mislocalization of Pex26. It will be an interesting to follow up on the cause of this bimodal distribution, which, however, is beyond the scope of this paper.

*Quantification of live-cell imaging showing using the localization of EGFP-Pex26 as a readout. Mean Pearson correlation coefficient (PCC) values and the SEM between EGFP-Pex26 and the mitochondria when expressing the ATAD1 variants indicated. Individual cell PCC values are represented as a single dot. *

Author Response:

Reviewer #1 (Public Review):

[...] While the study is addressing an interesting topic, I also felt this manuscript was limited in novel findings to take away. Certainly the study clearly shows that substitution saturation is achieved at synonymous CpG sites. However, subsequent main analyses do not really show anything new: the depletion of segregating sites in functional versus neutral categories (Fig 2) has been extensively shown in the literature and polymorphism saturation is not a necessary condition for observing this pattern.

We agree with the reviewer that many of the points raised were appreciated previously and did not mean to convey another impression. Our aim was instead to highlight some unique opportunities provided by being at or very near saturation for mCpG transitions. In that regard, we note that although depletion of variation in functional categories is to be expected at any sample size, the selection strength that this depletion reflects is very different in samples that are far from saturated, where invariant sites span the entire spectrum from neutral to lethal. Consider the depletion per functional category relative to synonymous sites in the adjoining plot in a sample of 100k: ~40% of mCpG LOF sites do not have T mutations. From our Fig. 4 and b, it can be seen that these sites are associated with a much broader range of hs values than sites invariant at 780k, so that information about selection at an individual site is quite limited (indeed, in our p-value formulation, these sites would be assigned p≤0.35, see Fig. 1). Thus, only now can we really start to tease apart weakly deleterious mutations from strongly deleterious or even embryonic lethal mutations. This allows us to identify individual sites that are most likely to underlie pathogenic mutations and functional categories that harbor deleterious variation at the extreme end of the spectrum of possible selection coefficients. More generally, saturation is useful because it allows one to learn about selection with many fewer untested assumptions than previously feasible.

Similarly, the diminishing returns on sampling new variable sites has been shown in previous studies, for example the first "large" human datasets ca. 2012 (e.g. Fig 2 in Nelson et al. 2012, Science) have similar depictions as Figure 3B although with smaller sample sizes and different approaches (projection vs simulation in this study).

We agree completely: diminishing returns is expected on first principles from coalescent theory, which is why we cited a classic theory paper when making that point in the previous version of the manuscript. Nonetheless, the degree of saturation is an empirical question, since it depends on the unknown underlying demography of the recent past. In that regard, we note that Nelson et al. predict that at sample sizes of 400K chromosomes in Europeans, approximately 20% of all synonymous sites will be segregating at least one of three possible alleles, when the observed number is 29%. Regardless, not citing Nelson et al. 2012 was a clear oversight on our part, for which we apologize; we now cite it in that context and in mentioning the multiple merger coalescent.

There are some simulations presented in Fig 4, but this is more of a hypothetical representation of the site-specific DFE under simulation conditions roughly approximating human demography than formal inference on single sites. Again, these all describe the state of the field quite well, but I was disappointed by the lack of a novel finding derived from exploiting the mutation saturation properties at methylated CpG sites.

As noted above, in our view, the novelty of our results lies in their leveraging saturation in order to identify sites under extremely strong selection and make inferences about selection without the need to rely on strong, untested assumptions.

However, we note that Fig 4 is not simply a hypothetical representation, in that it shows the inferred DFE for single mCpG sites for a fixed mutation rate and given a plausible demographic model, given data summarized in terms of three ranges of allele frequency (i.e., = 0, between 1 and 10 copies, or above 10 copies). One could estimate a DFE across all sites from those summaries of the data (i.e., from the proportion of mCpG sites in each of the three frequency categories), by weighting the three densities in Fig 4 by those proportions. That is, in fact, what is done in a recent preprint by Dukler et al. (2021, BioRxiv): they infer the DFE from two summaries of the allele frequency spectrum (in bins of sites), the proportion of invariant sites and the proportion of alleles at 1-70 copies, in a sample of 70K chromosomes.

To illustrate how something similar could be done with Fig. 4 based on individual sites, we obtain an estimate of the DFE for LOF mutations (shown in Panel B and D for two different prior distributions on hs) by weighting the posterior densities in Panel A by the fraction of LOF mutations that are segregating (73% at 780K; 9% at 15K) and invariant (27% and 91% respectively); in panel C, we show the same for a different choice of prior. For the smaller sample size considered, the posterior distribution recapitulates the prior, because there is little information about selection in whether a site is observed to be segregating or invariant, and particularly about strong selection. In the sample of 780K, there is much more information about selection in a site being invariant and therefore, there is a shift towards stronger selection coefficients for LOF mutations regardless of the prior.

Our goal was to highlight these points rather than infer a DFE using these two summaries, which throw out much of the information in the data (i.e., the allele frequency differences among segregating sites). In that regard, we note that the DFE inference would be improved by using the allele frequency at each of 1.1 million individual mCpG sites in the exome. We outline this next step in the Discussion but believe it is beyond the scope of our paper, as it is a project in itself – in particular it would require careful attention to robustness with regard to both the demographic model (and its impact on multiple hits), biased gene conversion and variability in mutation rates among mCpG sites. We now make these points explicitly in the Outlook.

Similarly, I felt the authors posed a very important point about limitations of DFE inference methods in the Introduction but ended up not really providing any new insights into this problem. The authors argue (rightly so) that currently available DFE estimates are limited by both the sparsity of polymorphisms and limited flexibility in parametric forms of the DFE. However, the nonsynonymous human DFE estimates in the literature appear to be surprisingly robust to sample size: older estimates (Eyre-Walker et al. 2006 Genetics, Boyko et al. 2008 PLOS Genetics) seem to at least be somewhat consistent with newer estimates (assuming the same mutation rate) from samples that are orders of magnitude larger (Kim et al. 2017 Genetics).

We are not quite sure what the reviewer has in mind by “somewhat consistent,” as Boyko et al. estimate that 35% of non-synonymous mutations have s>10^-2 while Kim et al. find that proportion to be “0.38–0.84 fold lower” than the Boyko et al. estimate (see, e.g., Fig. 4 in Kim et al., 2017). Moreover, the preprint by Dukler et al. mentioned above, which infers the DFE based on ~70K chromosomes, finds estimates inconsistent with those of Kim et al. (see SOM Table 2 and SOM Figure S5 in Dukler et al., 2021).

More generally, given that even 70K chromosomes carry little information about much of the distribution of selection coefficients (see our Fig. 4), we expect that studies based on relatively sample sizes will basically recover something close to their prior; therefore, they should agree when they use the same or similar parametric forms for the distribution of selection coefficients and disagree otherwise. The dependence on that choice is nicely illustrated in Kim et al., who consider different choices and then perform inference on the same data set and with the same fixed mutation rate for exomes; depending on their choice anywhere between 5%-28% of non-synonymous changes are inferred to be under strong selection with s>=10^-2 (see their Table S4).

Whether a DFE inferred under polymorphism saturation conditions with different methods is different, and how it is different, is an issue of broad and immediate relevance to all those conducting population genomic simulations involving purifying selection. The analyses presented as Fig 4A and 4B kind of show this, but they are more a demonstration of what information one might have at 1M+ sample sizes rather than an analysis of whether genome-wide nonsynonymous DFE estimates are accurate. In other words, this manuscript makes it clear that a problem exists, that it is a fundamental and important problem in population genetics, and that with modern datasets we are now poised to start addressing this problem with some types of sites, but all of this is already very well-appreciated except for perhaps the last point.

At least a crude analysis to directly compare the nonsynonymous genome-wide DFE from smaller samples to the 780K sample would be helpful, but it should be noted that these kinds of analyses could be well beyond the scope of the current manuscript. For example, if methylated nonsynonymous CpG sites are under a different level of constraint than other nonsynonymous sites (Fig. S14) then comparing results to a genome-wide nonsynonymous DFE might not make sense and any new analysis would have to try and infer a DFE independently from synonymous/nonsynonymous methylated CpG sites.

We are not sure what would be learned from this comparison, given that Figure 4 shows that, at least with an uninformative prior, there is little information about the true DFE in samples, even of tens of thousands of individuals. Thus, if some of the genome-wide nonsynonymous DFE estimates based on small sample sizes turn out to be accurate, it will be because the guess about the parametric shape of the DFE was an inspired one. In our view, that is certainly possible but not likely, given that the shape of the DFE is precisely what the field has been aiming to learn and, we would argue, what we are now finally in a position to do for CpG mutations in humans.

Reviewer #2 (Public Review):

This manuscript presents a simple and elegant argument that neutrally evolving CpG sites are now mutationally saturated, with each having a 99% probability of containing variation in modern datasets containing hundreds of thousands of exomes. The authors make a compelling argument that for CpG sites where mutations would create genic stop codons or impair DNA binding, about 20% of such mutations are strongly deleterious (likely impairing fitness by 5% or more). Although it is not especially novel to make such statements about the selective constraint acting on large classes of sites, the more novel aspect of this work is the strong site-by-site prediction it makes that most individual sites without variation in UK Biobank are likely to be under strong selection.

The authors rightly point out that since 99% of neutrally evolving CpG sites contain variation in the data they are looking at, a CpG site without variation is likely evolving under constraint with a p value significance of 0.01. However, a weakness of their argument is that they do not discuss the associated multiple testing problem-in other words, how likely is it that a given non synonymous CpG site is devoid of variation but actually not under strong selection? Since one of the most novel and useful deliverables of this paper is single-base-pair-resolution predictions about which sites are under selection, such a multiple testing correction would provide important "error bars" for evaluating how likely it is that an individual CpG site is actually constrained, not just the proportion of constrained sites within a particular functional category.

We thank the reviewer for pointing this out. One way to think about this problem might be in terms of false discovery rates, in which case the FDR would be 16% across all non-synonymous mCpG sites that are invariant in current samples, and ~4% for the subset of those sites where mutations lead to loss-of-function of genes.

Another way to address this issue, which we had included but not emphasized previously, is by examining how one’s beliefs about selection should be updated after observing a site to be invariant (i.e., using Bayes odds). At current sample sizes and assuming our uninformative prior, for a non-synonymous mCpG site that does not have a C>T mutation, the Bayes odds are 15:1 in favor of hs>0.5x10^-3; thus the chance that such a site is not under strong selection is 1/16, given our prior and demographic model. These two approaches (FDR and Bayes odds) are based on somewhat distinct assumptions.

We have now added and/or emphasized these two points in the main text.

The paper provides a comparison of their functional predictions to CADD scores, an older machine-learning-based attempt at identifying site by site constraint at single base pair resolution. While this section is useful and informative, I would have liked to see a discussion of the degree to which the comparison might be circular due to CADD's reliance on information about which sites are and are not variable. I had trouble assessing this for myself given that CADD appears to have used genetic variation data available a few years ago, but obviously did not use the biobank scale datasets that were not available when that work was published.

We apologize for the lack of clarity in the presentation. We meant to emphasize that de novo mutation rates vary across CADD deciles when considering all CpG sites (Fig. 2-figure supplement 5c), which confounds CADD precisely because it is based in part on which sites are variable. We have edited the manuscript to clarify this.

Reading this paper left me excited about the possibility of examining individual invariant CpG sites and deducing how many of them are already associated with known disease phenotypes. I believe the paper does not mention how many of these invariant sites appear in Clinvar or in databases of patients with known developmental disorders, and I wondered how close to saturation disease gene databases might be given that individuals with developmental disorders are much more likely to have their exomes sequenced compared to healthy individuals. One could imagine some such analyses being relatively low hanging fruit that could strengthen the current paper, but the authors also make several reference to a companion paper in preparation that deals more directly with the problem of assessing clinical variant significance. This is a reasonable strategy, but it does give the discussion section of the paper somewhat of a "to be continued" feel.

We apologize for the confusion that arose from our references to a second manuscript in prep. The companion paper is not a continuation of the current manuscript: it contains an analysis of fitness and pathogenic effects of loss-of-function variation in human exomes.

Following the reviewer’s suggestion to address the clinical significance of our results, we have now examined the relationship of mCpG sites invariant in current samples with Clinvar variants. We find that of the approximately 59,000 non-synonymous mCpG sites that are invariant, only ~3.6% overlap with C>T variants associated with at least one disease and classified as likely pathogenic in Clinvar (~5.8% if we include those classified as uncertain or with conflicting evidence as pathogenic). Approximately 2% of invariant mCpGs have C>T mutations in what is, to our knowledge, the largest collection of de novo variants ascertained in ~35,000 individuals with developmental disorders (DDD, Kaplanis et al. 2020). At the level of genes, of the 10k genes that have at least one invariant non-synonymous mCpG, only 8% (11% including uncertain variants) have any non-synonymous hits in Clinvar, and ~8% in DDD. We think it highly unlikely that the large number of remaining invariant sites are not seen with mutations in these databases because such mutations are lethal; rather it seems to us to be the case that these disease databases are far from saturation as they contain variants from a relatively small number of individuals, are subject to various ascertainment biases both at the variant level and at the individual level, and only contain data for a small subset of existing severe diseases.

With a view to assessing clinical relevance however, we can ask a related question, namely how informative being invariant in a sample of 780k is about pathogenicity in Clinvar. Although the relationship between selection and pathogenicity is far from straightforward, being an invariant non-synonymous mCpG in current samples not only substantially increases (15-10fold) the odds of hs > 0.5x10-3 (see Fig. 4b), it also increases the odds of being classified as pathogenic vs. benign in Clinvar 8-51 fold. In the DDD sample, we don’t know which variants are pathogenic; however, if we consider non-synonymous mutations that occur in consensus DDD genes as pathogenic (a standard diagnostic criterion), being invariant increases the odds of being classified as pathogenic 6-fold. We caution that both Clinvar classifications and the identification of consensus genes in DDD relies in part on whether a site is segregating in datasets like ExAC, so this exercise is somewhat circular. Nonetheless it illustrates that there is some information about clinical importance in mCpG sites that are invariant in current samples, and that the degree of enrichment (6 to 51-fold) is very roughly on par with the Bayes odds that we estimate of strong selection conditional on a site being invariant. We have added these findings to the main text and added the plot as Supplementary Figure 13.

Reviewer #3 (Public Review):

[...] The authors emphasize several times how important an accurate demographic model is. While we may be close to a solid demographic model for humans, this is certainly not the case for many other organisms. Yet we are not far off from sufficient sample sizes in a number of species to begin to reach saturation. I found myself wondering how different the results/inference would be under a different model of human demographic history. Though likely the results would be supplemental, it would be nice in the main text to be able to say something about whether results are qualitatively different under a somewhat different published model.

We had previously examined the effect of a few demographic scenarios with large increases in population size towards the present on the average length of the genealogy of a sample (and hence the expected number of mutations at a site) in Figure 3-figure supplement 1b, but without quantifying the effect on our selection inference. Following this suggestion, we now consider a widely used model of human demography inferred from a relatively small sample, and therefore not powered to detect the huge increase in population size towards the present (Tennessen et al. 2012). Using this model, we find a poor fit to the proportion of segregating CpG sites (the observed fraction is 99% in 780k exomes, when the model predicts 49%). Also, as expected, inferences about selection depend on the accuracy of the demographic model (as can be seen by comparing panel B to Fig 4B in the main text).

On a similar note, while a fixed hs simplifies much of the analysis, I wondered how results would differ for 1) completely recessive mutations and 2) under a distribution of dominance coefficients, especially one in which the most deleterious alleles were more recessive. Again, though I think it would strengthen the manuscript by no means do I feel this is a necessary addition, though some discussion of variation in dominance would be an easy and helpful add.

There's some discussion of population structure, but I also found myself wondering about GxE. That is, another reason a variant might be segregating is that it's conditionally neutral in some populations and only deleterious in a subset. I think no analysis to be done here, but perhaps some discussion?

We agree that our analysis ignores the possibilities of complete recessivity in fitness (h=0) as well as more complicated selection scenarios, such as spatially-varying selection (of the type that might be induced by GxE). We note however that so long as there are any fitness effects in heterozygotes, the allele dynamics will be primarily governed by hs; one might also imagine that under some conditions, the mean selection effect across environments would predict allele dynamics reasonably well even in the presence of GxE. Also worth exploring in our view is the standard assumption that hs remains fixed even as Ne changes dramatically. We now mention these points in the Outlook.

Maybe I missed it, but I don't think the acronym DNM is explained anywhere. While it was fairly self-explanatory, I did have a moment of wondering whether it was methylation or mutation and can't hurt to be explicit.

We apologize for the oversight and have updated the text accordingly.

Author Response:

Reviewer #1:

The manuscript by Piccolo and colleagues employs an in vitro neuruloid system to investigate the role of Hippo/YAP signaling pathway in early ectodermal fate specification. The authors examine YAP expression in forming neuruloids and test how manipulation of Hippo/Yap signaling affects their cellular composition. They observe that YAP expression is dynamic and enriched in cells occupying periphery of the neuruloid. Overactivation of the YAP activity by the Lats-kinase inhibitor TRULI leads to an expansion of TFAP2A+ cells (NNE) at early stages and of KRT18+ cells (epidermal) at later stages of development. Accordingly, the authors propose that YAP acts as a lineage determinant that (i) promotes a NNE fate during early development and (ii) impacts the fate of NNE cells by promoting an epidermal instead of a neural crest fate. Finally, the authors report that neuruloids developed with cells harboring mutations characteristics of Huntington's disease display elevated Yap activity.

The study takes advantage of the neuruloid system to examine the role of Hippo-Yap in early development and disease. A strength of the study is the use of the neuruloid as a proxy for the human embryo, which allows the authors to examine the control of spatial patterning in early development (in both wild type and altered cellular states). Yet, this model also presents significant limitations. Some of the results indicate a high degree of variability in YAP activity (and ectodermal patterning) in neuruloids obtained from different inductions. This raises the concern that the neuruloid system may interfere with Hippo/YAP. Furthermore, the model proposed by the authors is not consistent with the functional manipulations with pharmacological agents (e.g., pharmacological activation of YAP results in an increase of both neural and NNE cells; inhibition of YAP does not result in the expected phenotypes).

We thank the reviewer for her/his compliments on our work. The reviewer also points to the limitations of our neuruloid models and asks for clarifications.

The authors propose that YAP activation promotes a non-neural ectodermal (NNE) fate in early neuruloids, and subsequently drives NNE to differentiate into epidermis. However, manipulation of Hippo signaling with pharmacological inhibitors does not entirely support this, as treatment of neuruloids with agonist TRULI leads to expansion of both the PAX6 neural population and the NNE Tfap2a population. A prediction of the model is that treatment with verteporfin should neuralize the organoids, which is not the case (Fig 6A). This disconnect between the model presented in Figure 6D and the experimental results should be addressed by the authors.

We would like to thank the reviewer for this request. In our experiments we observed a dual effect of YAP activation (or HD mutation). As noted by the reviewer, ectodermal lineage- specification occurs both early (increased NNE induction) and late (enhanced epidermis differentiation and contraction of NC differentiation). Moreover, we observed a structural consequence of increased YAP activation in neuruloids, failure of the NE domain to fully close. Following the reviewer suggestion, we have now included an additional panel in Figure 6 to illustrate the phenotype alongside the difference in ectodermal lineage specification (panel E). We have also added in the Discussion a paragraph that highlights the architectural aspect of the observed phenotype.

Regarding the interpretation of the effect of pharmacological inhibition of YAP, we believe that the result of verteporfin treatment on WT neuruloids indicates that YAP activity is not required for this specification but can skew the differentiation towards NNE and epidermis. This is now included in the Results, and a new paragraph has been added in the Discussion directly addressing this point.

The study at times conflates YAP expression with activation of the Hippo-YAP pathway. While the images in figures 1,2, and 4 show changes in YAP expression, confirmation of Hippo-YAP pathway activity should include the use of a reporter (e.g., HOP-Flash) or at least high magnification images showing translocation of YAP to the nucleus. Overall, inclusion of better quantification of YAP-activity is crucial to support the manuscript's conclusions (the authors should also state the number of micropatterns used in each quantitative experiment).

Our evidence correlating YAP nuclear localization with activity is based on: (i) Immunoblots (Figures 1D and 2B); (ii) Confocal image analysis (Figures 1E, 2D, and 4B); and (iii) Induction of YAP target-genes expression as demonstrated by our scRNA-seq analysis, occurs in same epidermal (KRT18+) lineage cells that display the highest levels of YAP nuclear accumulation (Figure 2). However, to strengthen this argument and following the reviewer’s advice, we have now added magnified confocal microscope images of YAP/DAPI staining used to measure nuclear YAP localization at D4 (Figure 1—figure supplement 5). We have also added a slowed and magnified videos of the YAP-GFP/H2B-mCherry (and YAP-GFP alone) at D3-D4, which illustrates the dynamic accumulation of YAP in the nucleus of cells upon BMP4 stimulation (Figure 1—video 2, Figure 1—video 3, Figure 1—video 5, Figure 1—video 6, Figure 4—video 2 and Figure 4—video 3). Finally, the number of colonies analyzed for each experiment is now added in the Figure Legends.

A limitation of the study is that it does not investigate the possibility that Hippo/Yap could be affecting cell proliferation in the different lineages, instead of acting as a cell fate determinant. This is particularly important since Hippo is affected by cell density, which varies from the center to the periphery of the neuruloid. Different rates of proliferation over several days could potentially lead to drastic changes in neuruloid cellular composition.

To address the reviewer’s legitimate point, and assess to potential effects of YAP activation in HD-neuruloids, we performed three sets of experiments. First, we performed RNA-velocity analysis to determine the cellular trajectories within each lineage (FigureXA, below), and calculated the velocity of Seurat’s “cell cycle-associated” genes in each cell population in our scRNA-seq dataset at D4. This analysis indicates that the three ectodermal progenitors have a comparable rate of cell division, with NE being slightly faster than the others and epidermis being the slowest (Figure XB). However, these differences are subtle: the mean velocity of these cell-cycle genes within each population are not significantly different across the three ectodermal lineages (FigureXC). Second, comparison of velocity values between WT and HD, highlighted a significant HD-associated increase in the dynamic of cell-cycle associated genes only within the NE population (FigureXD), consistent with the observation that YAP is ectopically active in this lineage. This increase is also not very dramatic, for the mean velocity of these genes is not significantly different in any comparison at this time (Figure XE).

Figure X. Proliferation rate analysis of D4 neuruloid from scRNAseq dataset. A) transcriptional trajectories were identified in the three ectodermal lineages. B) Velocity of cell cycle associated genes show that NNE lineages (NC and E) are slightly faster than NE. C) However this is not significant the mean population level. D) NE in HD D4 neuruloids display subtle increase in the velocity of cell cycle associated genes. E) Such effect disappears at the mean population level.

Finally, quantification of the number of mitotic nuclei per colony as marked by phospho-histone H3 (Kim et al., 2017) at different time points, demonstrated that YAP activation by TRULI leads to an increase in cell proliferation, especially in late neuruloids. This evidence is now presented in the new Supplemental Figure 4—figure supplement 3. We thank the reviewer for bringing this point to our attention.

It is also important to note that our study does not suggest that YAP is a bona fide cell-fate determinant, but rather that that the global phenotypic signature of YAP activation is influenced by differential regulation of cell-cycle dynamics. Moreover, inasmuch as YAP inhibition with verteporfin does not effect neuruloid formation, we believe that YAP is more of a booster signal operating on top of differentiation programs.

The results of the study contradict a previous reports, and some of these contradictions are not sufficiently addressed. The authors state that the activation of YAP in culture leads to a "complete loss of NC-like SOX10+ colonies"; however, a number of studies in in vivo models support a role for YAP as a positive regulator of neural crest specification.

We thank the reviewer for pointing to the results observed in model systems. We have now included a paragraph in which we acknowledge that YAP has been previously associated with NC specification and survival. However, it should be noted that these conclusions are based on data obtained from non-human model organisms such as Xenopus, or relied on differentiation protocols that are independent of BMP4 stimulation. We believe that the phenotype of unbalanced specification of the NNE depends on an epistatic relationship between BMP4 and Hippo-YAP pathway, which might play a crucial role during human neurulation.

Furthermore, the authors briefly speculate on the finding that Huntington's disease neuruloids have high YAP activity (whereas tissues from patients have low activity), but there is no real clear link to the pathophysiology of the disease.

In our in vitro assay that recapitulates aspects of human neurulation, we observed an early increase (D4) followed by a later decline (D7) in YAP activity associated with HD mutation, which is comparable to a dysregulation of the Hippo pathway that was observed in HD patients. To better clarify this aspect and its potential implication during embryogenesis we have now expanded our Discussion on the possible connection between HD and embryonic development.

Experimental results presented in different figures are often inconsistent throughout the manuscript. This should be examined by the authors since it suggests a lack of reproducibility in the neuruloid protocol. For example, the expression of TFAP2A at D4 neuruloids is a sparse halo at D4 in Fig4D, but robust in Fig1E.

The reviewer is correct in pointing to a certain degree of variability between experiments, especially during the period (D4) when the first NNE lineage begin to emerge (i.e., Supplemental Figure 4—figure supplement 2). Because parallel experimental conditions such as comparison with HD samples or TRULI treatment show consistent trends, however, we believe that our interpretation of these results is fundamentally correct.

The western blot in fig1D shows bands for tYAP and pYAP at D4, while in Fig2B the bands are not present (Fig1D also shows double bands for both markers while fig2B presents single bands).

There are several splicing alternative isoforms of human YAP (Vrbský et al., 2021). Immunoblots for YAP in YAP-GFP biallelically tagged cell lines (Figure 1—figure supplement 1B) show that two isoforms are detectable at pluripotency. During neural induction (D1-D3) both isoforms are downregulated, and upon BMP4 stimulation the larger isoform (top band) is primarily upregulated, so that from D4 onwards only the top band is visible (Figure 2B). To better clarify this point, we now discuss this in the Results and include Supplemental Figures with the quantification of the top and bottom bands (D1-D4, Figure 1D) and only of the top band (D4D7, Figure 2B and Figure 1—figure supplement 4).

As Hippo responds very quickly to cell density, mechanical forces, etc., these inconsistencies could affect the proposed analyses.

As previously mentioned, we have assessed the effect on proliferation rate due to YAP activation by TRULI or HD mutation in neuruloids by scRNA-seq analysis and by counting the number of mitotic cells at different times. Our manuscript leaves open the relationship between HTT mutation and YAP hyperactivation, which likely is mediated in part by these factors, but we do address possible connections in the discussion.

Reviewer #2:

This manuscript by Piccolo et al identifies YAP signalling as key player in lineage determination during development of early human ectoderm. Additionally, the authors show that neuroloids generated using cells engineered to express penetrant levels of CAG repeats in the HTT gene display aberrant YAP signalling during ectodermal specification and that this phenotype can be partially rescued by inhibition of this pathway. This is interesting study and the similarity of the YAP-activated neuroloids and the HD neuroloids is striking. The value of this work would be increased by providing experiments to definitively demonstrate the role of YAP signalling in NNE specification and in HD neuroloids.

We also thank this reviewer for her/his compliments on our work. The reviewer also expresses specific recommendations listed below:

Specific comment: The authors describe the emergence of non-neuronal ectoderm (NNE) at the edges of the printed island cell colony and neuronal ectoderm (NE) within this circular colony. However, they do not show images of any lineage markers confirming that these regions are, in fact, NNE and NE.

We show in Figure 1E that the edges of the neuruloids are positive for TFAP2A, a marker for the NNE lineage. In Figure 4D we also show TFAP2A at the edge (NNE) and PAX6 at the center (NE). Additionally, the spatial identity of the various ectodermal lineages was full characterized in our previous study (Haremaki et al., 2018).

They also don't show that this YAP-GFP cell line recapitulates endogenous fix-and-stains of YAP in these colonies.

Figure 1E shows YAP expression at D4 by immunolabeling for YAP/DAPI acquired by confocal microscopy, which recapitulates that of immunofluorescence detection of nuclear YAP , shown in Figure 4B , and the results obtained by live fluorescence (YAP-GFP/H2B, Figure 4A).

Author Response

Reviewer #1 (Public Review):

The authors evaluate the involvement of the hippocampus in a fast-paced time-to-contact estimation task. They find that the hippocampus is sensitive to feedback received about accuracy on each trial and has activity that tracks behavioral improvement from trial to trial. Its activity is also related to a tendency for time estimation behavior to regress to the mean. This is a novel paradigm to explore hippocampal activity and the results are thus novel and important, but the framing as well as discussion about the meaning of the findings obscures the details of the results or stretches beyond them in many places, as detailed below.

We thank the reviewer for their constructive feedback and were happy to read that s/he considered our approach and results as novel and important. The comments led us to conduct new fMRI analyses, to clarify various unclear phrasings regarding our methods, and to carefully assess our framing of the interpretation and scope of our results. Please find our responses to the individual points below.

1) Some of the results appear in the posterior hippocampus and others in the anteriorhippocampus. The authors do not motivate predictions for anterior vs. posterior hippocampus, and they do not discuss differences found between these areas in the Discussion. The hippocampus is treated as a unitary structure carrying out learning and updating in this task, but the distinct areas involved motivate a more nuanced picture that acknowledges that the same populations of cells may not be carrying out the various discussed functions.

We thank the reviewer for pointing this out. We split the hippocampus into anterior and posterior sections because prior work suggested a different whole-brain connectivity and function of the two. This was mentioned in the methods section (page 15) in the initial submission but unfortunately not in the main text. Moreover, when discussing the results, we did indeed refer mostly to the hippocampus as a unitary structure for simplicity and readability, and because statements about subcomponents are true for the whole. However, we agree with the reviewer that the differences between anterior and posterior sections are very interesting, and that describing these effects in more detail might help to guide future work more precisely.

In response to the reviewer's comment, we therefore clarified at various locations throughout the manuscript whether the respective results were observed in the posterior or anterior section of the hippocampus, and we extended our discussion to reflect the idea that different functions may be carried out by distinct populations of hippocampal cells. In addition, we also now motivate the split into the different sections better in the main text. We made the following changes.

Page 3: “Second, we demonstrate that anterior hippocampal fMRI activity and functional connectivity tracks the behavioral feedback participants received in each trial, revealing a link between hippocampal processing and timing-task performance.

Page 3: “Fourth, we show that these updating signals in the posterior hippocampus were independent of the specific interval that was tested and activity in the anterior hippocampus reflected the magnitude of the behavioral regression effect in each trial.”

Page 5: “We performed both whole-brain voxel-wise analyses as well as regions-of-interest (ROI) analysis for anterior and posterior hippocampus separately, for which prior work suggested functional differences with respect to their contributions to memory-guided behavior (Poppenk et al., 2013, Strange et al. 2014).”

Page 9: “Because anterior and posterior sections of the hippocampus differ in whole-brain connectivity as well as in their contributions to memory-guided behavior (Strange et al. 2014), we analyzed the two sections separately. “

Page 9: “We found that anterior hippocampal activity as well as functional connectivity reflected the feedback participants received during this task, and its activity followed the performance improvements in a temporal-context-dependent manner. Its activity reflected trial-wise behavioral biases towards the mean of the sampled intervals, and activity in the posterior hippocampus signaled sensorimotor updating independent of the specific intervals tested.”

Page 10: “Intriguingly, the mechanisms at play may build on similar temporal coding principles as those discussed for motor timing (Yin & Troger, 2011; Eichenbaum, 2014; Howard, 2017; Palombo & Verfaellie, 2017; Nobre & van Ede, 2018; Paton & Buonomano, 2018; Bellmund et al., 2020, 2021; Shikano et al., 2021; Shimbo et al., 2021), with differential contributions of the anterior and posterior hippocampus. Note that our observation of distinct activity modulations in the anterior and posterior hippocampus suggests that the functions and coding principles discussed here may be mediated by at least partially distinct populations of hippocampal cells.”

Page 11: Interestingly, we observed that functional connectivity of the anterior hippocampus scaled negatively (Fig. 2C) with feedback valence [...]

2) Hippocampal activity is stronger for smaller errors, which makes the interpretationmore complex than the authors acknowledge. If the hippocampus is updating sensorimotor representations, why would its activity be lower when more updating is needed?

Indeed, we found that absolute (univariate) activity of the hippocampus scaled with feedback valence, the inverse of error (Fig. 2A). We see multiple possibilities for why this might be the case, and we discussed some of them in a dedicated discussion section (“The role of feedback in timed motor actions”). For example, prior work showed that hippocampal activity reflects behavioral feedback also in other tasks, which has been linked to learning (e.g. Schönberg et al., 2007; Cohen & Ranganath, 2007; Shohamy & Wagner, 2008; Foerde & Shohamy, 2011; Wimmer et al., 2012). In our understanding, sensorimotor updating is a form of ‘learning’ in an immediate and behaviorally adaptive manner, and we therefore consider our results well consistent with this earlier work. We agree with the reviewer that in principle activity should be stronger if there was stronger sensorimotor updating, but we acknowledge that this intuition builds on an assumption about the relationship between hippocampal neural activity and the BOLD signal, which is not entirely clear. For example, prior work revealed spatially informative negative BOLD responses in the hippocampus as a function of visual stimulation (e.g. Szinte & Knapen 2020), and the effects of inhibitory activity - a leading motif in the hippocampal circuitry - on fMRI data are not fully understood. This raises the possibility that the feedback modulation we observed might also involve negative BOLD responses, which would then translate to the observed negative correlation between feedback valence and the hippocampal fMRI signal, even if the magnitude of the underlying updating mechanism was positively correlated with error. This complicates the interpretation of the direction of the effect, which is why we chose to avoid making strong conclusions about it in our manuscript. Instead, we tried discussing our results in a way that was agnostic to the direction of the feedback modulation. Importantly, hippocampal connectivity with other regions did scale positively with error (Fig. 2B), which we again discussed in the dedicated discussion section.

In response to the reviewer’s comment, we revisited this section of our manuscript and felt the latter result deserved a better discussion. We therefore took this opportunity to extend our discussion of the connectivity results (including their relationship to the univariate-activity results as well as the direction of these effects), all while still avoiding strong conclusions about directionality. Following changes were made to the manuscript.

Page 11: Interestingly, we observed that functional connectivity of the anterior hippocampus scaled negatively (Fig. 2C) with feedback valence, unlike its absolute activity, which scaled positively with feedback valence (Fig. 2A,B), suggesting that the two measures may be sensitive to related but distinct processes.

Page 11: Such network-wide receptive-field re-scaling likely builds on a re-weighting of functional connections between neurons and regions, which may explain why anterior hippocampal connectivity correlated negatively with feedback valence in our data. Larger errors may have led to stronger re-scaling, which may be grounded in a corresponding change in functional connectivity.

3) Some tests were one-tailed without justification, which reduces confidence in the robustness of the results.

We thank the reviewer for pointing us to the fact that our choice of statistical tests was not always clear in the manuscript. In the analysis the reviewer is referring to, we predicted that stronger sensorimotor updating should lead to stronger activity as well as larger behavioral improvements across the respective trials. This is because a stronger update should translate to a more accurate “internal model” of the task and therefore to a better performance. We tested this one-sided hypothesis using the appropriate test statistic (contrasting trials in which behavioral performance did improve versus trials in which it did not improve), but we did not motivate our reasoning well enough in the manuscript. The revised manuscript therefore includes the two new statements shown below to motivate our choice of test statistic more clearly.

Page 7: [...] we contrasted trials in which participants had improved versus the ones in which they had not improved or got worse (see methods for details). Because stronger sensorimotor updating should lead to larger performance improvements, we predicted to find stronger activity for improvements vs. no improvements in these tests (one-tailed hypothesis).

Page 18: These two regressors reflect the tests for target-TTC-independent and target-TTC-specific updating, respectively. Because we predicted to find stronger activity for improvements vs. no improvements in behavioral performance, we here performed one-tailed statistical tests, consistent with the direction of this hypothesis. Improvement in performance was defined as receiving feedback of higher valence than in the corresponding previous trial.

4) The introduction motivates the novelty of this study based on the idea that thehippocampus has traditionally been thought to be involved in memory at the scale of days and weeks. However, as is partially acknowledged later in the Discussion, there is an enormous literature on hippocampal involvement in memory at a much shorter timescale (on the order of seconds). The novelty of this study is not in the timescale as much as in the sensorimotor nature of the task.

We thank the reviewer for this helpful suggestion. We agree that a key part of the novelty of this study is the use of the task that is typically used to study sensorimotor integration and timing rather than hippocampal processing, along with the new insights this task enabled about the role of the hippocampus in sensorimotor updating. As mentioned in the discussion, we also agree with the reviewer that there is prior literature linking hippocampal activity to mnemonic processing on short time scales. We therefore rephrased the corresponding section in the introduction to put more weight on the sensorimotor nature of our task instead of the time scales.

Note that the new statement still includes the time scale of the effects, but that it is less at the center of the argument anymore. We chose to keep it in because we do think that the majority of studies on hippocampal-dependent memory functions focus on longer time scales than our study does, and we expect that many readers will be surprised about the immediacy of how hippocampal activity relates to ongoing behavioral performance (on ultrashort time scales).

We changed the introduction to the following.

Page 2: Here, we approach this question with a new perspective by converging two parallel lines of research centered on sensorimotor timing and hippocampal-dependent cognitive mapping. Specifically, we test how the human hippocampus, an area often implicated in episodic-memory formation (Schiller et al., 2015; Eichenbaum, 2017), may support the flexible updating of sensorimotor representations in real time and in concert with other regions. Importantly, the hippocampus is not traditionally thought to support sensorimotor functions, and its contributions to memory formation are typically discussed for longer time scales (hours, days, weeks). Here, however, we characterize in detail the relationship between hippocampal activity and real-time behavioral performance in a fast-paced timing task, which is traditionally believed to be hippocampal-independent. We propose that the capacity of the hippocampus to encode statistical regularities of our environment (Doeller et al. 2005, Shapiro et al. 2017, Behrens et al., 2018; Momennejad, 2020; Whittington et al., 2020) situates it at the core of a brain-wide network balancing specificity vs. regularization in real time as the relevant behavior is performed.

5) The authors used three different regressors for the three feedback levels, asopposed to a parametric regressor indexing the level of feedback. The predictions are parametric, so a parametric regressor would be a better match, and would allow for the use of all the medium-accuracy data.

The reviewer raises a good point that overlaps with question 3 by reviewer 2. In the current analysis, we model the three feedback levels with three independent regressors (high, medium, low accuracy). We then contrast high vs. low accuracy feedback, obtaining the results shown in Fig. 2AB. The beta estimates obtained for medium-accuracy feedback are being ignored in this contrast. Following the reviewer’s feedback, we therefore re-run the model, this time modeling all three feedback levels in one parametric regressor. All other regressors in the model stayed the same. Instead of contrasting high vs. low accuracy feedback, we then performed voxel-wise t-tests on the beta estimates obtained for the parametric feedback regressor.

The results we observed were highly consistent across the two analyses, and all conclusions presented in the initial manuscript remain unchanged. While the exact t-scores differ slightly, we replicated the effects for all clusters on the voxel-wise map (on whole-brain FWE-corrected levels) as well as for the regions-of-interest analysis for anterior and posterior hippocampus. These results are presented in a new Supplementary Figure 3C.

Note that the new Supplementary Figure 3B shows another related new analyses we conducted in response to question 4 of reviewer 2. Here, we re-ran the initial analysis with three feedback regressors, but without modeling the inter-trial interval (ITI) and the inter-session interval (ISI, i.e. the breaks participants took) to avoid model over-specification. Again, we replicated the results for all clusters and the ROI analysis, showing that the initial results we presented are robust.

The following additions were made to the manuscript.

Page 5: Note that these results were robust even when fewer nuisance regressors were included to control for model over-specification (Fig. S3B; two-tailed one-sample t tests: anterior HPC, t(33) = -3.65, p = 8.9x10-4, pfwe = 0.002, d=-0.63, CI: [-1.01, -0.26]; posterior HPC, t(33) = -1.43, p = 0.161, pfwe = 0.322, d=-0.25, CI: [-0.59, 0.10]), and when all three feedback levels were modeled with one parametric regressors (Fig. S3C; two-tailed one-sample t tests: anterior HPC, t(33) = -3.59, p = 0.002, pfwe = 0.005, d=-0.56, CI: [-0.93, -0.20]; posterior HPC, t(33) = -0.99, p = 0.329, pfwe = 0.659, d=-0.17, CI: [-0.51, 0.17]). Further, there was no systematic relationship between subsequent trials on a behavioral level [...]

Page 17: Moreover, instead of modeling the three feedback levels with three independent regressors, we repeated the analysis modeling the three feedback levels as one parametric regressor with three levels. All other regressors remained unchanged, and the model included the regressors for ITIs and ISIs. We then conducted t-tests implemented in SPM12 using the beta estimates obtained for the parametric feedback regressor (Fig. 2C). Compared to the initial analyses presented above, this has the advantage that medium-accuracy feedback trials are considered for the statistics as well.

6) The authors claim that the results support the idea that the hippocampus is findingan "optimal trade-off between specificity and regularization". This seems overly speculative given the results presented.

We understand the reviewer's skepticism about this statement and agree that the manuscript does not show that the hippocampus is finding the trade-off between specificity and regularization. However, this is also not exactly what the manuscript claims. Instead, it suggests that the hippocampus “may contribute” to solving this trade-off (page 3) as part of a “brain-wide network“ (pages 2,3,9,12). We also state that “Our [...] results suggest that this trade-off [...] is governed by many regions, updating different types of task information in parallel” (Page 11). To us, these phrasings are not equivalent, because we do not think that the role of the hippocampus in sensorimotor updating (or in any process really) can be understood independently from the rest of the brain. We do however think that our results are in line with the idea that the hippocampus contributes to solving this trade-off, and that this is exciting and surprising given the sensorimotor nature of our task, the ultrashort time scale of the underlying process, and the relationship to behavioral performance. We tried expressing that some of the points discussed remain speculation, but it seems that we were not always successful in doing so in the initial submission. We apologize for the misunderstanding, adapted corresponding statements in the manuscript, and we express even more carefully that these ideas are speculation.

Following changes were made to the introduction and discussion.

Page 2: Here, we approach this question with a new perspective by converging two parallel lines of research centered on sensorimotor timing and hippocampal-dependent cognitive mapping. Specifically, we test how the human hippocampus, an area often implicated in episodic-memory formation (Schiller et al., 2015; Eichenbaum, 2017), may support the flexible updating of sensorimotor representations in real time and in concert with other regions.

Page 12: Because hippocampal activity (Julian & Doeller, 2020) and the regression effect (Jazayeri & Shadlen, 2010) were previously linked to the encoding of (temporal) context, we reasoned that hippocampal activity should also be related to the regression effect directly. This may explain why hippocampal activity reflected the magnitude of the regression effect as well as behavioral improvements independently from TTC, and why it reflected feedback, which informed the updating of the internal prior.

Page 12: This is in line with our behavioral results, showing that TTC-task performance became more optimal in the face of both of these two objectives. Over time, behavioral responses clustered more closely between the diagonal and the average line in the behavioral response profile (Fig. 1B, S1G), and the TTC error decreased over time. While different participants approached these optimal performance levels from different directions, either starting with good performance or strong regularization, the group approached overall optimal performance levels over the course of the experiment.

Page 13: This is in line with the notion that the hippocampus [...] supports finding an optimal trade off between specificity and regularization along with other regions. [...] Our results show that the hippocampus supports rapid and feedback-dependent updating of sensorimotor representations, suggesting that it is a central component of a brain-wide network balancing task specificity vs. regularization for flexible behavior in humans.

Note that in response to comment 1 by reviewer 2, the revised manuscript now reports the results of additional behavioral analyses that support the notion that participants find an optimal trade-off between specificity and regularization over time (independent of whether the hippocampus was involved or not).

7) The authors find that hippocampal activity is related to behavioral improvement fromthe prior trial. This seems to be a simple learning effect (participants can learn plenty about this task from a prior trial that does not have the exact same timing as the current trial) but is interpreted as sensitivity to temporal context. The temporal context framing seems too far removed from the analyses performed.

We agree with the reviewer that our observation that hippocampal activity reflects TTC-independent behavioral improvements across trials could have multiple explanations. Critically, i) one of them is that the hippocampus encodes temporal context, ii) it is only one of multiple observations that we build our interpretation on, and iii) our interpretation builds on multiple earlier reports

Interval estimates regress toward the mean of the sampled intervals, an effect that is often referred to as the “regression effect”. This effect, which we observed in our data too (Fig. 1B), has been proposed to reflect the encoding of temporal context (e.g. Jazayeri & Shadlen 2010). Moreover, there is a large body of literature on how the hippocampus may support the encoding of spatial and temporal context (e.g. see Bellmund, Polti & Doeller 2020 for review).

Because both hippocampal activity and the regression effect were linked to the encoding of (temporal) context, we reasoned that hippocampal activity should also be related to the regression effect directly. If so, one would expect that hippocampal activity should reflect behavioral improvements independently from TTC, it should reflect the magnitude of the regression effect, and it should generally reflect feedback, because it is the feedback that informs the updating of the internal prior.

All three observations may have independent explanations indeed, but they are all also in line with the idea that the hippocampus does encode temporal context and that this explains the relationship between hippocampal activity and the regression effect. It therefore reflects a sparse and reasonable explanation in our opinion, even though it necessarily remains an interpretation. Of course, we want to be clear on what our results are and what our interpretations are.

In response to the reviewer’s comment, we therefore toned down two of the statements that mention temporal context in the manuscript, and we removed an overly speculative statement from the result section. In addition, the discussion now describes more clearly how our results are in line with this interpretation.

Abstract: This is in line with the idea that the hippocampus supports the rapid encoding of temporal context even on short time scales in a behavior-dependent manner.

Page 13: This is in line with the notion that the hippocampus encodes temporal context in a behavior-dependent manner, and that it supports finding an optimal trade off between specificity and regularization along with other regions.

Page 12: Because hippocampal activity (Julian & Doeller, 2020) and the regression effect (Jazayeri & Shadlen, 2010) were previously linked to the encoding of (temporal) context, we reasoned that hippocampal activity should also be related to the regression effect directly. This may explain why hippocampal activity reflected the magnitude of the regression effect as well as behavioral improvements independently from TTC, and why it reflected feedback, which informed the updating of the internal prior.

The following statement was removed, overlapping with comment 2 by Reviewer 3:

Instead, these results are consistent with the notion that hippocampal activity signals the updating of task-relevant sensorimotor representations in real-time.

8) I am not sure the term "extraction of statistical regularities" is appropriate. The termis typically used for more complex forms of statistical relationships.

We agree with the reviewer that this expression may be interpreted differently by different readers and are grateful to be pointed to this fact. We therefore removed it and instead added the following (hopefully less ambiguous) statement to the manuscript.

Page 9: This study investigated how the human brain flexibly updates sensorimotor representations in a feedback-dependent manner in the service of timing behavior.

Reviewer #2 (Public Review):

The authors conducted a study involving functional magnetic resonance imaging and a time-to-contact estimation paradigm to investigate the contribution of the human hippocampus (HPC) to sensorimotor timing, with a particular focus on the involvement of this structure in specific vs. generalized learning. Suggestive of the former, it was found that HPC activity reflected time interval-specific improvements in performance while in support of the latter, HPC activity was also found to signal improvements in performance, which were not specific to the individual time intervals tested. Based on these findings, the authors suggest that the human HPC plays a key role in the statistical learning of temporal information as required in sensorimotor behaviour.

By considering two established functions of the HPC (i.e., temporal memory and generalization) in the context of a domain that is not typically associated with this structure (i.e., sensorimotor timing), this study is potentially important, offering novel insight into the involvement of the HPC in everyday behaviour. There is much to like about this submission: the manuscript is clearly written and well-crafted, the paradigm and analyses are well thought out and creative, the methodology is generally sound, and the reported findings push us to consider HPC function from a fresh perspective. A relative weakness of the paper is that it is not entirely clear to what extent the data, at least as currently reported, reflects the involvement of the HPC in specific and generalized learning. Since the authors' conclusions centre around this observation, clarifying this issue is, in my opinion, of primary importance.

We thank the reviewer for these positive and extremely helpful comments, which we will address in detail below. In response to these comments, the revised manuscript clarifies why the observed performance improvements are not at odds with the idea that an optimal trade-off between specificity and regularization is found, and how the time course of learning relates to those reported in previous literature. In addition, we conducted two new fMRI analyses, ensuring that our conclusions remain unchanged even if feedback is modeled with one parametric regressor, and if the number or nuisance regressors is reduced to control for overparameterization of the model. Please find our responses underneath each individual point below.

1) Throughout the manuscript, the authors discuss the trade-off between specific and generalized learning, and point towards Figure S1D as evidence for this (i.e., participants with higher TTC accuracy exhibited a weaker regression effect). What appears to be slightly at odds with this, however, is the observation that the deviation from true TTC decreased with time (Fig S1F) as the regression line slope approached 0.5 (Fig S1E) - one would have perhaps expected the opposite i.e., for deviation from true TTC to increase as generalization increases. To gain further insight into this, it would be helpful to see the deviation from true TTC plotted for each of the four TTC intervals separately and as a signed percentage of the target TTC interval (i.e., (+) or (-) deviation) rather than the absolute value.

We thank the reviewer for raising this important question and for the opportunity to elaborate on the relationship between the TTC error and the magnitude of the regression effect in behavior. Indeed, we see that the regression slopes approach 0.5 and that the TTC error decreases over the course of the experiment. We do not think that these two observations are at odds with each other for the following reasons:

First, while the reviewer is correct in pointing out that the deviation from the TTC should increase as “generalization increases”, that is not what we found. It was not the magnitude of the regularization per se that increased over time, but the overall task performance became more optimal in the face of both objectives: specificity and generalization. This optimum is at a regression-line slope of 0.5. Generalization (or regularization how we refer to it in the present manuscript), therefore did not increase per se on group level.

Second, the regression slopes approached 0.5 on the group-level, but the individual participants approached this level from different directions: Some of them started with a slope value close to 1 (high accuracy), whereas others started with a slope value close to 0 (near full regression to the mean). Irrespective of which slope value they started with, over time, they got closer to 0.5 (Rebuttal Figure 1A). This can also be seen in the fact that the group-level standard deviation in regression slopes becomes smaller over the course of the experiment (Rebuttal Figure 1B, SFig 1G). It is therefore not generally the case that the regression effect becomes stronger over time, but that it becomes more optimal for longer-term behavioral performance, which is then also reflected in an overall decrease in TTC error. Please see our response to the reviewer’s second comment for more discussion on this.

Third, the development of task performance is a function of two behavioral factors: a) the accuracy and b) the precision in TTC estimation. Accuracy describes how similar the participant’s TTC estimates were to the true TTC, whereas precision describes how similar the participant’s TTC estimates were relative to each other (across trials). Our results are a reflection of the fact that participants became both more accurate over time on average, but also more precise. To demonstrate this point visually, we now plotted the Precision and the Accuracy for the 8 task segments below (Rebuttal Figure 1C, SFig 1H), showing that both measures increased as the time progressed and more trials were performed. This was the case for all target durations.

In response to the reviewer’s comment, we clarified in the main text that these findings are not at odds with each other. Furthermore, we made clear that regularization per se did not increase over time on group level. We added additional supporting figures to the supplementary material to make this point. Note that in our view, these new analyses and changes more directly address the overall question the reviewer raised than the figure that was suggested, which is why we prioritized those in the manuscript.

However, we appreciated the suggestion a lot and added the corresponding figure for the sake of completeness.

Following additions were made.

Page 5: In support of this, participants' regression slopes converged over time towards the optimal value of 0.5, i.e. the slope value between veridical performance and the grand mean (Fig. S1F; linear mixed-effects model with task segment as a predictor and participants as the error term, F(1) = 8.172, p = 0.005, ε2=0.08, CI: [0.01, 0.18]), and participants' slope values became more similar (Fig. S1G; linear regression with task segment as predictor, F(1) = 6.283, p = 0.046, ε2 = 0.43, CI: [0, 1]). Consequently, this also led to an improvement in task performance over time on group level (i.e. task accuracy and precision increased (Fig. S1I), and the relationship between accuracy and precision became stronger (Fig. S1H), linear mixed-effect model results for accuracy: F(1) = 15.127, p = 1.3x10-4, ε2=0.06, CI: [0.02, 0.11], precision: F(1) = 20.189, p = 6.1x10-5, ε2 = 0.32, CI: [0.13, 1]), accuracy-precision relationship: F(1) = 8.288, p =0.036, ε2 = 0.56, CI: [0, 1], see methods for model details).

Page 12: This suggests that different regions encode distinct task regularities in parallel to form optimal sensorimotor representations to balance specificity and regularization. This is in line with our behavioral results, showing that TTC-task performance became more optimal in the face of both of these two objectives. Over time, behavioral responses clustered more closely between the diagonal and the average line in the behavioral response profile (Fig. 1B, S1G), and the TTC error decreased over time. While different participants approached these optimal performance levels from different directions, either starting with good performance or strong regularization, the group approached overall optimal performance levels over the course of the experiment.

Page 15: We also corroborated this effect by measuring the dispersion of slope values between participants across task segments using a linear regression model with task segment as a predictor and the standard deviation of slope values across participants as the dependent variable (Fig. S1G). As a measure of behavioral performance, we computed two variables for each target-TTC level: sensorimotor timing accuracy, defined as the absolute difference in estimated and true TTC, and sensorimotor timing precision, defined as coefficient of variation (standard deviation of estimated TTCs divided by the average estimated TTC). To study the interaction between these two variables for each target TTC over time, we first normalized accuracy by the average estimated TTC in order to make both variables comparable. We then used a linear mixed-effects model with precision as the dependent variable, task segment and normalized accuracy as predictors and target TTC as the error term. In addition, we tested whether accuracy and precision increased over the course of the experiment using separate linear mixed-effects models with task segment as predictor and participants as the error term.

2) Generalization relies on prior experience and can be relatively slow to develop as is the case with statistical learning. In Jazayeri and Shadlen (2010), for instance, learning a prior distribution of 11-time intervals demarcated by two briefly flashed cues (compared to 4 intervals associated with 24 possible movement trajectories in the current study) required ~500 trials. I find it somewhat surprising, therefore, that the regression line slope was already relatively close to 0.5 in the very first segment of the task. To what extent did the participants have exposure to the task and the target intervals prior to entering the scanner?

We thank the reviewer for raising the important question about the time course of learning in our task and how our results relate to prior work on this issue. Addressing the specific reviewer question first, participants practiced the task for 2-3 minutes prior to scanning. During the practice, they were not specifically instructed to perform the task as well as they could nor to encode the intervals, but rather to familiarize themselves with the general experimental setup and to ask potential questions outside the MRI machine. While they might have indeed started encoding the prior distribution of intervals during the practice already, we have no way of knowing, and we expect the contribution of this practice on the time course of learning during scanning to be negligible (for the reasons outlined above).

However, in addition to the specific question the reviewer asked, we feel that the comment raises two more general points: 1) How long does it take to learn the prior distribution of a set of intervals as a function of the number of intervals tested, and 2) Why are the learning slopes we report quite shallow already in the beginning of the scan?

Regarding (1), we are not aware of published reports that answer this question directly, and we expect that this will depend on the task that is used. Regarding the comparison to Jazayeri & Shadlen (2010), we believe the learning time course is difficult to compare between our study and theirs. As the reviewer mentioned, our study featured only 4 intervals compared to 11 in their work, based on which we would expect much faster learning in our task than in theirs. We did indeed sample 24 movement directions, but these were irrelevant in terms of learning the interval distribution. Moreover, unlike Jazayeri & Shadlen (2010), our task featured moving stimuli, which may have added additional sensory, motor and proprioceptive information in our study which the participants of the prior study could not rely on.

Regarding (2), and overlapping with the reviewer’s previous comment, the average learning slope in our study is indeed close to 0.5 already in the first task segment, but we would like to highlight that this is a group-level measure. The learning slopes of some subjects were closer to 1 (i.e. the diagonal in Fig 1B), and the one of others was closer to 0 (i.e. the mean) in the beginning of the experiment. The median slope was close to 0.65. Importantly, the slopes of most participants still approached 0.5 in the course of the experiment, and so did even the group-level slope the reviewer is referring to. This also means that participants’ slopes became more similar in the course of the experiment, and they approached 0.5, which we think reflects the optimal trade-off between regressing towards the mean and regressing towards the diagonal (in the data shown in Fig. 1B). This convergence onto the optimal trade-off value can be seen in many measures, including the mean slope (Rebuttal Figure 1A, SFig 1F), the standard deviation in slopes (Rebuttal Figure 1B, SFig 1G) as well as the Precision vs. Accuracy tradeoff (Rebuttal Figure 1C, SFig 1H). We therefore think that our results are well in line with prior literature, even though a direct comparison remains difficult due to differences in the task.

In response to the reviewer’s comment, and related to their first comment, we made the following addition to the discussion section.

Page 12: This suggests that different regions encode distinct task regularities in parallel to form optimal sensorimotor representations to balance specificity and regularization. This is well in line with our behavioral results, showing that TTC-task performance became more optimal in the face of both of these two objectives. Over time, behavioral responses clustered more closely between the diagonal and the average line in the behavioral response profile (Fig. 1B, S1G), and the TTC error decreased over time. While different participants approached these optimal performance levels from different directions, either starting with good performance or strong regularization, the group approached overall optimal performance levels over the course of the experiment.

3) I am curious to know whether differences between high-accuracy andmedium-accuracy feedback as well as between medium-accuracy and low-accuracy feedback predicted hippocampal activity in the first GLM analysis (middle page 5). Currently, the authors only present the findings for the contrast between high-accuracy and low-accuracy feedback. Examining all feedback levels may provide additional insight into the nature of hippocampal involvement and is perhaps more consistent with the subsequent GLM analysis (bottom page 6) in which, according to my understanding, all improvements across subsequent trials were considered (i.e., from low-accuracy to medium-accuracy; medium-accuracy to high-accuracy; as well as low-accuracy to high-accuracy).

We thank the reviewer for this thoughtful question, which relates to questions 5 by reviewer 1. The reviewer is correct that the contrast shown in Fig 2 does not consider the medium-accuracy feedback levels, and that the model in itself is slightly different from the one used in the subsequent analysis presented in Fig. 3. To reply to this comment as well as to a related one by reviewer 1 together, we therefore repeated the full analysis while modeling the three feedback levels in one parametric regressor, which includes the medium-accuracy feedback trials, and is consistent with the analysis shown in Fig. 3. The results of this new analysis are presented in the new Supplementary Fig. 3B.

In short, the model included one parametric regressor with three levels reflecting the three types of feedback, and all nuisance regressors remained unchanged. Instead of contrasting high vs. low accuracy feedback, we then performed voxel-wise t-tests on the beta estimates obtained for the parametric feedback regressor. We found that our results presented initially were very robust: Both the observed clusters in the voxel-wise analysis (on whole-brain FWE-corrected levels) as well as the ROI results replicated across the two analyses, and our conclusions therefore remain unchanged.

We made multiple textual additions to the manuscript to include this new analysis, and we present the results of the analysis including a direct comparison to our initial results in the new Supplementary Fig. 3. Following textual additions were.

Page 5: Note that these results were robust even when fewer nuisance regressors were included to control for model over-specification (Fig. S3B; two-tailed one-sample t tests: anterior HPC, t(33) = -3.65, p = 8.9x10-4, pfwe = 0.002, d=-0.63, CI: [-1.01, -0.26]; posterior HPC, t(33) = -1.43, p = 0.161, pfwe = 0.322, d=-0.25, CI: [-0.59, 0.10]), and when all three feedback levels were modeled with one parametric regressors (Fig. S3C; two-tailed one-sample t tests: anterior HPC, t(33) = -3.59, p = 0.002, pfwe = 0.005, d=-0.56, CI: [-0.93, -0.20]; posterior HPC, t(33) = -0.99, p = 0.329, pfwe = 0.659, d=-0.17, CI: [-0.51, 0.17]). Further, there was no systematic relationship between subsequent trials on a behavioral level [...]

Page 17: Moreover, instead of modeling the three feedback levels with three independent regressors, we repeated the analysis modeling the three feedback levels as one parametric regressor with three levels. All other regressors remained unchanged, and the model included the regressors for ITIs and ISIs. We then conducted t-tests implemented in SPM12 using thebeta estimates obtained for the parametric feedback regressor (Fig. S2C). Compared to the initial analyses presented above, this has the advantage that medium-accuracy feedback trials are considered for the statistics as well.

4) The authors modeled the inter-trial intervals and periods of rest in their univariateGLMs. This approach of modelling all 'down time' can lead to model over-specification and inaccurate parameter estimation (e.g. Pernet, 2014). A comment on this approach as well as consideration of not modelling the inter-trial intervals would be useful.

This is an important issue that we did not address in our initial manuscript. We are aware and agree with the reviewer’s general concern about model over-specification, which can be a big problem in regression as it leads to biased estimates. We did examine whether our model was overspecified before running it, but we did not report a formal test of it in the manuscript. We are grateful to be given the opportunity to do so now.

In response to the reviewer’s comment, we repeated the full analysis shown in Fig. 2 while excluding the nuisance regressors for inter-trial intervals (ISI) and breaks (or inter-session intervals, ISI). All other regressors and analysis steps stayed unchanged relative to the one reported in Fig. 2. The new results are presented in a new Supplementary Figure 3B.

Like for our previous analysis, we again see that the results we initially presented were extremely robust even on whole-brain FWE corrected levels, as well as on ROI level. Our conclusions therefore remain unchanged, and the results we presented initially are not affected by potential model overspecification. In addition to the new Supplementary Figure 3B, we made multiple textual changes to the manuscript to describe this new analysis and its implications. Note that we used the same nuisance regressors in all other GLM analyses too, meaning that it is also very unlikely that model overspecification affects any of the other results presented. We thank the reviewer for suggesting this analysis, and we feel including it in the manuscript has further strengthened the points we initially made.

Following additions were made to the manuscript.

Page 16: The GLM included three boxcar regressors modeling the feedback levels, one for ITIs, one for button presses and one for periods of rest (inter-session interval, ISI) [...]

Page 16: ITIs and ISIs were modeled to reduce task-unrelated noise, but to ensure that this did not lead to over-specification of the above-described GLM, we repeated the full analysis without modeling the two. All other regressors including the main feedback regressors of interest remained unchanged, and we repeated both the voxel-wise and ROI-wise statistical tests as described above (Fig. S2B).

Page 17: Note that these results were robust even when fewer nuisance regressors were included to control for model over-specification (Fig. S3B; two-tailed one-sample t tests: anterior HPC, t(33) = -3.65, p = 8.9x10-4, pfwe = 0.002, d=-0.63, CI: [-1.01, -0.26]; posterior HPC, t(33) = -1.43, p = 0.161, pfwe = 0.322, d=-0.25, CI: [-0.59, 0.10]), and when all three feedback levels were modeled with one parametric regressors (Fig. S3C; two-tailed one-sample t tests: anterior HPC, t(33) = -3.59, p = 0.002, pfwe = 0.005, d=-0.56, CI: [-0.93, -0.20]; posterior HPC, t(33) = -0.99, p = 0.329, pfwe = 0.659, d=-0.17, CI: [-0.51, 0.17]). Further, there was no systematic relationship between subsequent trials on a behavioral level [...]

Reviewer #3 (Public Review):

This paper reports the results of an interesting fMRI study examining the neural correlates of time estimation with an elegant design and a sensorimotor timing task. Results show that hippocampal activity and connectivity are modulated by performance on the task as well as the valence of the feedback provided. This study addresses a very important question in the field which relates to the function of the hippocampus in sensorimotor timing. However, a lack of clarity in the description of the MRI results (and associated methods) currently prevents the evaluation of the results and the interpretations made by the authors. Specifically, the model testing for timing-specific/timing-independent effects is questionable and needs to be clarified. In the current form, several conclusions appear to not be fully supported by the data.

We thank the reviewer for pointing us to many methodological points that needed clarification. We apologize for the confusion about our methods, which we clarify in the revised manuscript. Please find our responses to the individual points below.

Major points

Some methodological points lack clarity which makes it difficult to evaluate the results and the interpretation of the data.

We really appreciate the many constructive comments below. We feel that clarifying these points improved our manuscript immensely.

1) It is unclear how the 3 levels of accuracy and feedback (high, medium, and lowperformance) were computed. Please provide the performance range used for this classification. Was this adjusted to the participants' performance?

The formula that describes how the response window was computed for the different speed levels was reported in the methods section of the original manuscript on page 13. It reads as follows:

“The following formula was used to scale the response window width: d ± ((k ∗ d)/2) where d is the target TTC and k is a constant proportional to 0.3 and 0.6 for high and medium accuracy, respectively.“

In response to the reviewer’s comment, we now additionally report the exact ranges of the different response windows in a new Supplementary Table 1 and refer to it in the Methods section as follows.

Page 10: To calibrate performance feedback across different TTC durations, the precise response window widths of each feedback level scaled with the speed of the fixation target (Table S1).

2) The description of the MRI results lacks details. It is not always clear in the resultssection which models were used and whether parametric modulators were included or not in the model. This makes the results section difficult to follow. For example,

a) Figure 2: According to the description in the text, it appears that panels A and B report the results of a model with 3 regressors, ie one for each accuracy/feedback level (high, medium, low) without parametric modulators included. However, the figure legend for panel B mentions a parametric modulator suggesting that feedback was modelled for each trial as a parametric modulator. The distinction between these 2 models must be clarified in the result section.

We thank the reviewer very much for spotting this discrepancy. Indeed, Figure 2 shows the results obtained for a GLM in which we modeled the three feedback levels with separate regressors, not with one parametric regressor. Instead, the latter was the case for Figure 3. We apologize for the confusion and corrected the description in the figure caption, which now reads as follows. The description in the main text and the methods remain unchanged.

Caption Fig. 2: We plot the beta estimates obtained for the contrast between high vs. low feedback.

Moreover, note that in response to comment 5 by reviewer 1 and comment 3 by reviewer 2, the revised manuscript now additionally reports the results obtained for the parametric regressor in the new Supplementary Figure 3C. All conclusions remain unchanged.

Additionally, it is unclear how Figure 2A supports the following statement: "Moreover, the voxel-wise analysis revealed similar feedback-related activity in the thalamus and the striatum (Fig. 2A), and in the hippocampus when the feedback of the current trial was modeled (Fig. S3)." This is confusing as Figure 2A reports an opposite pattern of results between the striatum/thalamus and the hippocampus. It appears that the statement highlighted above is supported by results from a model including current trial feedback as a parametric modulator (reported in Figure S3).

We agree with the reviewer that our result description was confusing and changed it. It now reads as follows.

Page 5: Moreover, the voxel-wise analysis revealed feedback-related activity also in the thalamus and the striatum (Fig. 2A) [...]

Also, note that it is unclear from Figure 2A what is the direction of the contrast highlighting the hippocampal cluster (high vs. low according to the text but the figure shows negative values in the hippocampus and positive values in the thalamus). These discrepancies need to be addressed and the models used to support the statements made in the results sections need to be explicitly described.

The description of the contrast is correct. Negative values indicate smaller errors and therefore better feedback, which is mentioned in the caption of Fig. 2 as follows:

“Negative values indicate that smaller errors, and higher-accuracy feedback, led to stronger activity.”

Note that the timing error determined the feedback, and that we predicted stronger updating and therefore stronger activity for larger errors (similar to a prediction error). We found the opposite. We mention the reasoning behind this analysis at various locations in the manuscript e.g. when talking about the connectivity analysis:

“We reasoned that larger timing errors and therefore low-accuracy feedback would result in stronger updating compared to smaller timing errors and high-accuracy feedback”

In response to the reviewer’s remark, we clarified this further by adding the following statement to the result section.

Page 5: “Using a mass-univariate general linear model (GLM), we modeled the three feedback levels with one regressor each plus additional nuisance regressors (see methods for details). The three feedback levels (high, medium and low accuracy) corresponded to small, medium and large timing errors, respectively. We then contrasted the beta weights estimated for high-accuracy vs. low-accuracy feedback and examined the effects on group-level averaged across runs.”

b) Connectivity analyses: It is also unclear here which model was used in the PPIanalyses presented in Figure 2. As it appears that the seed region was extracted from a high vs. low contrast (without modulators), the PPI should be built using the same model. I assume this was the case as the authors mentioned "These co-fluctuations were stronger when participants performed poorly in the previous trial and therefore when they received low-accuracy feedback." if this refers to low vs. high contrast. Please clarify.

Yes, the PPI model was built using the same model. We clarified this in the methods section by adding the following statement to the PPI description.

Page 17: “The PPI model was built using the same model that revealed the main effects used to define the HPC sphere “

Yes, the reviewer is correct in thinking that the contrast shows the difference between low vs. high-accuracy feedback. We clarified this in the main text as well as in the caption of Fig. 2.

Caption Fig 2: [...] We plot results of a psychophysiological interactions (PPI) analysis conducted using the hippocampal peak effects in (A) as a seed for low vs. high-accuracy feedback. [...]

Page 17: The estimated beta weight corresponding to the interaction term was then tested against zero on the group-level using a t-test implemented in SPM12 (Fig. 2C). The contrast reflects the difference between low vs. high-accuracy feedback. This revealed brain areas whose activity was co-varying with the hippocampus seed ROI as a function of past-trial performance (n-1).

c) It is unclear why the model testing TTC-specific / TTC-independent effects (resultspresented in Figure 3) used 2 parametric modulators (as opposed to building two separate models with a different modulator each). I wonder how the authors dealt with the orthogonalization between parametric modulators with such a model. In SPM, the orthogonalization of parametric modulators is based on the order of the modulators in the design matrix. In this case, parametric modulator #2 would be orthogonalized to the preceding modulator so that a contrast focusing on the parametric modulator #2 would highlight any modulation that is above and beyond that explained by modulator #1. In this case, modulation of brain activity that is TTC-specific would have to be above and beyond a modulation that is TTC-independent to be highlighted. I am unsure that this is what the authors wanted to test here (or whether this is how the MRI design was built). Importantly, this might bias the interpretation of their results as - by design - it is less likely to observe TTC-specific modulations in the hippocampus as there is significant TTC-independent modulation. In other words, switching the order of the modulators in the model (or building two separate models) might yield different results. This is an important point to address as this might challenge the TTC-specific/TTC-independent results described in the manuscript.

We thank the reviewer for raising this important issue. When running the respective analysis, we made sure that the regressors were not collinear and we therefore did not expect substantial overlap in shared variance between them. However, we agree with the reviewer that orthogonalizing one regressor with respect to the other could still affect the results. To make sure that our expectations were indeed met, we therefore repeated the main analysis twice: 1) switching the order of the modulators and 2) turning orthogonalization off (which is possible in SPM12 unlike in previous versions). In all cases, our key results and conclusions remained unchanged, including the central results of the hippocampus analyses.

Anterior (ant.) / Posterior (post.) Hippocampus ROI analysis with A) original order of modulators, B) switching the order of the modulators and C) turning orthogonalization of modulators off. ABC) Orange color corresponds to the TTC-independent condition whereas light-blue color corresponds to the TTC-specific condition. Statistics reflect p<0.05 at Bonferroni corrected levels () obtained using a group-level one-tailed one-sample t-test against zero; A) pfwe = 0.017, B) pfwe = 0.039, C) pfwe = 0.039.*

Because orthogonalization did not affect the conclusions, the new manuscript simply reports the analysis for which it was turned off. Note that these new figures are extremely similar to the original figures we presented, which can be seen in the exemplary figure below showing our key results at a liberal threshold for transparency. In addition, we clarified that orthogonalization was turned off in the methods section as follows.

Page 18: These two regressors reflect the tests for target-TTC-independent and target-TTC-specific updating, respectively, and they were not orthogonalized to each other.

Comparison of old & new results: also see Fig. 3 and Fig. S5 in manuscript

d) It is also unclear how the behavioral improvement was coded/classified "wecontrasted trials in which participants had improved versus the ones in which they had not improved or got worse"- It appears that improvement computation was based on the change of feedback valence (between high, medium and low). It is unclear why performance wasn't used instead? This would provide a finer-grained modulation?

We thank the reviewer for the opportunity to clarify this important point. First, we chose to model feedback because it is the feedback that determines whether participants update their “internal model” or not. Without feedback, they would not know how well they performed, and we would not expect to find activity related to sensorimotor updating. Second, behavioral performance and received feedback are tightly correlated, because the former determines the latter. We therefore do not expect to see major differences in results obtained between the two. Third, we did in fact model both feedback and performance in two independent GLMs, even though the way the results were reported in the initial submission made it difficult to compare the two.

Figure 4 shows the results obtained when modeling behavioral performance in the current trial as an F-contrast, and Supplementary Fig 4 shows the results when modeling the feedback received in the current trial as a t-contrast. While the voxel-wise t-maps/F-maps are also quite similar, we now additionally report the t-contrast for the behavioral-performance GLM in a new Supplementary Figure 4C. The t-maps obtained for these two different analyses are extremely similar, confirming that the direction of the effects as well as their interpretation remain independent of whether feedback or performance is modeled.

The revised manuscript refers to the new Supplementary Figure 4C as follows.

Page 17: In two independent GLMs, we analyzed the time courses of all voxels in the brain as a function of behavioral performance (i.e. TTC error) in each trial, and as a function of feedback received at the end of each trial. The models included one mean-centered parametric regressor per run, modeling either the TTC error or the three feedback levels in each trial, respectively. Note that the feedback itself was a function of TTC error in each trial [...] We estimated weights for all regressors and conducted a t-test against zero using SPM12 for our feedback and performance regressors of interest on the group level (Fig. S4A). [...]

Page 17: In addition to the voxel-wise whole-brain analyses described above, we conducted independent ROI analyses for the anterior and posterior sections of the hippocampus (Fig. S2A). Here, we tested the beta estimates obtained in our first-level analysis for the feedback and performance regressors of interest (Fig. S4B; two-tailed one-sample t tests: anterior HPC, t(33) = -5.92, p = 1.2x10-6, pfwe = 2.4x10-6, d=-1.02, CI: [-1.45, -0.6]; posterior HPC, t(33) = -4.07, p = 2.7x10-4, pfwe = 5.4x10-4, d=-0.7, CI: [-1.09, -0.32]). See section "Regions of interest definition and analysis" for more details.

If the feedback valence was used to classify trials as improved or not, how was this modelled (one regressor for improved, one for no improvement? As opposed to a parametric modulator with performance improvement?).

We apologize for the lack of clarity regarding our regressor design. In response to this comment, we adapted the corresponding paragraph in the methods to express more clearly that improvement trials and no-improvement trials were modeled with two separate parametric regressors - in line with the reviewer’s understanding. The new paragraph reads as follows.

Page 18: One regressor modeled the main effect of the trial and two parametric regressors modeled the following contrasts: Parametric regressor 1: trials in which behavioral performance improved \textit{vs}. parametric regressor 2: trials in which behavioral performance did not improve or got worse relative to the previous trial.

Last, it is also unclear how ITI was modelled as a regressor. Did the authors mean a parametric modulator here? Some clarification on the events modelled would also be helpful. What was the onset of a trial in the MRI design? The start of the trial? Then end? The onset of the prediction time?

The Inter-trial intervals (ITIs) were modeled as a boxcar regressor convolved with the hemodynamic response function. They describe the time after the feedback-phase offset and the subsequent trial onset. Moreover, the start of the trial was the moment when the visual-tracking target started moving after the ITI, whereas the trial end was the offset of the feedback phase (i.e. the moment in which the feedback disappeared from the screen). The onset of the “prediction time” was the moment in which the visual-tracking target stopped moving, prompting participants to estimate the time-to-contact. We now explain this more clearly in the methods as shown below.

Page 16: The GLM included three boxcar regressors modeling the feedback levels, one for ITIs, one for button presses and one for periods of rest (inter-session interval, ISI), which were all convolved with the canonical hemodynamic response function of SPM12. The start of the trial was considered as the trial onsets for modeling (i.e. the time when the visual-tracking target started moving). The trial end was the offset of the feedback phase (i.e. the moment in which the feedback disappeared from the screen). The ITI was the time between the offset of the feedback-phase and the subsequent trial onset.

On a related note, in response to question 4 by reviewer 2, we now repeated one of the main analyses (Fig. 2) without modeling the ITI (as well as the Inter-session interval, ISI). We found that our key results and conclusions are independent of whether or not these time points were modeled. These new results are presented in the new Supplementary Figure 3B.

Page 16: ITIs and ISIs were modeled to reduce task-unrelated noise, but to ensure that this did not lead to over-specification of the above-described GLM, we repeated the full analysis without modeling the two. [...]

1. Perhaps as a result of a lack of clarity in the result section and the MRI methods, it appears that some conclusions presented in the result section are not supported by the data. E.g. "Instead, these results are consistent with the notion that hippocampal activity signals the updating of task-relevant sensorimotor representations in real-time." The data show that hippocampal activity is higher during and after an accurate trial. This pattern of results could be attributed to various processes such as e.g. reward or learning etc. I would recommend not providing such interpretations in the result section and addressing these points in the discussion.

Similar to above, statements like "These results suggest that the hippocampus updates information that is independent of the target TTC". The data show that higher hippocampal activity is linked to greater improvement across trials independent of the timing of the trial. The point about updating is rather speculative and should be presented in the discussion instead of the result section.

The reviewer is referring to two statements in the results section that reflect our interpretation rather than a description of the results. In response to the reviewer’s comment, we therefore removed the following statement from the results.

Instead, these results are consistent with the notion that hippocampal activity signals the updating of task-relevant sensorimotor representations in real-time.

In addition, we replaced the remaining statement by the following. We feel this new statement makes clear why we conducted the analysis that is described without offering an interpretation of the results that were presented before.

Page 8: We reasoned that updating TTC-independent information may support generalization performance by means of regularizing the encoded intervals based on the temporal context in which they were encoded.

Author Response:

Reviewer #1 (Public Review):

The manuscript provides very high quality single-cell physiology combined with population physiology to reveal distinctives roles for two anatomically dfferent LN populations in the cockroach antennal lobe. The conclusion that non-spiking LNs with graded responses show glomerular-restricted responses to odorants and spiking LNs show similar responses across glomeruli generally supported with strong and clean data, although the possibility of selective interglomerular inhibition has not been ruled out. On balance, the single-cell biophysics and physiology provides foundational information useful for well-grounded mechanistic understanding of how information is processed in insect antennal lobes, and how each LN class contributes to odor perception and behavior.

Thank you for this positive feedback.

Reviewer #2 (Public Review):

The manuscript "Task-specific roles of local interneurons for inter- and intraglomerular signaling in the insect antennal lobe" evaluates the spatial distribution of calcium signals evoked by odors in two major classes of olfactory local neurons (LNs) in the cockroach P. Americana, which are defined by their physiological and morphological properties. Spiking type I LNs have a patchy innervation pattern of a subset of glomeruli, whereas non-spiking type II LNs innervate almost all glomeruli (Type II). The authors' overall conclusion is that odors evoke calcium signals globally and relatively uniformly across glomeruli in type I spiking LNs, and LN neurites in each glomerulus are broadly tuned to odor. In contrast, the authors conclude that they observe odor-specific patterns of calcium signals in type II nonspiking LNs, and LN neurites in different glomeruli display distinct local odor tuning. Blockade of action potentials in type I LNs eliminates global calcium signaling and decorrelates glomerular tuning curves, converting their response profile to be more similar to that of type II LNs. From these conclusions, the authors infer a primary role of type I LNs in interglomerular signaling and type III LNs in intraglomerular signaling.

The question investigated by this study - to understand the computational significance of different types of LNs in olfactory circuits - is an important and significant problem. The design of the study is straightforward, but methodological and conceptual gaps raise some concerns about the authors' interpretation of their results. These can be broadly grouped into three main areas.

1) The comparison of the spatial (glomerular) pattern of odor-evoked calcium signals in type I versus type II LNs may not necessarily be a true apples-to-apples comparison. Odor-evoked calcium signals are an order of magnitude larger in type I versus type II cells, which will lead to a higher apparent correlation in type I cells. In type IIb cells, and type I cells with sodium channel blockade, odor-evoked calcium signals are much smaller, and the method of quantification of odor tuning (normalized area under the curve) is noisy. Compare, for instance, ROI 4 & 15 (Figure 4) or ROI 16 & 23 (Figure 5) which are pairs of ROIs that their quantification concludes have dramatically different odor tuning, but which visual inspection shows to be less convincing. The fact that glomerular tuning looks more correlated in type IIa cells, which have larger, more reliable responses compared to type IIb cells, also supports this concern.

We agree with the reviewer that "the comparison of the spatial (glomerular) pattern of odor-evoked calcium signals is not necessarily a true apples-to-apples comparison". Type I and type II LNs are different neuron types. Given their different physiology and morphology, this is not even close to a "true apples-to-apples comparison" - and a key point of the manuscript is to show just that.

As we have emphasized in response to Essential Revision 1, the differences in Ca2+ signals are not an experimental shortcoming but a physiologically relevant finding per se. These data, especially when combined with the electrophysiological data, contribute to a better understanding of these neurons’ physiological and computational properties.

It is physiologically determined that the Ca2+ signals during odorant stimulation in the type II LNs are smaller than in type I LNs. And yes, the signals are small because small postsynpathetic Ca2+ currents predominantly cause the signals. Regardless of the imaging method, this naturally reduces the signal-to-noise ratio, making it more challenging to detect signals. To address this issue, we used a well-defined and reproducible method for analyzing these signals. In this context, we do not agree with the very general criticism of the method. The reviewer questions whether the signals are odorant-induced or just noise (see also minor point 12). If we had recorded only noise, we would expect all tuning curves (for each odorant and glomerulus) to be the same. In this context, we disagree with the reviewer's statement that the tuning curves do not represent the Ca2+ signals in Figure 4 (ROI 4 and 15) and Figure 5 (ROI 16 and 23). This debate reflects precisely the kind of 'visual inspection bias' that our clearly defined analysis aims to avoid. On close inspection, the differences in Ca2+ signals can indeed be seen. Figure II (of this letter) shows the signals from the glomeruli in question at higher magnification. The sections of the recordings that were used for the tuning curves are marked in red.

Figure II: Ca2+ signals of selected glomeruli that were questioned by the reviewer.

2) An additional methodological issue that compounds the first concern is that calcium signals are imaged with wide-field imaging, and signals from each ROI likely reflect out of plane signals. Out of plane artifacts will be larger for larger calcium signals, which may also make it impossible to resolve any glomerular-specific signals in the type I LNs.

Thank you for allowing us to clarify this point. The reviewer comment implies that the different amplitudes of the Ca2+ signals indicate some technical-methodological deficiency (poorly chosen odor concentration). But in fact, this is a key finding of this study that is physiologically relevant and crucial for understanding the function of the neurons studied. These very differences in the Ca2+ signals are evidence of the different roles these neurons play in AL. The different signal amplitudes directly show the distinct physiology and Ca2+ sources that dominate the Ca2+ signals in type I and type II LNs. Accordingly, it is impractical to equalize the magnitude of Ca2+ signals under physiological conditions by adjusting the concentration of odor stimuli.

In the following, we address these issues in more detail: 1) Imaging Method 2) Odorant stimulation 3) Cell type-specific Ca2+ signals

1) Imaging Method:

Of course, we agree with the reviewer comment that out-of-focus and out-of-glomerulus fluorescence can potentially affect measurements, especially in widefield optical imaging in thick tissue. This issue was carefully addressed in initial experiments. In type I LNs, which innervate a subset of glomeruli, we detected fluorescence signals, which matched the spike pattern of the electrophysiological recordings 1:1, only in the innervated glomeruli. In the not innervated ROIs (glomeruli), we detected no or comparatively very little fluorescence, even in glomeruli directly adjacent to innervated glomeruli.

To illustrate this, FIGURE I (of this response letter) shows measurements from an AL in which an uniglomerular projection neuron was investigated in an a set of experiments that were not directly related to the current study. In this experiment, a train of action potential was induced by depolarizing current. The traces show the action potential induced fluorescent signals from the innervated glomerulus (glomerulus #1) and the directly adjacent glomeruli.

These results do not entirely exclude that the large Ca2+ signals from the innervated LN glomeruli may include out-of-focus and out-of-glomerulus fluorescence, but they do show that the bulk of the signal is generated from the recorded neuron in the respective glomeruli.

Figure I: Simultaneous electrophysiological and optophysiological recordings of a uniglomerular projection using the ratiometric Ca2+ indicator fura-2. The projection neuron has its arborization in glomerulus 1. The train of action potentials was induced with a depolarizing current pulse (grey bar).

2) Odorant Stimulation: It is important to note that the odorant concentration cannot be varied freely. For these experiments, the odorant concentrations have to be within a 'physiologically meaningful' range, which means: On the one hand, they have to be high enough to induce a clear response in the projection neurons (the antennal lobe output). On the other hand, however, the concentration was not allowed to be so high that the ORNs were stimulated nonspecifically. These criteria were met with the used concentrations since they induced clear and odorant-specific activity in projection neurons.

3) Cell type-specific Ca2+ signals:

The differences in Ca2+ signals are described and discussed in some detail throughout the text (e.g., page 6, lines 119-136; page 9, lines 193-198; page 10-11, lines 226-235; page 14-15, line 309-333). Briefly: In spiking type I LNs, the observed large Ca2+ signals are mediated mainly by voltage-depended Ca2+ channels activated by the Na+-driven action potential's strong depolarization. These large Ca2+ signals mask smaller signals that originate, for example, from excitatory synaptic input (i.e., evoked by ligand-activated Ca2+ conductances). Preventing the firing of action potentials can unmask the ligand-activated signals, as shown in Figure 4 (see also minor comments 8. and 10.). In nonspiking type II LNs, the action potential-generated Ca2+ signals are absent; accordingly, the Ca2+ signals are much smaller. In our model, the comparatively small Ca2+ signals in type II LNs are mediated mainly by (synaptic) ligand-gated Ca2+ conductances, possibly with contributions from voltage-gated Ca2+ channels activated by the comparatively small depolarization (compared with type I LNs).

Accordingly, our main conclusion, that spiking LNs play a primary role in interglomerular signaling, while nonspiking LNs play an essential role in intraglomeular signaling, can be DIRECTLY inferred from the differences in odorant induced Ca2+ signals alone.

a) Type I LN: The large, simultaneous, and uniform Ca2+ signals in the innervated glomeruli of an individual type I LN clearly show that they are triggered in each glomerulus by the propagated action potentials, which conclusively shows lateral interglomerular signal propagation.

b) Type II LNs: In the type II LNs, we observed relatively small Ca2+ signals in single glomeruli or a small fraction of glomeruli of a given neuron. Importantly, the time course and amplitude of the Ca2+ signals varied between different glomeruli and different odors. Considering that type II LNs in principle, can generate large voltage-activated Ca2+ currents (larger that type I LNS; page 4, lines 82-86, Husch et al. 2009a,b; Fusca and Kloppenburg 2021), these data suggest that in type II LNs electrical or Ca2+ signals spread only within the same glomerulus; and laterally only to glomeruli that are electrotonically close to the odorant stimulated glomerulus.

Taken together, this means that our conclusions regarding inter- and intraglomerular signaling can be derived from the simultaneously recorded amplitudes and the dynamics of the membrane potential and Ca2+ signals alone. This also means that although the correlation analyses support this conclusion nicely, the actual conclusion does not ultimately depend on the correlation analysis. We had (tried to) expressed this with the wording, “Quantitatively, this is reflected in the glomerulus-specific odorant responses and the diverse correlation coefficiiants across…” (page 10, lines 216-217) and “ …This is also reflected in the highly correlated tuning curves in type I LNs and low correlations between tuning curves in type II LNs”(page 13, lines 293-295).

3) Apart from the above methodological concerns, the authors' interpretation of these data as supporting inter- versus intra-glomerular signaling are not well supported. The odors used in the study are general odors that presumably excite feedforward input to many glomeruli. Since the glomerular source of excitation is not determined, it's not possible to assign the signals in type II LNs as arising locally - selective interglomerular signal propagation is entirely possible. Likewise, the study design does not allow the authors to rule out the possibility that significant intraglomerular inhibition may be mediated by type I LNs.

The reviewer addresses an important point. However, from the comment, we get the impression that he/she has not taken into account the entire data set and the DISCUSSION. In fact, this topic has already been discussed in some detail in the original version (page 12, lines 268-271; page 15-16; lines 358-374). This section even has a respective heading: "Inter- and intraglomerular signaling via nonspiking type II LNs" (page 15, line 338). We apologize if our explanations regarding this point were unclear, but we also feel that the reviewer is arguing against statements that we did not make in this way.

a) In 11 out of 18 type II LNs we found 'relatively uncorrelated' (r=0.43±0.16, N=11) glomerular tuning curves. These experiments argue strongly for a 'local excitation' with restricted signal propagation and do not provide support for interglomerular signal propagation. Thus, these results support our interpretation of intraglomerular signaling in this set of neurons.

b) In 7 out of 18 experiments, we observed 'higher correlated' glomerular tuning curves (r=0.78±0.07, N=7). We agree with the reviewer that this could be caused by various mechanisms, including simultaneous input to several glomeruli or by interglomerular signaling. Both possibilities were mentioned and discussed in the original version of the manuscript (page 12, lines 268-271; page 15-16; lines 358-374). In the Discussion, we considered the latter possibility in particular (but not exclusively) for the type IIa1 neurons that generate spikelets. Their comparatively stronger active membrane properties may be particularly suitable for selective signal transduction between glomeruli.

c) We have not ruled out that local signaling exists in type I LNs – in addition to interglomerular signaling. The highly localized Ca2+ signals in type I LNs, which we observed when Na+ -driven action potential generation was prevented, may support this interpretation. However, we would like to reiterate that the simultaneous electrophysiological and optophysiological recordings, which show highly correlated glomerular Ca2+ dynamics that match 1:1 with the simultaneously recorded action potential pattern, clearly suggest interglomerular signaling. We also want to emphasize that this interpretation is in agreement with previous models derived from electrophysiological studies(Assisi et al., 2011; Fujiwara et al., 2014; Hong and Wilson, 2015; Nagel and Wilson, 2016; Olsen and Wilson, 2008; Sachse and Galizia, 2002; Wilson, 2013).

In light of the reviewer's comment(s), we have modified the text to clarify these points (page 14, lines 317-319).

Reviewer #3 (Public Review):

To elucidate the role of the two types of LNs, the authors combined whole-cell patch clamp recordings with calcium imaging via single cell dye injection. This method enables to monitor calcium dynamics of the different axons and branches of single LNs in identified glomeruli of the antennal lobe, while the membrane potential can be recorded at the same time. The authors recorded in total from 23 spiking (type I LN) and 18 non-spiking (type II LN) neurons to a set of 9 odors and analyzed the firing pattern as well as calcium signals during odor stimulation for individual glomeruli. The recordings reveal on one side that odor-evoked calcium responses of type I LNs are odor-specific, but homogeneous across glomeruli and therefore highly correlated regarding the tuning curves. In contrast, odor-evoked responses of type II LNs show less correlated tuning patterns and rather specific odor-evoked calcium signals for each glomerulus. Moreover the authors demonstrate that both LN types exhibit distinct glomerular branching patterns, with type I innervating many, but not all glomeruli, while type II LNs branch in all glomeruli.

From these results and further experiments using pharmacological manipulation, the authors conclude that type I LNs rather play a role regarding interglomerular inhibition in form of lateral inhibition between different glomeruli, while type II LNs are involved in intraglomerular signaling by developing microcircuits in individual glomeruli.

In my opinion the methodological approach is quite challenging and all subsequent analyses have been carried out thoroughly. The obtained data are highly relevant, but provide rather an indirect proof regarding the distinct roles of the two LN types investigated. Nevertheless, the conclusions are convincing and the study generally represents a valuable and important contribution to our understanding of the neuronal mechanisms underlying odor processing in the insect antennal lobe. I think the authors should emphasize their take-home messages and resulting conclusions even stronger. They do a good job in explaining their results in their discussion, but need to improve and highlight the outcome and meaning of their individual experiments in their results section.

Thank you for this positive feedback.

References:

Assisi, C., Stopfer, M., Bazhenov, M., 2011. Using the structure of inhibitory networks to unravel mechanisms of spatiotemporal patterning. Neuron 69, 373–386. https://doi.org/10.1016/j.neuron.2010.12.019

Das, S., Trona, F., Khallaf, M.A., Schuh, E., Knaden, M., Hansson, B.S., Sachse, S., 2017. Electrical synapses mediate synergism between pheromone and food odors in Drosophila melanogaster . Proc Natl Acad Sci U S A 114, E9962–E9971. https://doi.org/10.1073/pnas.1712706114

Fujiwara, T., Kazawa, T., Haupt, S.S., Kanzaki, R., 2014. Postsynaptic odorant concentration dependent inhibition controls temporal properties of spike responses of projection neurons in the moth antennal lobe. PLOS ONE 9, e89132. https://doi.org/10.1371/journal.pone.0089132

Fusca, D., Husch, A., Baumann, A., Kloppenburg, P., 2013. Choline acetyltransferase-like immunoreactivity in a physiologically distinct subtype of olfactory nonspiking local interneurons in the cockroach (Periplaneta americana). J Comp Neurol 521, 3556–3569. https://doi.org/10.1002/cne.23371

Fuscà, D., and Kloppenburg, P. (2021). Odor processing in the cockroach antennal lobe-the network components. Cell Tissue Res.

Hong, E.J., Wilson, R.I., 2015. Simultaneous encoding of odors by channels with diverse sensitivity to inhibition. Neuron 85, 573–589. https://doi.org/10.1016/j.neuron.2014.12.040

Husch, A., Paehler, M., Fusca, D., Paeger, L., Kloppenburg, P., 2009a. Calcium current diversity in physiologically different local interneuron types of the antennal lobe. J Neurosci 29, 716–726. https://doi.org/10.1523/JNEUROSCI.3677-08.2009

Husch, A., Paehler, M., Fusca, D., Paeger, L., Kloppenburg, P., 2009b. Distinct electrophysiological properties in subtypes of nonspiking olfactory local interneurons correlate with their cell type-specific Ca2+ current profiles. J Neurophysiol 102, 2834–2845. https://doi.org/10.1152/jn.00627.2009

Nagel, K.I., Wilson, R.I., 2016. Mechanisms Underlying Population Response Dynamics in Inhibitory Interneurons of the Drosophila Antennal Lobe. J Neurosci 36, 4325–4338. https://doi.org/10.1523/JNEUROSCI.3887-15.2016

Neupert, S., Fusca, D., Kloppenburg, P., Predel, R., 2018. Analysis of single neurons by perforated patch clamp recordings and MALDI-TOF mass spectrometry. ACS Chem Neurosci 9, 2089–2096.

Olsen, S.R., Bhandawat, V., Wilson, R.I., 2007. Excitatory interactions between olfactory processing channels in the Drosophila antennal lobe. Neuron 54, 89–103. https://doi.org/10.1016/j.neuron.2007.03.010

Olsen, S.R., Wilson, R.I., 2008. Lateral presynaptic inhibition mediates gain control in an olfactory circuit. Nature 452, 956–960. https://doi.org/10.1038/nature06864

Sachse, S., Galizia, C., 2002. Role of inhibition for temporal and spatial odor representation in olfactory output neurons: a calcium imaging study. J Neurophysiol. 87, 1106–17.

Shang, Y., Claridge-Chang, A., Sjulson, L., Pypaert, M., Miesenbock, G., 2007. Excitatory Local Circuits and Their Implications for Olfactory Processing in the Fly Antennal Lobe. Cell 128, 601–612.

Wilson, R.I., 2013. Early olfactory processing in Drosophila: mechanisms and principles. Annu Rev Neurosci 36, 217–241. https://doi.org/10.1146/annurev-neuro-062111-150533

Yaksi, E., Wilson, R.I., 2010. Electrical coupling between olfactory glomeruli. Neuron 67, 1034–1047. https://doi.org/10.1016/j.neuron.2010.08.041

Author Response

Reviewer #2 (Public Review):

In this MEG work employing two types of bistable perception test and unique regression analyses, the authors identified different neural frequencies to different components of visual perception: its content and stability.

Strengths:

This study has a nice set of three different experiments to clarify neural differences between content, memory and stability of visual perception.

The state space analysis appears to be powerful to identify such different neural signatures for different cognitive components as well.

Weaknesses:

Despite such strengths, this work may have the somewhat critical weakness specified in the recommendations for the authors.

First, in the analysis to identify content-specific neural frequency, the authors concluded that the SCP is more relevant to the visual perceptual content compared to the neural activity in the alpha and beta-band frequencies. In my impression, to claim this, it would be necessary to show statistically significant differences in the prediction accuracy between the SCP and the other frequencies. Given the not-so-high prediction accuracy seen in the SCP-based analysis, such statistical supports appear essential.

We have now directly compared decoding accuracy for SCP and alpha/beta oscillations, which showed statistically significant differences in both the ambiguous and unambiguous conditions for both ambiguous images. We have added these results as a supplementary figure (new Figure 2—figure supplement 1).

Second, two behavioural metrics in the neural state space analysis-i.e., Switch and Direction-may be too arbitrary. As suggested by the power-law distribution of the percept duration, the neural dynamics during seemingly stable percept may not be able to be described in linear functions. Instead, the brain may go back and forth between several neural states even when we are thinking we're experiencing stable visual consciousness. If so, the current definition of the Switch metric and Direction index, which seems to be based on the behaviour of the Switch index, may be arbitrary. In other words, I feel the authors may have to elaborate the rationale for the definitions of such metrics.

First, we note it is generally accepted in the field that the distribution of percept durations follows a gamma distribution instead of a power-law distribution (e.g., Sterzer et al., TiCS 2009; Blake & Logothetis Nature Rev. Neurosci 2002; Kleinschmidt et al., 1998; Leopold et al., TiCS 1999), and microswitches have not been reported either using the more classic task as that employed here or the more recently developed ‘no-report’ task of using eye-tracking statistics to deduce perceptual switches without overt report (e.g., Frassle et al., J Neurosci 2014).

Second, while brain activity may fluctuate during these time periods, it never crosses the threshold of evoking a conscious report, and thus we would expect that such fluctuations, if they do occur, would be of a lower magnitude than those that do produce a conscious report.

Most importantly, our goal here is to define behavioral metrics in order to identify components of neural dynamics underpinning the relevant aspect of behavior. As such, our definition of the behavioral metric should not be directly informed by observed spontaneous dynamics of brain activity (especially those that may be observed in the data but are of unclear relevance to perceptual switching); otherwise the analysis would be prone to circularity and spurious correlations (i.e., using observed brain dynamics to inform construction of behavioral metrics might pick up aspect of brain dynamics not really relevant to behavior in the analysis results).

Finally, the timing characteristics of ‘Switch’ and ‘Direction’ behavioral metrics are not arbitrary; instead they are the simplest behavioral functions that allow a comparison of pre- and post-switching periods (or when the percepts might be in the ‘stabilizing’ phase vs. the ‘destabilizing’ phase). Nevertheless, the regression analysis can pick up on other temporal patterns of changes not exactly the same as our defined behavioral metric. This can be seen for SCP and beta activity projected onto the Direction axis, where it has the lowest value at ~20th percentile of the trial (not 50th percentile as assumed by the behavioral metric). To confirm that the analysis is not highly dependent on the precise timing definition of the behavioral metrics, we ran a control analysis, where the switching point was set at 30%tile (rather than 50%tile as in the original analysis). This control analysis resulted in a similar pattern of neural results (Figure R1).

Figure R1: Changing temporal behavior definition (switching point moved from 50th percentile to 30th percentile of percept duration) does not significantly alter the neural results. Compare to Figure 4—figure supplement 1, ‘Switch’ and “Direction’ Columns.

Author Response

Reviewer #1 (Public Review):

In computational modeling studies of behavioral data using reinforcement learning models, it has been implicitly assumed that parameter estimates generalize across tasks (generalizability) and that each parameter reflects a single cognitive function (interpretability). In this study, the authors examined the validity of these assumptions through a detailed analysis of experimental data across multiple tasks and age groups. The results showed that some parameters generalize across tasks, while others do not, and that interpretability is not sufficient for some parameters, suggesting that the interpretation of parameters needs to take into account the context of the task. Some researchers may have doubted the validity of these assumptions, but to my knowledge, no study has explicitly examined their validity. Therefore, I believe this research will make an important contribution to researchers who use computational modeling. In order to clarify the significance of this research, I would like the authors to consider the following points.

1) Effects of model misspecification

In general, model parameter estimates are influenced by model misspecification. Specifically, if components of the true process are not included in the model, the estimates of other parameters may be biased. The authors mentioned a little about model misspecification in the Discussion section, but they do not mention the possibility that the results of this study itself may be affected by it. I think this point should be discussed carefully.

The authors stated that they used state-of-the-art RL models, but this does not necessarily mean that the models are correctly specified. For example, it is known that if there is history dependence in the choice itself and it is not modeled properly, the learning rates depending on valence of outcomes (alpha+, alpha-) are subject to biases (Katahira, 2018, J Math Pscyhol). In the authors' study, the effect of one previous choice was included in the model as choice persistence, p. However, it has been pointed out that not including the effect of a choice made more than two trials ago in the model can also cause bias (Katahira, 2018). The authors showed taht the learning rate for positive RPE, alpha+ was inconsistent across tasks. But since choice persistence was included only in Task B, it is possible that the bias of alpha+ was different between tasks due to individual differences in choice persistence, and thus did not generalize.

However, I do not believe that it is necessary to perform a new analysis using the model described above. As for extending the model, I don't think it is possible to include all combinations of possible components. As is often said, every model is wrong, and only to varying degrees. What I would like to encourage the authors to do is to discuss such issues and then consider their position on the use of the present model. Even if the estimation results of this model are affected by misspecification, it is a fact that such a model is used in practice, and I think it is worthwhile to discuss the nature of the parameter estimates.

We thank the reviewer for this thoughtful question, and have added the following paragraph to the discussion section that is aims to address it:

“Another concern relates to potential model misspecification and its effects on model parameter estimates: If components of the true data-generating process are not included in a model (i.e., a model is misspecified), estimates of existing model parameters may be biased. For example, if choices have an outcome-independent history dependence that is not modeled properly, learning rate parameters have shown to be biased [63]. Indeed, we found that learning rate parameters were inconsistent across the tasks in our study, and two of our models (A and C) did not model history dependence in choice, while the third (model B) only included the effect of one previous choice (persistence parameter), but no multi-trial dependencies. It is hence possible that the differences in learning rate parameters between tasks were caused by differences in the bias induced by misspecification of history dependence, rather than a lack of generalization. Though pressing, however, this issue is difficult to resolve in practicality, because it is impossible to include all combinations of possible parameters in all computational models, i.e., to exhaustively search the space of possible models ("Every model is wrong, but to varying degrees"). Furthermore, even though our models were likely affected by some degree of misspecification, the research community is currently using models of this kind. Our study therefore sheds light on generalizability and interpretability in a realistic setting, which likely includes models with varying degrees of misspecification. Lastly, our models were fitted using robust computational tools and achieved good behavioral recovery (Fig. D.7), which also reduces the likelihood of model misspecification.“

2) Issue of reliability of parameter estimates

I think it is important to consider not only the bias in the parameter estimates, but also the issue of reliability, i.e., how stable the estimates will be when the same task is repeated with the same individual. For the task used in this study, has test-retest reliability been examined in previous studies? I think that parameters with low reliability will inevitably have low generalizability to other tasks. In this study, the use of three tasks seems to have addressed this issue without explicitly considering the reliability, but I would like the author to discuss this issue explicitly.

We thank the reviewer for this useful comment, and have added the following paragraph to the discussion section to address it:

“Furthermore, parameter generalizability is naturally bounded by parameter reliability, i.e., the stability of parameter estimates when participants perform the same task twice (test-retest reliability) or when estimating parameters from different subsets of the same dataset (split-half reliability). The reliability of RL models has recently become the focus of several parallel investigations [...], some employing very similar tasks to ours [...]. The investigations collectively suggest that excellent reliability can often be achieved with the right methods, most notably by using hierarchical model fitting. Reliability might still differ between tasks or models, potentially being lower for learning rates than other RL parameters [...], and differing between tasks (e.g., compare [...] to [...]). In this study, we used hierarchical fitting for tasks A and B and assessed a range of qualitative and quantitative measures of model fit for each task [...], boosting our confidence in high reliability of our parameter estimates, and the conclusion that the lack of between-task parameter correlations was not due to a lack of parameter reliability, but a lack of generalizability. This conclusion is further supported by the fact that larger between-task parameter correlations (r>0.5) than those observed in humans were attainable---using the same methods---in a simulated dataset with perfect generalization.“

3) About PCA

In this paper, principal component analysis (PCA) is used to extract common components from the parameter estimates and behavioral features across tasks. When performing PCA, were each parameter estimate and behavioral feature standardized so that the variance would be 1? There was no mention about this. It seems that otherwise the principal components would be loaded toward the features with larger variance. In addition, Moutoussis et al. (Neuron, 2021, 109 (12), 2025-2040) conducted a similar analysis of behavioral parameters of various decision-making tasks, but they used factor analysis instead of PCA. Although the authors briefly mentioned factor analysis, it would be better if they also mentioned the reason why they used PCA instead of factor analysis, which can consider unique variances.

To answer the reviewer's first question: We indeed standardized all features before performing the PCA. Apologies for missing to include this information - we have now added a corresponding sentence to the methods sections.

We also thank the reviewer for the mentioned reference, which is very relevant to our findings and can help explain the roles of different PCs. Like in our study, Moutoussis et al. found a first PC that captured variability in task performance, and subsequent PCs that captured task contrasts. We added the following paragraph to our manuscript:

“PC1 therefore captured a range of "good", task-engaged behaviors, likely related to the construct of "decision acuity" [...]. Like our PC1, decision acuity was the first component of a factor analysis (variant of PCA) conducted on 32 decision-making measures on 830 young people, and separated good and bad performance indices. Decision acuity reflects generic decision-making ability, and predicted mental health factors, was reflected in resting-state functional connectivity, but was distinct from IQ [...].”

To answer the reviewer's question about PCA versus FA, both approaches are relatively similar conceptually, and oftentimes share the majority of the analysis pipeline in practice. The main difference is that PCA breaks up the existing variance in a dataset in a new way (based on PCs rather than the original data features), whereas FA aims to identify an underlying model of latent factors that explain the observable features. This means that PCs are linear combinations of the original data features, whereas Factors are latent factors that give rise to the observable features of the dataset with some noise, i.e., including an additional error term.

However, in practice, both methods share the majority of computation in the way they are implemented in most standard statistical packages: FA is usually performed by conducting a PCA and then rotating the resulting solution, most commonly using the Varimax rotation, which maximizes the variance between features loadings on each factor in order to make the result more interpretable, and thereby foregoing the optimal solution that has been achieved by the PCA (which lack the error term). Maximum variance in feature loadings means that as many features as possible will have loadings close to 0 and 1 on each factor, reducing the number of features that need to be taken into account when interpreting this factor. Most relevant in our situation is that PCA is usually a special case of FA, with the only difference that the solution is not rotated for maximum interpretability. (Note that this rotation can be minor if feature loadings already show large variance in the PCA solution.)

To determine how much our results would change in practice if we used FA instead of PCA, we repeated the analysis using FA. Both are shown side-by-side below, and the results are quite similar:

We therefore conclude that our specific results are robust to the choice of method used, and that there is reason to believe that our PC1 is related to Moutoussis et al.’s F1 despite the differences in method.

Reviewer #2 (Public Review):

I am enthusiastic about the comprehensive approach, the thorough analysis, and the intriguing findings. This work makes a timely contribution to the field and warrants a wider discussion in the community about how computational methods are deployed and interpreted. The paper is also a great and rare example of how much can be learned from going beyond a meta-analytic approach to systematically collect data that assess commonly held assumptions in the field, in this case in a large data-driven study across multiple tasks. My only criticism is that at times, the paper misses opportunities to be more constructive in pinning down exactly why authors observe inconsistencies in parameter fits and interpretation. And the somewhat pessimistic outlook relies on some results that are, in my view at least, somewhat expected based on what we know about human RL. Below I summarize the major ways in which the paper's conclusions could be strengthened.

One key point the authors make concerns the generalizability of absolute vs. relative parameter values. It seems that at least in the parameter space defined by +LRs and exploration/noise (which are known to be mathematically coupled), subjects clustered similarly for tasks A and C. In other words, as the authors state, "both learning rate and inverse temperature generalized in terms of the relationships they captured between participants". This struck me as a more positive and important result than it was made out to be in the paper, for several reasons:

• As authors point out in the discussion, a large literature on variable LRs has shown that people adapt their learning rates trial-by-trial to the reward function of the environment; given this, and given that all models tested in this work have fixed learning rates, while the three tasks vary on the reward function, the comparison of absolute values seems a bit like a red-herring.

We thank the reviewers for this recommendation and have reworked the paper substantially to address the issue. We have modified the highlights, abstract, introduction, discussion, conclusion, and relevant parts of the results section to provide equal weight to the successes and failures of generalization.

Highlights:

● “RL decision noise/exploration parameters generalize in terms of between-participant variation, showing similar age trajectories across tasks.”

● “These findings are in accordance with previous claims about the developmental trajectory of decision noise/exploration parameters.”

Abstract:

● “We found that some parameters (exploration / decision noise) showed significant generalization: they followed similar developmental trajectories, and were reciprocally predictive between tasks.“

The introduction now introduces different potential outcomes of our study with more equal weight:

“Computational modeling enables researchers to condense rich behavioral datasets into simple, falsifiable models (e.g., RL) and fitted model parameters (e.g., learning rate, decision temperature) [...]. These models and parameters are often interpreted as a reflection of ("window into") cognitive and/or neural processes, with the ability to dissect these processes into specific, unique components, and to measure participants' inherent characteristics along these components.

For example, RL models have been praised for their ability to separate the decision making process into value updating and choice selection stages, allowing for the separate investigation of each dimension. Crucially, many current research practices are firmly based on these (often implicit) assumptions, which give rise to the expectation that parameters have a task- and model-independent interpretation and will seamlessly generalize between studies. However, there is growing---though indirect---evidence that these assumptions might not (or not always) be valid.

The following section lays out existing evidence in favor and in opposition of model generalizability and interpretability. Building on our previous opinion piece, which---based on a review of published studies---argued that there is less evidence for model generalizability and interpretability than expected based on current research practices [...], this study seeks to directly address the matter empirically.”

We now also provide more even evidence for both potential outcomes:

“Many current research practices are implicitly based on the interpretability and generalizability of computational model parameters (despite the fact that many researchers explicitly distance themselves from these assumptions). For our purposes, we define a model variable (e.g., fitted parameter, reward-prediction error) as generalizable if it is consistent across uses, such that a person would be characterized with the same values independent of the specific model or task used to estimate the variable. Generalizability is a consequence of the assumption that parameters are intrinsic to participants rather than task dependent (e.g., a high learning rate is a personal characteristic that might reflect an individual's unique brain structure). One example of our implicit assumptions about generalizability is the fact that we often directly compare model parameters between studies---e.g., comparing our findings related to learning-rate parameters to a previous study's findings related to learning-rate parameters. Note that such a comparison is only valid if parameters capture the same underlying constructs across studies, tasks, and model variations, i.e., if parameters generalize. The literature has implicitly equated parameters in this way in review articles [...], meta-analyses [...], and also most empirical papers, by relating parameter-specific findings across studies. We also implicitly evoke parameter generalizability when we study task-independent empirical parameter priors [...], or task-independent parameter relationships (e.g., interplay between different kinds of learning rates [...]), because we presuppose that parameter settings are inherent to participants, rather than task specific.

We define a model variable as interpretable if it isolates specific and unique cognitive elements, and/or is implemented in separable and unique neural substrates. Interpretability follows from the assumption that the decomposition of behavior into model parameters "carves cognition at its joints", and provides fundamental, meaningful, and factual components (e.g., separating value updating from decision making). We implicitly invoke interpretability when we tie model variables to neural substrates in a task-general way (e.g., reward prediction errors to dopamine function [...]), or when we use parameters as markers of psychiatric conditions (e.g., working-memory parameter and schizophrenia [...]). Interpretability is also required when we relate abstract parameters to aspects of real-world decision making [...], and generally, when we assume that model variables are particularly "theoretically meaningful" [...].

However, in midst the growing recognition of computational modeling, the focus has also shifted toward inconsistencies and apparent contradictions in the emerging literature, which are becoming apparent in cognitive [...], developmental [...], clinical [...], and neuroscience studies [...], and have recently become the focus of targeted investigations [...]. For example, some developmental studies have shown that learning rates increased with age [...], whereas others have shown that they decrease [...]. Yet others have reported U-shaped trajectories with either peaks [...] or troughs [...] during adolescence, or stability within this age range [...] (for a comprehensive review, see [...]; for specific examples, see [...]). This is just one striking example of inconsistencies in the cognitive modeling literature, and many more exist [...]. These inconsistencies could signify that computational modeling is fundamentally flawed or inappropriate to answer our research questions. Alternatively, inconsistencies could signify that the method is valid, but our current implementations are inappropriate [...]. However, we hypothesize that inconsistencies can also arise for a third reason: Even if both method and implementation are appropriate, inconsistencies like the ones above are expected---and not a sign of failure---if implicit assumptions of generalizability and interpretability are not always valid. For example, model parameters might be more context-dependent and less person-specific that we often appreciate [...]“

In the results section, we now highlight findings more that are compatible with generalization: “For α+, adding task as a predictor did not improve model fit, suggesting that α+ showed similar age trajectories across tasks (Table 2). Indeed, α+ showed a linear increase that tapered off with age in all tasks (linear increase: task A: β = 0.33, p < 0.001; task B: β = 0.052, p < 0.001; task C: β = 0.28, p < 0.001; quadratic modulation: task A: β = −0.007, p < 0.001; task B: β = −0.001, p < 0.001; task C: β = −0.006, p < 0.001). For noise/exploration and Forgetting parameters, adding task as a predictor also did not improve model fit (Table 2), suggesting similar age trajectories across tasks.”

“For both α+ and noise/exploration parameters, task A predicted tasks B and C, and tasks B and C predicted task A, but tasks B and C did not predict each other (Table 4; Fig. 2D), reminiscent of the correlation results that suggested successful generalization (section 2.1.2).”

“Noise/exploration and α+ showed similar age trajectories (Fig. 2C) in tasks that were sufficiently similar (Fig. 2D).” And with respect to our simulation analysis (for details, see next section):

“These results show that our method reliably detected parameter generalization in a dataset that exhibited generalization. ”

We also now provide more nuance in our discussion of the findings:

“Both generalizability [...] and interpretability (i.e., the inherent "meaningfulness" of parameters) [...] have been explicitly stated as advantages of computational modeling, and many implicit research practices (e.g., comparing parameter-specific findings between studies) showcase our conviction in them [...]. However, RL model generalizability and interpretability has so far eluded investigation, and growing inconsistencies in the literature potentially cast doubt on these assumptions. It is hence unclear whether, to what degree, and under which circumstances we should assume generalizability and interpretability. Our developmental, within-participant study revealed a nuanced picture: Generalizability and interpretability differed from each other, between parameters, and between tasks.”

“Exploration/noise parameters showed considerable generalizability in the form of correlated variance and age trajectories. Furthermore, the decline in exploration/noise we observed between ages 8-17 was consistent with previous studies [13, 66, 67], revealing consistency across tasks, models, and research groups that supports the generalizability of exploration / noise parameters. However, for 2/3 pairs of tasks, the degree of generalization was significantly below the level of generalization expected for perfect generalization. Interpretability of exploration / noise parameters was mixed: Despite evidence for specificity in some cases (overlap in parameter variance between tasks), it was missing in others (lack of overlap), and crucially, parameters lacked distinctiveness (substantial overlap in variance with other parameters).”

“Taken together, our study confirms the patterns of generalizable exploration/noise parameters and task-specific learning rate parameters that are emerging from the literature [13].”

• Regarding the relative inferred values, it's unclear how high we really expect correlations between the same parameter across tasks to be. E.g., if we take Task A and make a second, hypothetical, Task B by varying one feature at a time (say, stochasticity in reward function), how correlated are the fitted LRs going to be? Given the different sources of noise in the generative model of each task and in participant behavior, it is hard to know whether a correlation coefficient of 0.2 is "good enough" generalizability.

We thank the reviewer for this excellent suggestion, which we think helped answer a central question that our previous analyses had failed to address, and also provided answers to several other concerns raised by both reviewers in other section. We have conducted these additional analyses as suggested, simulating artificial behavioral data for each task, fitting these data using the models used in humans, repeating the analyses performed on humans on the new fitted parameters, and using bootstrapping to statistically compare humans to the hence obtained ceiling of generalization. We have added the following section to our paper, which describes the results in detail:

“Our analyses so far suggest that some parameters did not generalize between tasks, given differences in age trajectories (section 2.1.3) and a lack of mutual prediction (section 2.1.4). However, the lack of correspondence could also arise due to other factors, including behavioral noise, noise in parameter fitting, and parameter trade-offs within tasks. To rule these out, we next established the ceiling of generalizability attainable using our method.

We established the ceiling in the following way: We first created a dataset with perfect generalizability, simulating behavior from agents that use the same parameters across all tasks (suppl. Appendix E). We then fitted this dataset in the same way as the human dataset (e.g., using the same models), and performed the same analyses on the fitted parameters, including an assessment of age trajectories (suppl. Table E.8) and prediction between tasks (suppl. Tables E.9, E.10, and E.11). These results provide the practical ceiling of generalizability. We then compared the human results to this ceiling to ensure that the apparent lack of generalization was valid (significant difference between humans and ceiling), and not in accordance with generalization (lack of difference between humans and ceiling).

Whereas humans had shown divergent trajectories for parameter alpha- (Fig. 2B; Table 1), the simulated agents did not show task differences for alpha- or any other parameter (suppl. Fig E.8B; suppl. Table E.8, even when controlling for age (suppl. Tables E.9 and E.10), as expected from a dataset of generalizing agents. Furthermore, the same parameters were predictive between tasks in all cases (suppl. Table E.11). These results show that our method reliably detected parameter generalization in a dataset that exhibited generalization.

Lastly, we established whether the degree of generalization in humans was significantly different from agents. To this aim, we calculated the Spearman correlations between each pair of tasks for each parameter, for both humans (section 2.1.2; suppl. Fig. H.9) and agents, and compared both using bootstrapped confidence intervals (suppl. Appendix E). Human parameter correlations were significantly below the ceiling for all parameters except alpha+ (A vs B) and epsilon / 1/beta (A vs C; suppl. Fig. E.8C). This suggests that humans were within the range of maximally detectable generalization in two cases, but showed less-than-perfect generalization between other task combinations and for parameters Forgetting and alpha-.”

• The +LR/inverse temp relationship seems to generalize best between tasks A/C, but not B/C, a common theme in the paper. This does not seem surprising given that in A and C there is a key additional task feature over the bandit task in B -- which is the need to retain state-action associations. Whether captured via F (forgetting) or K (WM capacity), the cognitive processes involved in this learning might interact with LR/exploration in a different way than in a task where this may not be necessary.

We thank the reviewer for this comment, which raises an important issue. We are adding the specific pairwise correlations and scatter plots for the pairs of parameters the reviewer asked about below (“bf_alpha” = LR task A; “bf_forget” = F task A; “rl_forget” = F task C; “rl_log_alpha” = LR task C; “rl_K” = WM capacity task C):

Within tasks:

Between tasks:

To answer the question in more detail, we have expanded our section about limitations stemming from parameter tradeoffs in the following way:

“One limitation of our results is that regression analyses might be contaminated by parameter cross-correlations (sections 2.1.2, 2.1.3, 2.1.4), which would reflect modeling limitations (non-orthogonal parameters), and not necessarily shared cognitive processes. For example, parameters alpha and beta are mathematically related in the regular RL modeling framework, and we observed significant within-task correlations between these parameters for two of our three tasks (suppl. Fig. H.10, H.11). This indicates that caution is required when interpreting correlation results. However, correlations were also present between tasks (suppl. Fig. H.9, H.11), suggesting that within-model trade-offs were not the only explanation for shared variance, and that shared cognitive processes likely also played a role.

Another issue might arise if such parameter cross-correlations differ between models, due to the differences in model parameterizations across tasks. For example, memory-related parameters (e.g., F, K in models A and C) might interact with learning- and choice-related parameters (e.g., alpha+, alpha-, noise/exploration), but such an interaction is missing in models that do not contain memory-related parameters (e.g., task B). If this indeed the case, i.e., parameters trade off with each other in different ways across tasks, then a lack of correlation between tasks might not reflect a lack of generalization, but just the differences in model parameterizations. Suppl. Fig. \ref{figure:S2AlphaBetaCorrelations} indeed shows significant, medium-sized, positive and negative correlations between several pairs of Forgetting, memory-related, learning-related, and exploration parameters (though with relatively small effect sizes; Spearman correlation: 0.17 < |r| < 0.22).

The existence of these correlations (and differences in correlations between tasks) suggest that memory parameters likely traded off with each other, as well as with other parameters, which potentially affected generalizability across tasks. However, some of the observed correlations might be due to shared causes, such as a common reliance on age, and the regression analyses in the main paper control for these additional sources of variance, and might provide a cleaner picture of how much variance is actually shared between parameters.

Furthermore, correlations between parameters within models are frequent in the existing literature, and do not prevent researchers from interpreting parameters---in this sense, the existence of similar correlations in our study allows us to address the question of generalizability and interpretability in similar circumstances as in the existing literature.”

• More generally, isn't relative generalizability the best we would expect given systematic variation in task context? I agree with the authors' point that the language used in the literature sometimes implies an assumption of absolute generalizability (e.g. same LR across any task). But parameter fits, interactions, and group differences are usually interpreted in light of a single task+model paradigm, precisely b/c tasks vary widely across critical features that will dictate whether different algorithms are optimal or not and whether cognitive functions such as WM or attention may compensate for ways in which humans are not optimal. Maybe a more constructive approach would be to decompose tasks along theoretically meaningful features of the underlying Markov Decision Process (which gives a generative model), and be precise about (1) which features we expect will engage additional cognitive mechanisms, and (2) how these mechanisms are reflected in model parameters.

We thank the reviewer for this comment, and will address both points in turn:

(1) We agree with the reviewer's sentiment about relative generalizability: If we all interpreted our models exclusively with respect to our specific task design, and never expected our results to generalize to other tasks or models, there would not be a problem. However, the current literature shows a different pattern: Literature reviews, meta-analyses, and discussion sections of empirical papers regularly compare specific findings between studies. We compare specific parameter values (e.g., empirical parameter priors), parameter trajectories over age, relationships between different parameters (e.g., balance between LR+ and LR-), associations between parameters and clinical symptoms, and between model variables and neural measures on a regular basis. The goal of this paper was really to see if and to what degree this practice is warranted. And the reviewer rightfully alerted us to the fact that our data imply that these assumptions might be valid in some cases, just not in others.

(2) With regard to providing task descriptions that relate to the MDP framework, we have included the following sentence in the discussion section:

“Our results show that discrepancies are expected even with a consistent methodological pipeline, and using up-to-date modeling techniques, because they are an expected consequence of variations in experimental tasks and computational models (together called "context"). Future research needs to investigate these context factors in more detail. For example, which task characteristics determine which parameters will generalize and which will not, and to what extent? Does context impact whether parameters capture overlapping versus distinct variance? A large-scale study could answer these questions by systematically covering the space of possible tasks, and reporting the relationships between parameter generalizability and distance between tasks. To determine the distance between tasks, the MDP framework might be especially useful because it decomposes tasks along theoretically meaningful features of the underlying Markov Decision Process.“

Another point that merits more attention is that the paper pretty clearly commits to each model as being the best possible model for its respective task. This is a necessary premise, as otherwise, it wouldn't be possible to say with certainty that individual parameters are well estimated. I would find the paper more convincing if the authors include additional information and analysis showing that this is actually the case.

We agree with the sentiment that all models should fit their respective task equally well. However, there is no good quantitative measure of model fit that is comparable across tasks and models - for example, because of the difference in difficulty between the tasks, the number of choices explained would not be a valid measure to compare how well the models are doing across tasks. To address this issue, we have added the new supplemental section (Appendix C) mentioned above that includes information about the set of models compared, and explains why we have reason to believe that all models fit (equally) well. We also created the new supplemental Figure D.7 shown above, which directly compares human and simulated model behavior in each task, and shows a close correspondence for all tasks. Because the quality of all our models was a major concern for us in this research, we also refer the reviewer and other readers to the three original publications that describe all our modeling efforts in much more detail, and hopefully convince the reviewer that our model fitting was performed according to high standards.

I am particularly interested to see whether some of the discrepancies in parameter fits can be explained by the fact that the model for Task A did not account for explicit WM processes, even though (1) Task A is similar to Task C (Task A can be seen as a single condition of Task C with 4 states and 2 possible visible actions, and stochastic rather than deterministic feedback) and (2) prior work has suggested a role for explicit memory of single episodes even in stateless bandit tasks such as Task B.

We appreciate this very thoughtful question, which raises several important issues. (1) As the reviewer said, the models for task A and task C are relatively different even though the underlying tasks are relatively similar (minus the differences the reviewer already mentioned, in terms of visibility of actions, number of actions, and feedback stochasticity). (2) We also agree that the model for task C did not include episodic memory processes even though episodic memory likely played a role in this task, and agree that neither the forgetting parameters in tasks A and C, nor the noise/exploration parameters in tasks A, B, and C are likely specific enough to capture all the memory / exploration processes participants exhibited in these tasks.

However, this problem is difficult to solve: We cannot fit an episodic-memory model to task B because the task lacks an episodic-memory manipulation (such as, e.g., in Bornstein et al., 2017), and we cannot fit a WM model to task A because it lacks the critical set-size manipulation enabling identification of the WM component (modifying set size allows the model to identify individual participants’ WM capacities, so the issue cannot be avoided in tasks with only one set size). Similarly, we cannot model more specific forgetting or exploration processes in our tasks because they were not designed to dissociate these processes. If we tried fitting more complex models that include these processes to these tasks, they would most likely lose in model comparison because the increased complexity would not lead to additional explained behavioral variance, given that the tasks do not elicit the relevant behavioral patterns. Because the models therefore do not specify all the cognitive processes that participants likely employ, the situation described by the reviewer arises, namely that different parameters sometimes capture the same cognitive processes across tasks and models, while the same parameters sometimes capture different processes.

And while the reviewer focussed largely on memory-related processes, the issue of course extends much further: Besides WM, episodic memory, and more specific aspects of forgetting and exploration, our models also did not take into account a range of other processes that participants likely engaged in when performing the tasks, including attention (selectivity, lapses), reasoning / inference, mental models (creation and use), prediction / planning, hypothesis testing, etc., etc. In full agreement with the reviewer’s sentiment, we recently argued that this situation is ubiquitous to computational modeling, and should be considered very carefully by all modelers because it can have a large impact on model interpretation (Eckstein et al., 2021).

If we assume that many more cognitive processes are likely engaged in each task than are modeled, and consider that every computational model includes just a small number of free parameters, parameters then necessarily reflect a multitude of cognitive processes. The situation is additionally exacerbated by the fact that more complex models become increasingly difficult to fit from a methodological perspective, and that current laboratory tasks are designed in a highly controlled and consequently relatively simplistic way that does not lend itself to simultaneously test a variety of cognitive processes.

The best way to deal with this situation, we think, is to recognize that in different contexts (e.g., different tasks, different computational models, different subject populations), the same parameters can capture different behaviors, and different parameters can capture the same behaviors, for the reasons the reviewer lays out. Recognizing this helps to avoid misinterpreting modeling results, for example by focusing our interpretation of model parameters to our specific task and model, rather than aiming to generalize across multiple tasks. We think that recognizing this fact also helps us understand the factors that determine whether parameters will capture the same or different processes across contexts and whether they will generalize. This is why we estimated here whether different parameters generalize to different degrees, which other factors affect generalizability, etc. Knowing the practical consequences of using the kinds of models we currently use will therefore hopefully provide a first step in resolving the issues the reviewer laid out.

It is interesting that one of the parameters that generalizes least is LR-. The authors make a compelling case that this is related to a "lose-stay" behavior that benefits participants in Task B but not in Task C, which makes sense given the probabilistic vs deterministic reward function. I wondered if we can rule out the alternative explanation that in Task C, LR- could reflect a different interpretation of instructions vis. a vis. what rewards indicate - do authors have an instruction check measure in either task that can be correlated with this "lose-stay" behavior and with LR-? And what does the "lose-stay" distribution look like, for Task C at least? I basically wonder if some of these inconsistencies can be explained by participants having diverging interpretations of the deterministic nature of the reward feedback in Task C. The order of tasks might matter here as well -- was task order the same across participants? It could be that due to the within-subject design, some participants may have persisted in global strategies that are optimal in Task B, but sub-optimal in Task C.

The PCA analysis adds an interesting angle and a novel, useful lens through which we can understand divergence in what parameters capture across different tasks. One observation is that loadings for PC2 and PC3 are strikingly consistent for Task C, so it looks more like these PCs encode a pairwise contrast (PC2 is C with B and PC2 is C with A), primarily reflecting variability in performance - e.g. participants who did poorly on Task C but well on Task B (PC2) or Task A (PC3). Is it possible to disentangle this interpretation from the one in the paper? It also is striking that in addition to performance, the PCs recover the difference in terms of LR- on Task B, which again supports the possibility that LR- divergence might be due to how participants handle probabilistic vs. deterministic feedback.

We appreciate this positive evaluation of our PCA and are glad that it could provide a useful lens for understanding parameters. We also agree to the reviewer's observation that PC2 and PC3 reflect task contrasts (PC2: task B vs task C; PC3: task A vs task C), and phrase it in the following way in the paper:

“PC2 contrasted task B to task C (loadings were positive / negative / near-zero for corresponding features of tasks B / C / A; Fig. 3B). PC3 contrasted task A to both B and C (loadings were positive / negative for corresponding features on task A / tasks B and C; Fig. 3C).”

Hence, the only difference between our interpretation and the reviewer’s seems to be whether PC3 contrasts task C to task B as well as task A, or just to task A. Our interpretation is supported by the fact that loadings for tasks A and C are quite similar on PC3; however, both interpretations seem appropriate.

We also appreciate the reviewer's positive evaluation of the fact that the PCA reproduces the differences in LR-, and its relationship to probabilistic/deterministic feedback. The following section reiterates this idea:

“alpha- loaded positively in task C, but negatively in task B, suggesting that performance increased when participants integrated negative feedback faster in task C, but performance decreased when they did the same in task B. As mentioned before, contradictory patterns of alpha- were likely related to task demands: The fact that negative feedback was diagnostic in task C likely favored fast integration of negative feedback, while the fact that negative feedback was not diagnostic in task B likely favored slower integration (Fig. 1E). This interpretation is supported by behavioral findings: "Lose-stay" behavior (repeating choices that produce negative feedback) showed the same contrasting pattern as alpha- on PC1. It loaded positively in task B, showing Lose-stay behavior benefited performance, but it loaded negatively on task C, showing that it hurt performance (Fig. 3A). This supports the claim that lower alpha- was beneficial in task B, while higher alpha- was beneficial in task C, in accordance with participant behavior and developmental differences.“

Author Response:

Reviewer #1 (Public Review):

The authors make juxtacellular recordings on awake mice, which should yield clear responses of actions potentials, and employ a number of manipulations to silence pathways. They also record from a "non"-whisker secondary thalamic region, LP, as a null hypothesis to establish if certain effects are related to "behavior" - read arousal or saliency". I have no major qualms.

In light of Petersen's paper (Cell Reports 2014) on cholinergic effects on spike rates in primary whisker somatosensory cortex, I can imagine that the authors considered measuring from cholinergic neurons in nucleus basalis during whisking. I'll assume that this is easier said than done. As such, the current manuscript passes my threshold for publication modulo issues raised below that are related to anatomy.

The cholinergic experiments are an interesting idea. However, inactivation of S1 did not change the relationship between POm and whisking, suggesting that cholinergic modulation of S1 and thereby corticothalamic output are not the key mechanism. It is conceivable that acetylcholine modulates POm directly, but the critical experiments would involve extensive manipulations of POm (a whole additional study). Nevertheless, we have added a reference to Eggermann & Petersen and discussed this issue further in the revision.

I provide a figure-by-figure critique:

(1) Recent work from Deschênes et al (Neuron 2016) points to a description of whisking in terms of Angle = Set-point_angle - Whisking-amplitude [1 + cosine(Phase - Phase_0)], where Phase is a rapidly varying, typically rhythmic function of time. Why not use this notation as opposed to yet another descriptive statistic and report the kinetics as the time averaged parameters , i.e., the most forward position, and ,Whisking-amplitude>, i.e., the half-amplitude of the average whisk?

We are not entirely sure what the reviewer means by “another descriptive statistic” as we do not introduce new approaches for analyzing whisking in this paper. (Perhaps the reviewer refers to “median angle”, which is an average of all the whisker positions on a single frame. We use this measurement because our videos contain the entire whisker field rather than just a single whisker as in our other studies, e.g. Hong et al 2018, Rodgers et al 2021). We based our parameterization of median angle on two publications: Hill et al (2011 Neuron) and Moore et al (2015 PLoS Biology). Moore et al describes whisking as a function of phase, amplitude, and midpoint:

where 𝜃(t) is the median whisker angle at time 𝑡 , 𝜙 is the phase as computed by the Hilbert transform of the filtered whisker angle, 𝜃^Amplitude is the difference between the most protracted and retracted whisker positions over a single cycle, and 𝜃^midpoint is the central angle of a single whisk cycle. As we understand the reviewer, we are using the formulation they describe. We are happy to consider alternate formulations if we are missing something.

A critical issue is to confirm where the recording were made. This the authors should supply at least a typical record of anatomy from their POm as well as VPM and LP recording. The beauty of the juxtacellular technique is that neurons can be labeling after the recording

We used the juxtacellular recording technique for its superior recording quality. We did not label individual cells after recording because we recorded multiple cells per animal over several days. The number of cells would complicate matching of filled cells to recorded physiological data, and biotin filling is not stable over multiple days (beyond 36 hours). Instead, as described in the original manuscript, we tracked the relative locations of all inserted pipettes and labeled the final track with DiI. Cells were roughly localized along the tracks using relative microdrive depths. Due to the morphological homogeneity of thalamic neurons, filling individual cells would not be more informative than labelling the recording site with DiI. New Figure 1 – figure supplement 1 includes representative histology images from our recordings in POm, VPM, LP, and M1.

(2) Did the authors make sure that the mystacial pad is not moving by imaging the pad as opposed to just the shaft of the whiskers? The top view in Figure 1A makes this hard to check.

To address this concern, we provide new data, in which both the cut and uncut sides of the face of mice were imaged. We measured the movement of the mystacial pads as motion energy – the mean absolute difference in pixel values across video frames. The motor nerve surgery almost completely abolished movement of the mystacial pad. A new figure panel (Figure 2B) demonstrates the movement of the normal and paralyzed mystacial pads.

Further, did the authors perform post-hoc anatomy to insure that both the ramus buccolabialis inferior and ramus buccolabialis superior muscles were cut? This is critical; it is also easy to leave the maxillolabialis (external retractor) innervated if the cut is too far rostral.

We did not attempt to cut muscles. We only cut the motor nerve. We did not examine the face post mortem, as it was obvious that both whisker and mystacial pad movement were absent (as in new Figure 2B).

(3/4) As relevant background, the text should note that whisker primary motor cortex maintains a copy of the envelope of the whisking, i.e., an ill-defined summation of set-point and amplitudes, even if the sensory input (Ahrens & Kleinfeld J Neurophysiol 2004) or motor output (Fee et al. J Neurophysiol 1997) in the periphery are cut.

The Results text now cites these papers as motivation for the experiments of Figure 3.

(6/7) Same comments in (1) in whisking parameters and anatomy.

As we discussed in (1), we are using the conventional parameterization of others. Histological examples are now included in Figure 1 – figure supplement 1.

Reviewer #3 (Public Review):

Previous studies in urethane-anesthetized rats (PMID 16605304) proposed that POm cells code whisker movements. This was observed using "artificial whisking" procedures (stimulating the motor nerve to produce a whisking-like movement). It has been clear for some time now that there are substantial (obvious) differences between this procedure and natural whisking. In addition, under urethane-anesthesia animals are in a sleep-like state that is very dissimilar to waking (although some work has tested the effect of network state on artificial whisking responses in both primary thalamus and cortex; see 25505118). In the present study, the authors measured activity in POm cells during whisking in awake (head-fixed) mice to determine if they code whisking movement. However, this seems to have already been done previously. For instance, Moore et al (2015; 26393890) found that coding of whisking in the ascending paralemniscal pathway, including POm, is "relatively poor" (as stated in the abstract), which is the same conclusion reached in the present study. The authors should clarify the main differences observed in whisking coding between their study and previous work.

The authors then focused on the idea that POm codes behavioral state. However, many studies have previously determined that state has a great impact on thalamocortical dynamics; thalamic cells are very sensitive to state including cells in primary whisker thalamic nuclei, such as VPM, and these effects can be produced by neuromodulators (see work by Castro-Alamancos' group, for example, 16306412). There is nothing special about VPM in this regard; other thalamic sensory nuclei are also sensitive to behavioral state and neuromodulators. Therefore, the observation that POm and LP cells are sensitive to state is unsurprising. It is also known that these thalamic state changes have a great impact on the state of the cortex (see 20053845), which seems very relevant to the main conclusion. The POm has to be doing something different than coding behavioral state since most thalamic nuclei do this. The study did not identify the role of POm, which certainly has to be different from LP (otherwise, why would these nuclei be differentiated?). POm is unlikely to be specialized for monitoring state since this is done by most of the thalamus -including VPM, which projects to the same cortical region. Thus, while it is interesting that most of the whisker-related activity in POm is state-dependent, the study does not clarify the role of POm.

We have added the references we did not already include to our text and improved our discussion.

Prior studies (such as Moore et al 2015 and Urbain et al 2015) have previously characterized the encoding of whisker motion in POm. Indeed, we note the consistency between our results and such studies in both the introduction and conclusion. Here we expand upon prior studies to directly test two prominent hypotheses about the role of the paralemniscal pathway: that it encodes sensory reafference, and that it inherits a motor efference copy from cortical and subcortical regions. We present the impact of several manipulations of the vibrissal system (facial paralysis, cortical silencing, and lesion of superior colliculus) on thalamic activity that, to our knowledge, have not been previously reported. Moreover, we leveraged a novel comparison of POm and LP to test whether movement‐correlations of POm reflected true motor modulation or rather state dependency. We have provided evidence that the coupling of POm activity to whisking reflects state rather than motor signals. We never suggested that POm is a unique monitor of behavioral state. We suggest instead that secondary thalamic nuclei may be state‐modulated and have specific impacts on response gain and plasticity in their respective cortical areas. While our work is consistent with previous studies, we believe these results are novel extensions of past work.

The main strength of the study is that it was performed in awake mice with behavioral state monitoring, which contributes to the current understanding of active whisking coding in the complex network of the vibrissa system.

In our opinion, the main strength of our study is its multiple manipulations to test the sources of modulation and the leveraging of a POm‐LP comparison. We have revised the text to reinforce these points.

Author Response

Reviewer #3 (Public Review):

Q1) The manuscript reports that in vitro fertilization (including in vitro culture) of mouse embryos seemingly originates metabolic alterations probably caused by enhanced oxidative stress compared to in vivo development. Such alterations apparently increase anaerobic glycolysis, as evidenced by altered pH and lactate levels, and remain after birth, as evidenced by altered protein abundance of MCT1 and LDHB.

The manuscript concludes that IVF alters embryo metabolism, increasing oxidative damage and glycolytic activity. The topic is interesting but I consider that the conclusions are not well supported by the experiments:

1) In vivo generated blastocysts are analyzed at a more advanced developmental stage than their in vitro counterparts as evidenced by their increased cell number (70 vs. 50 cells). In this regard, the developmental timing when in vitro generated blastocysts are collected is undisclosed in the Materials and methods. This has an obvious effect on all experiments as the differences observed may be stage-specific rather than IVF vs. in vivo.

A1) Thank you for the comment. The reviewer is correct and it is indeed well known that in vitro fertilization and embryo culture results in profound changes to the embryo. Overall, embryos generated in vitro are delayed compared to embryos generated in vivo. To control for this, as done in our past publications (Belli 2019; Bloise 2014; Delle Piane 2010; Giritharan 2012; Giritharan 2010; Giritharan 2006; Giritharan 2007; Rinaudo 2006; Rinaudo 2004), or by others (Doherty 2000; Ecker 2004; Weinerman 2016), we limited the analysis to expanded blastocysts of similar morphology (under microscopic examination) in all of the groups. Therefore the embryos appeared morphological similar in all of the groups. As an alternative, we could have waited longer time in vitro, but this would have resulted in embryo hatching and being not morphological similar to in vivo embryos. In addition, the 2 IVF groups provide an internal control: embryos were at the same developmental stage, but showed significant changes in metabolism and cell numbers. (96 hours of culture +13-14hours for egg collection+ 4hours of fertilization= time post HCG administration)

We have added this information as follows: Line 377-382: To control for the known delay in development after culture in vitro, for all experiments, only expanded blastocysts of similar morphology were used, as done before (Doherty 2000; Rinaudo 2006; Rinaudo 2004). The in vivo-generated blastocysts were isolated by flushing 96-98 hours after hCG administration. IVF- 5% O2 and 20% O2 generated embryos reached the blastocyst stage after 96-98 hours following in vitro culture and 113-114 hours after hCG administration, respectively.

Q2) Several methods are not reliable to quantify the parameters analyzed. For instance, determining protein content by immunofluorescence has been largely shown to be misleading as immunofluorescence can be affected by multiple parameters. Intracellular pH was also analyzed by an assay also based on immunofluorescence, which can also be affected by embryo size (the blastocoel is a call-devoid cavity). These analyses are not reliable.

A2) Thank you for the comments.

We appreciate the comments and concerns. Any single method can result in error and possible bias. Immunofluorescence analysis is a robust method that has been used to analyze the distribution of proteins in cells or tissues. For instance, oxidative stress (Liu et al., 2022, Reprod Domest Anim), several signaling molecule (Spirkova et al., 2022, Biol Reprod) and DNA methylation level (Diaz et al, 2021, Fron Gent) have been measured by immunofluorescence in preimplantation embryos and oocytes. It our study, to minimize errors, we followed exactly the same protocol and we found immunofluorescence to be reliable. In addition, global proteomics analysis of blastocysts provide partial independent confirmation of our results. While LDH-A and MCT1 were not detected, LDH-B was detected and found to be lower in IVF blastocysts, exactly as show by IF studies. Finally, western blot analysis of adult tissues confirmed reduction in LDH-B and MCT-1 levels.

These comments have been added to the discussion as follows:

Line 299-302: Unsupervised global proteomics analysis revealed that LDH-B was downregulated in IVF embryos. We confirmed these results by performing immunofluorescence studies. In addition we found that IVF embryos showed downregulation of both LDHA and B and of the monocarboxylate transporter, MCT 1, providing an explanation for the increase in their lactate levels

Regarding pH measurement: to control for the possible variation in blastocoel size in different embryos, we compared immunofluorescence level of only the inner cell mass and trophoblast region of blastocysts and excluded the blastocoel region.

This clarification has been added to the method section as follow:

Line 488-491: To control for the possible variation in blastocoel size in different embryos, we compared immunofluorescence level of only the inner cell mass and trophoblast region of blastocysts and excluded the blastocoel region.

Q3) Identifying proteins and metabolites in such small samples is technically difficult and error-prone, requiring validation by alternative techniques.

We appreciate the comments and concerns. Any single method can result in error and possible bias. Immunofluorescence analysis is a robust method that has been used to analyze the distribution of proteins in cells or tissues. For instance, oxidative stress (Liu 2022), several signaling molecule (Spirkova 2022) and DNA methylation level (Diaz 2021) have been measured by immunofluorescence in preimplantation embryos and oocytes. It our study, to minimize errors, we followed exactly the same protocol and we found immunofluorescence to be reliable. In addition, global proteomics analysis of blastocysts (triplicate for each group; n=100 blastocysts for each replicate; total 900 embryos). provide partial independent confirmation of our results. While LDH-A and MCT1 were not detected, LDH-B was detected and found to be lower in IVF blastocysts, exactly as show by IF studies. Finally, western blot analysis of adult tissues confirmed reduction in LDH-B and MCT-1 levels.

These comments have been added to the discussion as follows:

Line 299-302: Unsupervised global proteomics analysis revealed that LDH-B was downregulated in IVF embryos. We confirmed these results by performing immunofluorescence studies. In addition we found that IVF embryos showed downregulation of both LDHA and B and of the monocarboxylate transporter, MCT 1, providing an explanation for the increase in their lactate levels

Q4) Given the small size of these embryos (~80 µm diameter), it is unclear how they can alter significantly the composition of 500 µl of medium (106 their own volume).

To collect 300 blastocysts, we performed multiple IVF, each IVF resulting in 10-20 blastocysts cultured in 30 microliters of media. While intracellular lactate and pyruvate were performed on the embryos collected, the media from different experiments was pooled to a final 500 microliter volume. Lactate and pyruvate levels were measured in this final volume for each group of embryo (FB, IVF5% and IVF20%)

This has been clarified in the method section as follows:

Line 516-519: To collect 300 blastocysts, we performed multiple IVF, each IVF resulting in 10-20 blastocysts cultured in 30 microliters of media. While intracellular lactate and pyruvate were performed on the embryos collected, the media from different experiments was pooled to a final 500 microliter volume.

Q5) The metabolic changes observed in the offspring lack a mechanistic explanation.

Thank you for the comment. We can formulate a hypothesis in which (Figure 8) oxidative stress from in vitro condition increase ROS and induce oxidative damage resulting in a shift toward Warburg metabolism, given that lactate is a critical energy source (Brooks, 2018). The higher intracellular lactate levels will likely induce epigenetic changes, to favor Warburg metabolism during development, as an embryonic attempt to optimize growth based on the environment predicted to be experienced in the future. When the environment does not match the prediction, disease risk increases (Godfrey 2007). Low lactate would be beneficial in a setting of low food resources because it could favor lipolysis (Brooks, 2020). In fact, lactate activates the hydroxycarboxylic acid receptor 1 (HCAR1), a G protein-coupled receptor, which in turn inhibits lipolysis in fat cells via cAMP and CREB (Liu 2009). However, since there is an abundance of food in our society, this mismatch could predispose IVF concepti to develop chronic disease like glucose intolerance.

This hypothesis has been added to line 333-344:

In summary, we can formulate a hypothesis in which (Figure 8) oxidative stress from in vitro condition increase ROS and induce oxidative damage resulting in a shift toward Warburg metabolism, given that lactate is a critical energy source (Brooks, 2018). The higher intracellular lactate levels will likely induce epigenetic changes, to favor Warburg metabolism during development, as an embryonic attempt to optimize growth based on the environment predicted to be experienced in the future. When the environment does not match the prediction, disease risk increases (Godfrey 2007). Low lactate would be beneficial in a setting of low food resources because it could favor lipolysis (Brooks, 2020). In fact, lactate activates the hydroxycarboxylic acid receptor 1 (HCAR1), a G protein-coupled receptor in turn inhibits lipolysis in fat cells via cAMP and CREB (Liu 2009). However, since there is an abundance of food in our society, this mismatch could predispose IVF concepti to develop chronic disease like glucose intolerance.

Author Response

Public Evaluation Summary

The authors aim to tackle a fundamental question with their study: whether there is a direct age-associated increase of transcriptional noise. To investigate this question, they develop tools to analyze single-cell sequencing data from mouse and human aging datasets. Ultimately, application of their novel tool (Scallop) suggests that transcriptional noise does not change with age, changes in transcriptional noise can be attributed to other sources such as subtle shifts in cell identity. This study is in principle of broad interest, but it currently lacks a definitive demonstration of the robustness of Scallop. Systematic testing of this new package would ultimately strengthen the key conclusion of the work and give additional users more confidence when using the tool to estimate expression noise.

We have now attempted to further demonstrate the robustness of Scallop by performing a more systematic analysis and a side-by-side comparison to other existing methods using a set of artificially generated datasets. These analyses have resulted in the inclusion of six supplementary figures that are presented in the subsections Scallop membership score accurately identifies transcriptionally noisy cells, Ability to detect noisy cells within cell types, Effect of cellular composition, Effect of dataset size, Effect of feature expression and Effect of cell type marker expression within the Results section of the revised manuscript.

We have also included a supplementary figure showing an in-depth analysis of a dataset where ageassociated increase in transcriptional noise was detected using alternative methods, but whose closer dissection has revealed that the difference in noise is due to a single donor and to the choice of methods. We discuss this is in the subsection Distance-to-centroid methods detect transcriptionally stable cell subtypes as transcriptional noise within the Results section.

Finally, we have revised the manuscript to clarify the main points raised by the reviewers: the definition of transcriptional noise, the reasoning behind the choice of the single-cell aging datasets and Leiden’s rationale. Also, we have expanded the description of the method to make the definition of membership score more clear to the readers, and discussed the implications of our main findings (a lack of evidence for age-related transcriptional noise) in the broader context of theories of aging.

Reviewer #1 (Public Review):

In the present study, Ibanez-Sole et al evaluate transcriptional noise across aging and tissues in several publicly available mouse and human datasets. Initially, the authors compare 4 generalized approaches to quantify transcriptional noise across cell types and later implement a new approach which uses iterative clustering to assess cellular noise. Based on implementation of this approach (scallop), the authors survey noise across seven sc-seq datasets relevant for aging. Here, the authors conclude that enhanced transcriptional noise is not a hallmark of aging, rather changes in cell identity and abundances, namely immune and endothelial cells. The development of new tools to quantify transcriptional noise from sc-seq data presents appeal, as these datasets are increasing exponentially. Further, the conclusion that increased transcriptional noise is not a defined aspect of aging is clearly an important contribution; however, given the provocative nature of this claim, more comprehensive and systematic analyses should be performed. In particular, the robustness and appeal of scallop is still not sufficiently demonstrated and given the complexity (multiple tissues, species and diverse relative age ranges) of datasets analyzed, a more thorough comparison should be performed. I list a few thoughts below:

Initially, the authors develop Decibel, which centralizes noise quantification methods. The authors provide schematics shown in Fig 1, and compare noise estimates with aging in Fig 2 - Supplement 2. Since the authors emphasize the necessary use of scallop as a ”better” pipeline, more systematic comparisons to the other methods should be made side-by-side.

We thank the reviewer for their positive assessment of the manuscript and their suggestions. We agree that side-by-side benchmarking of Scallop with the methods implemented in Decibel, as well as a more thorough analysis on the effect of different features such as dataset size, cellular composition, etc. might have on the output of Scallop will reinforce the main points of the manuscript. To experimentally respond to these requests, we took advantage of a set of four artificial datasets previously generated by us with the R package splatter (v1.10.1; as described in Ascensión et al. [1]). In the present work, we first run a side-by-side comparison between Scallop and two distance-to-centroid (DTC) methods on the four artificial datasets with increasing degrees of transcriptional noise present in them (the novel data are included as Figure 1 – Figure supplement 1 in the revised manuscript). Then, we compared Scallop to one DTC method regarding their ability to detect noisy cells in different cell types (Figure 1 – Figure supplement 2). Finally, we implemented four simulations to test the effect of the following features on the performance of Scallop: cellular composition (Figure 1 – Figure supplement 3), dataset size (Figure 1 – Figure supplement 4), number of genes (Figure 1 – Figure supplement 5) and marker gene expression (Figure 1 – Figure supplement 6). A summary of these results follows.

Side-by-side comparison of Scallop vs DTC methods

Each of the four artificial datasets used consists of 10K cells, from 9 populations, named Group1 to Group9, with the following relative abundances: 25, 20, 15, 10, 10, 7, 5.5, 4, and 3.5%, respectively. The four datasets only differ in the de.prob parameter used in their generation. The de.prob parameter determines the probability that a gene is differentially expressed between subpopulations within the dataset. The greater the de.prob value, the more differentially expressed genes there will be between clusters, meaning that the different cell types present in the dataset will cluster in a more robust way. Decreasing the value of de.prob results in datasets with noisy cells, with populations that do not have such a strong transcriptional signature. In order to study how Scallop can capture the degree of robustness with which cells of the same cell type cluster together, we selected four de.prob values (0.05, 0.016, 0.01 and 0.005) and measured transcriptional noise using Scallop and two DTC methods, the whole transcriptome-based Euclidean distance to cell type mean and the invariant gene-based Euclidean distance to tissue mean expression. These two methods were selected because GCL does not yield a transcriptional noise measure per cell, so no comparisons can be made with respect to the amount of noisy cells the method is able to detect within a cluster. Similarly, comparing Scallop to the ERCC spike in-based method was not possible for artificial datasets. Importantly, these analyses showed that Scallop, unlike DTC methods, was able to discern between the core transcriptionally stable cells within each cell type cluster from the more noisy cells that lie in between clusters (provided in the Figure 1 - Supplement 1 of revised manuscript).

Effect of dataset features on the performance of Scallop

We simulated five artificial datasets with the same nine cell type populations but whose relative abundances were different between datasets. We used the imbalance degree (ID) to measure class imbalance in each of them and to make sure that the selected cell compositions represented a wide range of imbalance degrees (to this end, we explored ID values between 1.2 and 5.3). The ID provides a normalized summary of the extent of class imbalance in a dataset in so-called ”multiclass” settings, that is to say, where more than two classes are present. It was specifically developed to improve the commonly used imbalance ratio (IR) measurement, whose calculation only considers the abundance of the most and the least popular classes and which gives the same summary for datasets with different numbers of minority classes. The presence of multiple minority classes is not uncommon in single-cell RNAseq datasets, as tissues might contain several rare cell types. We observed that the transcriptional noise measurements provided by Scallop were very robust to changes in imbalance degree (see Figure 1 - Supplement 3), both in qualitative and in quantitative terms. For instance, Group2 and Group8 were always detected as the most stable and noisiest cell types, respectively, regardless of their relative abundance in the dataset, and their average percentage of noise had little variation between different ID values: it ranged between 0-0.14% (Group2) and 16-18% (Group8).

The effect of dataset size (number of cells) and the number of genes was evaluated by generating versions of an artificial dataset where cells/genes had been subsampled from an original artificial dataset (the one generated with de.prob=0.001). We tested datasets sized 1,000-10,000 cells and with a number of genes between 5,000 and 14,000. Dataset size had nearly no impact on the transcriptional noise measurements provided by Scallop (Figure 1 - Supplement 4 of the revised manuscript). The average percentage of transcriptional noise per cell type remained within a narrow range as we implemented a ten-fold increase in dataset size. Perhaps more strikingly, removing the expression of most genes did not substantially impact transcriptional noise measurements per cell type (Figure 1 - Supplement 5). The variation when removing half of the genes (7,000 genes) was minimal, and we did not see important changes in transcriptional noise measurements unless over 60% of the genes from the original dataset were removed. For example, Figure 1 - Supplement 5C shows that noise measurements suffer important variations when removing 8,000 and 9,000 genes (and therefore keeping 6,000 and 5,000 genes, respectively), but only some cell types (Groups 4, 7, 8 and 9) were affected by these variations.

In order to measure the effect marker gene expression has on the membership with which cells are assigned to their cell type cluster, we ran a simulation where the top 10 markers for a cell type were removed from the dataset one by one, so that the first simulation lacked the expression of the Top1 marker, the second simulation had the effect of the first 2 markers removed (Top1 and Top2), and so on. Then, we ran Scallop on each of the resulting datasets and observed a steady increase in transcriptional noise associated with that cell type. This provided evidence that the strength of cell type marker expression in a cluster is directly related to its transcriptional stability (or lack of transcriptional noise). We included the result of this experiment in the revised version of the manuscript (Figure 1 - Supplement 6).

In conclusion, by using artificially generated datasets where the ground truth (cell type labels, degree of noise, etc) was known, the newly provided systematic analyses showed that Scallop had a remarkably robust response to said changes in dataset features, further reinforcing the manuscript conclusions.

For example, scallop noise estimates (Fig 2) compared to other euclidean distance-based measures (Fig 2 supplement 2) looks fairly similar.

It is true that some datasets show similar trends regardless of the transcriptional noise quantification method. For instance, the murine brain dataset by Ximerakis et al. shows no overall change in noise between the age groups across different methods. However, we do observe important differences in other examples. This is the case of the human pancreas dataset by Enge et al. and the human skin dataset by Solé-Boldo et al., where not only the magnitude but also the directionality of the trend are different depending on the method used to measure noise. In the former, three methods (Scallop, invariant gene-based Euclidean distance to average tissue expression and GCL) show an age-related increase in noise, whereas one method (whole transcriptome-based Euclidean distance to the cell type mean) shows a decrease in noise. In the latter, two methods (Scallop and GCL) yield a decrease in noise and the two DTC methods measure a mild increase in noise. These inconsistencies can now be reconciled with our proposed explanation that said ”noise” may actually be referring to substantially different biology in the diverse experimental settings.

Are downstream observations (ex lung immune composition changes more than noise) supported from these methods as well? If so, this would strengthen the overall conclusion on noise with age, but if not, it would be relevant to understand why.

Studying changes in cell type composition in the lung and other aged tissues would be highly pertinent. Nevertheless, we have measured changes in cell type composition using only one method that is based on Generalized Linear Models, covered in the subsection Age-related cell type enrichment of the Methods. The methods that we have compared in our study (DTC methods, ERCC-based methods, GCL, etc.) were all designed to measure transcriptional noise, but not changes in cell type composition.

Whether the effects of cell type composition changes are bigger than changes in noise for the rest of the methods used to measure noise was probably not clear enough in the original manuscript. We found no evidence for an increase in noise associated with aging, regardless of the method used. Although not included in the manuscript, we did generate heatmaps similar to the one shown in Figure 3B for each of the noise quantification methods. However, as the heatmap on the right side (the one showing cell type enrichment) was identical in each figure, we considered them to be redundant and decided not to include them, since they did not provide any additional insight besides giving more examples of lack of evidence for transcriptional noise, this time at the cell type level. We consider that the lack of evidence was already well demonstrated in the previous analyses (Figure 2 and Figure 2 - Supplement 2.

Similarly, the ’validation of scallop seems mostly based on the ability to localize noisy vs stable cells in Fig 1 supplement 1 and relative robustness within dataset to input parameters (Fig 1 supplement 2). A more systematic analysis should be performed to robustly establish this method. For example, noise cell clustering comparisons across the 7 datasets used. In addition, the Levy et all 2020 implemented a pathway-based approach to validate. Specifically, surrogate genes were derived from GCL value where KEGG preservation was used as an output. Similar additional types of analyses should be performed in scallop.

We believe that this legitimate concern is now solved with the newly included data. In particular, with the systematic comparison between Scallop and DTC methods on three artificially generated datasets with different degrees of transcriptional noise provided in Figure 1 - Supplement 2. The ability of Scallop to detect cells that are particularly noisy within a cell type, or cells that lie between cell types, may represent its biggest advantage with respect to other methods. DTC methods fail to discern between stable and noisy cells within cell types. Also, in our analysis, DTC methods were unable to distinguish between cell types that have a marked transcriptional program (which systematically cluster together) and those that have a less clear transcriptomic identity (which have at least part of their cells be assigned to other cell types across bootstrap iterations). However, comparing the performance of Scallop on the same datasets showed that our method was able distinguish between the two cases.

The conclusion that immune and endothelial cell transcriptional shifts associate more with age than noise are quite compelling, but seem entirely restricted to the mouse and human lung datasets. It would be interesting to know if pan-tissues these same cell types enrich age-related effects or whether this phenomenon is localized.

We agree with the reviewer that it would be very interesting to see whether a change in cell type composition (and particularly, an increase in abundance of immune cell types) is observed in aged tissues other than the lung. Qualitative cell type composition changes in the aging lung have been described in the literature [5]. Specifically, the higher abundance of immune cell types was observed in a single-nucleus RNAseq dataset of cardiopulmonary cells in Macaca fascicularis [6]. However, we believe that trying to answer the question whether this phenomenon holds in other tissues would require a systematic analysis of several datasets for each tissue with a sufficient number of donors/individuals in each of them. This is because our approach to measure age-associated cell type enrichment using generalized linear models relies heavily on having multiple biological replicates for each age group. Unfortunately, this is not the case for most published single-cell RNAseq datasets of aging. In any case, we have toned down the last sentence in the subsection Changes in the abundance of the immune and endothelial cell repertoires characterize the human aging lung by making it more clear that our claim regarding changes in the cellular composition of aged tissues is based on lung datasets (the text in italics represents what was added in the revised version of the manuscript):

"Even though the evidence for changes in tissue composition are based on a single tissue, we hypothesize that these facts may have influenced previous analyses of transcriptional noise associated with aging."

As discussed in the original manuscript, there is evidence published by other groups pointing out to pantissue changes in cellular composition with age, which undoubtedly will influence those analyses that did not pay attention to cellular composition changes in the datasets that they compared. Cellular composition is in fact a very important aspect that has been greatly overlooked. In fact, only one [7] out of the seven articles that had measured transcriptional noise in aging (the datasets used in Figure 2) had attempted to remove its effect by subsampling cells to balance compositions between age groups prior to their noise analysis. In any case, we do not believe this is the only phenomenon underlying the purported increase in transcriptional noise associated with age. Each dataset will most probably have different issues that the authors originally misread as an increase in noise or loss of cellular identity of a particular organ or tissue. As an additional example of such phenomena, we have now included a re-analysis of the data by Enge et al. [3] on ”noisy” β-cells in the aged human pancreas (Figure 5–Figure supplement 2 of the revised manuscript). In this case, rather than observing an age-dependent pattern, the 21-year-old donor presents much lower transcriptional noise values than the rest of the donors. However, there is no significant difference between the 22-year-old donor and the rest of the donors. We conclude that the statistically significant differences between the ”young” and ”old” age categories can be attributed to the abnormal noise values obtained for the 21-year-old donor, of uncertain origin. Finding out all causes of apparent transcriptional noise in other organs and tissues would be too lengthy, and certainly out of scope for the present manuscript.

Related to these, there does not seem to be a specific rationale for why these datasets (the seven used in total or the lung for deep-dive), were selected. Clearly, many mouse and human sc-RNA-seq datasets exist with large variations in age so expanding the datasets analyzed and/or providing sufficient rationale as to why these ones are appearing for noise analyses would be helpful. For example, querying ”aging” across sc-seq datasets in Single cell portal yields 79 available datasets: https://singlecell.broadinstitute. org/single_cell?type=study&page=1&terms=aging&facets=organism_age%3A0%7C103%7Cyears.

We now realize that the reasoning behind our selection of aging datasets was not sufficiently clear in the original manuscript. We thank the reviewer for pointing out this omission. We have made a more explicit reference to Appendices 2, 3, 4 and 6 in the revised manuscript. The seven selected scRNAseq datasets are those where transcriptional noise had originally been measured by the authors, using the computational methods that we later implemented in Decibel. Our aim was to first recapitulate previous reports of transcriptional noise using our novel method (Scallop). Thus, we downloaded all publicly available scRNAseq datasets of aged tissues where transcriptional noise had explicitly been measured. Some of them had reported an increase in transcriptional noise only in some cell types (for instance, the human aged pancreas dataset by Enge et al. [3]), whereas others found an increase in most cell types [7]. Appendix 2 summarizes the main features of those seven datasets (tissue, organism and number of cells) and provides information on whether an increase in transcriptional noise was observed in the original article where they were published. Additionally, the ”scope” column indicates where that increase was found (in which cell types), and the ”Method” column briefly describes the computational method used to measure transcriptional noise in that article. Appendix 3 provides information on the final datasets that were used in our analysis (Figure 2). Not every sample from the original dataset was included, so the inclusion criteria are specified there, as well as the number of cells, individuals and age of each of the cohorts. Appendix 4 shows the abnormal count distribution of two samples that were discarded from the Kimmel lung dataset. As for the selection of lung for the deep dive, the reason was that this was the organ with most datasets available, both for mouse and human. Appendix 6 provides information on the number of cells and donors per age cohort in the human lung datasets included in this study.

We have included the following sentence in the Increased transcriptional noise is not a universal hallmark of aging subsection in the Results:

"We provide a summary of the main characteristics of each dataset, as well as the findings regarding transcriptional noise obtained in each of the original studies, whether changes in transcriptional noise were restricted to particular cell types, and the computational method used to measure noise (see Appendix 2)."

The analysis that noise is indistinguishable from cell fate shifts is compelling, but again relies on one specific example where alternative surfactant genes are used as markers. The same question arises if this observation holds up to other cell types within other organs. For example the human cell atlas contains over dozens of tissue with large variations in age (https://www.science.org/doi/10.1126/science. abl4290).

We sympathize with this comment but hope that the reviewer will agree with us that providing an additional example of different phenomena originally reported as ”transcriptional noise” (in this case in aged human pancreas; see Figure 5 – Figure supplement 2), but actually reflecting something else, may be sufficient to prevent interested readers. In our opinion, it is likely that diverse phenomena will underlie the purported increases in transcriptional noise, and a re-analysis should be made case-by-case. We can only hope that researchers in the field re-analyze the available aging datasets in this new light.

Reviewer #2 (Public Review):

In this manuscript, Ibanez-Sole et al. focus on an important open question in ageing research; ”how does transcriptional noise increase at the cellular level?”. They developed two python toolkits, one for comparison of previously described methods to measure transcriptional noise, Decibel, and another one implementing a new method of variability measure based on cluster memberships, Scallop. Using published datasets and comparing multiple methods, they suggest that increased transcriptional noise is not a fundamental property of ageing, but instead, previous reports might have been driven by age-related changes in cell type compositions.

I would like to congratulate the authors on openly providing all code and data associated with the manuscript. The authors did not restrict their paper to one dataset or one approach but instead provided a comprehensive analysis of diverse biology across murine and human tissues.

While the results support their main conclusions, the lack of robustness/sensitivity measures for the methods used makes it difficult to judge the biology.The authors use real data to compare between methods but using synthetic data with known artificial ’variability’ across cell clusters can first establish the methods, which would make the results more convincing and easier to interpret. Despite the comprehensive analysis of biological data, a detailed prior description of how the methods behave against e.g. the number of cells in each cell type cluster, the number of cell types in the dataset, and % feature expression, would make the paper more convincing. Once the details of the method is provided, the python toolkit can be widely used, not limited to the ageing research community. I am also concerned that a definition of ’transcriptional noise’ (e.g. genome-wide noise, transcriptional dysregulation in cell-type-specific genes, noise in certain pathways) and its interpretation with regard to the biology of ageing is missing. Differences in different methods could be explained by the different biology they capture. Moreover, the interpretation of a lack of different types of variability may not be the same for the biology of ageing.

Increased transcriptional noise is compatible with genomic instability, loss of proteostasis and epigenetic regulation. Showing a lack of consistent transcriptional noise can challenge the widespread assumptions about how these hallmarks affect the organism. Overall, I found the paper very interesting and central to the field of ageing biology. However, I believe it requires a more detailed description of the methods and interpretations in the context of biology and theories of ageing.

We thank the reviewer for their positive assessment of the manuscript and their suggestions. We respond to each of the specific comments below.

Major comments

1) The concept of transcriptional noise is central to the manuscript; however, what the authors consider as transcriptional noise and why is not clear. Genome-wide vs. function or cell-type specific noise could have different implications for the biology of ageing. In line with this, a discussion of the findings in the context of theories of ageing is necessary to understand its implications.

We thank the reviewer for pointing out the lack of clarity in this key point. The use of the ”transcriptional noise” term in the literature is quite heterogeneous, and we agree that the lack of a consensus definition may be confusing to the reader. For this reason, we adopted in the introduction the definition by Raser and O’Shea [8] as ”the measured level of variation in gene expression among cells supposed to be identical”, i.e. the sum of both intrinsic and extrinsic noise as previously defined by Swain and colleagues [9, 10]. In our opinion, this is generally what the literature of age-associated transcriptional noise is referring to.

With Scallop, we aimed to translate this concept to the context of single-cell RNAseq datasets, where clusters obtained using a community detection algorithm are typically annotated as distinct cell types.

Therefore, we aimed to measure transcriptional noise here defined as ”lack of membership to cell type clusters”. When running a clustering algorithm iteratively, if a cell is not unambiguously assigned to the same cluster, we consider it to be noisy. Conversely, when a cell consistently clusters with the same group of cells, we consider it to be stable. The membership score we use as a measure of stability is the frequency with which any given cell was assigned to the same cluster across all iterations.

We have included in the Results section an explicit reference to the Methods subsection that explains how Scallop works in detail, so that the readers can easily find that information:

"A detailed description of the three steps of the method (bootstrapping, cluster relabeling and computation of the membership score) is provided in the Scallop subsection in the Methods."

Additionally, we have now realized that the formula to compute the membership score might be more easily understood if we renamed the freq_score as freq_score(c), to make it clear that each cell is assigned a score. Also, we have used n and m instead of i and j in this notation, to avoid confusing the readers with the notation used in the previous section, where i and j represented the i-th and j-th bootstrap iterations. Finally, we have included a small paragraph to clarify what each component of the formula refers to. Below we show the formula and text included in the Methods section of the revised manuscript:

"Where |cn| is the number of times cell c was assigned to the n-th cluster, and Pm∈clusters |cm| is the sum of all assignments made on cell c, which is the same as the number of times cell c was clustered across bootstrap iterations."

Thus, and in order to accommodate this reviewer’s concerns, we have now included this exact definition of how we measure noise plus a statement making clear that we refer to the sum of both intrinsic and extrinsic noise aspects, with no distinction among them.

Similarly, we had discussed our findings in the framework of different theories of aging, such as their potential relationship to some of the established hallmarks of aging (genomic instability, epigenetic deregulation and loss of proteostasis), as well as with more recent theories of aging such as cell type imbalance in aged organs [11] and inter-tissue convergence [12]. However, it is now clear to us that this was not enough so we have now expanded these paragraphs to make our understanding of the work implications better understood. More specifically:

"Our results suggest that transcriptional noise is not a bona fide hallmark of aging. Instead, we posit that previous analyses of noise in aging scRNAseq datasets have been confounded by a number of factors, including both computational methods used for analysis as well as other biology-driven sources of variability."

2) While I found the suggested method, Scallop, quite exciting and valuable, I would suggest including a number of performance/robustness measures (primarily based on simulations) on how sensitive the method is to the number of cells in each cell type (cellular composition), misannotations, % feature expression (number of 0s) etc.:

We have analyzed the effect of cellular composition and the percentage of feature expression by using artificially generated datasets (see Figure 1 - Supplements 3 and 5, respectively; and section Effect of dataset features on the performance of Scallop in the response to reviewer #1). Although studying the effect of misannotations on downstream analysis is important, we believe that Scallop was already designed so that its effects could be avoided, since the membership is measured for each cluster (and not for each cell type label). That is to say, a reference clustering is obtained at the beginning of the pipeline and memberships are computed using that output as a reference, which means Scallop noise values attributed to each cell are not affected by the original labeling of the dataset.

The output of these analyses reinforced our original conclusions, and it is now included in the Results section:

"In order to characterize and validate our method for transcriptional noise quantification, we conducted three types of analyses. First, we used artificially generated datasets containing various degrees of transcriptional noise to compare the performance of Scallop and DTC methods side-by-side, regarding their ability to measure transcriptional noise and detect noisy cells within cell types. Next, we ran simulations using artificial datasets in order to study the effect of a number of dataset features on the performance of Scallop: cellular composition, dataset size, number of genes and marker expression. Finally, we graphically evaluated the output of Scallop on a dataset of human T cells, we analyzed its robustness to its input parameters, and we studied the relationship between membership and robust marker expression, using a PBMC dataset."

2.1) Most importantly, knowing that cell-type composition changes with age, it is important to know how sensitive community detection is to the number of cells in each cell type. While the average can be robust, I wonder if the size of the cell-type cluster affects membership (voting).

We have included an analysis on a set of artificial datasets with different cellular compositions to evaluate the performance of Scallop in the presence of different degrees of class imbalance (see Figure 1 - Supplement 3). We explain the output of this analysis, which reinforces the algorithm’s robustness, in the Results section:

"Next, we ran a series of simulations on artificially generated datasets to evaluate the performance of Scallop in the presence of different levels of class imbalance, dataset size, number of genes, and different degrees of expression of cell type markers. Our analysis showed that Scallop was remarkably robust to changes in cellular composition (see Figure 1 - Supplement 3). Both the average percentage of noise and the distribution remained unchanged for a wide range of class imbalance degrees. Similarly, altering the dataset size (number of cells) and the number of genes of an artificial dataset did not cause any major changes on the transcriptional noise values attributed to each cell type (see Figure 1 - Supplements 4 and 5). Additionally, we conducted an analysis where we identified the 10 most differentially expressed gene markers for a cell type and measured the transcriptional noise associated with that cell type as we removed the expression of those genes from the dataset (Figure 1 - Supplement 5). Transcriptional noise steadily increased as we removed the effect of the top marker genes that defined the cell type under study (see Figure 1 - Supplement 5B). This experiment provides further evidence on how strong marker expression is related to robust cell type identity and how the lack of it results in transcriptional noise."

3) Although the Leiden algorithm is widely used by many single-cell clustering methods, since the proposed methodology is heavily dependent on clustering, I suggest including a description of the Leiden algorithm.

We agree that understanding how community detection algorithms in general –and Leiden in particular– work is crucial to understand the core of the paper, so we have included a brief introduction to these methods in the Methods section, at the beginning of the Scallop subsection:

Leiden is a graph-based community detection algorithm that was designed to improve the popular Louvain method [13]. Graph-community detection methods take a graph representation of a dataset. In the context of single-cell RNAseq data, shared nearest neighbor (SNN) graphs are commonly used. These are graphs whose nodes represent individual cells and edges connect pairs of cells that are part of the K-nearest neighbors of each other by some distance metric. The aim of community detection algorithms like Leiden is to find groups of nodes that are densely connected between them, by optimizing modularity. For a graph with C communities, the modularity (Q) is computed by taking, for each community (group of cells), the difference between the actual number of edges in that community (ei) and the number of expected edges in that community ( K2/1/2m).

Where r is a resolution parameter (r > 0) that controls for the amount of communities: a greater resolution parameter gives more communities whereas a low resolution parameter fewer clusters. Since maximizing the modularity of a graph is an NP-hard problem, different heuristics are used, and Leiden has shown to outperform Louvain in this task both in terms of quality and speed [14]. However, users can choose to run the Louvain method instead by setting the parameter clustering="louvain" in the initialization of the Bootstrap object.

3.1) Most importantly, the authors comment that they found stronger expression of cell-type specific markers in the cells with high membership values - is it already a product of the Leiden algorithm that it weighs highly variable (thus cell-type specific) features higher - resulting in better prediction of cell-types for cells with strong cell-marker expression? It is important to make a description of transcriptional noise at this stage as it could be genome-wide or more specific to cell-type markers. Can authors provide any support that their method can capture both?

We agree with the reviewer that finding a stronger expression of cell-type markers in cells with high membership values is indeed something we expected. The graph representation of the dataset taken as input by Leiden is built after running highly variable gene detection and PCA. The neighbors of each cell are detected based on the expression of genes that are highly variable, as the reviewer pointed out, so genes that are differentially expressed between cells are more likely to contribute to the clusters found by Leiden.

Whether Scallop measures genome-wide or cell type-specific noise (or a mixture of both) is a very interesting question. Clusters in single-cell RNA sequencing datasets are often mainly driven by the presence/absence of a few cell type markers, rather than changes in expression levels of broader sets of genes. Moreover, it has been shown that single-cell RNAseq datasets generally preserve the same population structure even after data binarization [15]. This is a consequence of the sparsity of single-cell RNAseq datasets. In our case, any difference in expression between one cluster vs the rest of the cells in the dataset –be it the expression of a gene that was not detected in the rest of the cells or a higher expression of a gene whose presence is weaker in other clusters– will certainly have an impact on the output of every downstream analysis, from clustering to dimensionality reduction. The influence of the expression of cell type-specific markers on Scallop membership has been demonstrated in several analyses. First, the simulation where we measured the impact of removing the 10 most defining markers for a particular cell type on transcriptional noise measurements (included in the Figure 1 - Supplement 6 of the revised manuscript). Also, Figure 5 provides evidence that the differential expression of a handful of genes (in this case, genes coding for surfactant proteins) can have an impact on the clustering solutions obtained for a set of human alveolar macrophages, and this in turn influences the membership scores obtained with Scallop. In essence, Scallop merely provides a measure of the robustness of clustering at the single-cell level, so any type of transcriptional noise might have an impact on Scallop memberships, provided it is sufficiently strong to influence the output of the clustering algorithm used. In other words, the fact Scallop membership captures a mixture of both types of noise (genome-wide and that associated with cell type-specific markers) is a consequence of the influence both types of noise have on clustering.

4) The authors conclude that Scallop outperforms other methods through the analysis of biological data, where there is no positive and negative control. I suggest creating synthetic datasets (which could be based on real data), introducing different levels of noise artificially (considering biological constraints like max/min expression levels) and then testing the performance where the truth about each dataset is known. Otherwise, the definitions of noisy and stable cells, regardless of the method, are arbitrary.

Our initial focus was on biological datasets, were no positive and negative controls regarding transcriptional noise could be used, but we agree in the need of including an analysis using simulations on artificial datasets. We analyzed artificially generated datasets with known degrees of transcriptional noise in order to evaluate the performance of Scallop on a setting where the ground truth is known beforehand. The way we modeled transcriptional noise was by tuning the de.prob parameter, which determines the probability that a gene will be differentially expressed between clusters. The creation of these datasets is explained in detail in the Methods section of the revised manuscript, and specifically in the subsections Performance of Scallop and two DTC methods on four artificial datasets with increasing transcriptional noise. and Ability to detect noisy cells within cell types.

We have now included the following section in the Results:

"We compared the output of Scallop and two DTC methods (the whole transcriptome-based Euclidean distance to average cell type expression and the invariant gene-based Euclidean distance to average tissue expression) on four artificially generated datasets containing various levels of transcriptional noise. The analysis showed that Scallop, unlike DTC methods, was able to discern between the core transcriptionally stable cells within each cell type cluster from the more noisy cells that lie in between clusters (see Figure 1 - Supplement 1). We then compared one of the DTC methods to Scallop regarding their ability to detect noisy cells within each of the cell types, by plotting the top 10% noisiest and top 10% most stable cells and (see Figure 1 - Supplement 2A). Analyzing the distribution of noise values for each cell type separately revealed that Scallop can distinguish between clusters that mainly consist of transcriptionally stable cells from noisier clusters that do not have such a distinct transcriptional signature (Figure 1 - Supplement 2B."

Reviewer #3 (Public Review):

In this manuscript, Ibáñez-Solé et al aim to clarify the answer to a very basic and important question that has gained a lot of attention in the past ∼5 years due to fast-increasing pace of research in the aging field and development/optimization of single-cell gene expression quantification techniques: how does noise in gene expression change during the course of cellular/tissue aging? As the authors clearly describe, there have been multiple datasets available in the literature but one could not say the same for the number of available analysis pipelines, especially a pipeline that quantifies membership of single cells to their assigned cell type cluster. To address these needs, Ibáñez-Solé et al developed: 1. a toolkit (named Decibel) to implement the common methods for the quantification of age-related noise in scRNAseq data; and 2. a method (named Scallop) for obtaining membership information for single-cells regarding their assigned celltype cluster. Their analyses showed that previously-published aging datasets had large variability between tissues and datasets, and importantly the author’s results show that noise-increase in aging could not be claimed as a universal phenotype (as previously suggested by various studies).

We thank the reviewer for their positive assessment of the manuscript and their suggestions.

Comments:

1) In two relevant papers (doi.org/10.1038/s41467-017-00752-9anddoi.org/10.1016/j.isci. 2018.08.011), previous work had already shown what haploid/diploid genetic backgrounds could show in terms of intercellular/intracellular noise. Due to the direct nature of age/noise quantification in these papers, one cannot blame any computational pipeline-related issues for the ”unconventional” results. The authors should cite and sufficiently discuss the noise-related results of these papers in their Discussion section. These two papers collectively show how the specific gene, its protein half-life and ploidy can lead to similar/different noise outcomes.

We agree that we have failed to mention and sufficiently discuss the effects of measuring transcriptional noise from data generated via destructive experimentation, where no longitudinal analyses are possible. As aforementioned in the response to other reviewers, the body of literature on transcriptional noise is quite wide and based on heterogeneous assumptions. We have focused our efforts in measuring actual noise in scRNAseq aging datasets, which by definition imply sampling of different cells and thus make assumptions at the population level. We believe our results provide a different and interesting perspective into transcriptional noise and aging, but we agree with this reviewer in the need to discuss our findings in the context of other attempts to measure transcriptional noise in a more direct way. We have now included a brief discussion of the work by Sarnoski et al. and Liu et al.. This point is explained in more detail later in the letter.

2) While the authors correctly put a lot of emphasis on studying the same cell type or tissue for a faithful interpretation of noise-related results, they ignore another important factor: tracking the same cell over time instead of calculating noise from single-cell populations at supposedly-different age points. Obviously, scRNAseq cannot analyze the same cell twice, but inability to assess noise-in-aging in the same cell over time is still an important concern. Noise could/does affect the generation durations and therefore neighboring cells in the same cluster may not have experienced the same amount of mitotic aging, for example. Also, perhaps a cell has already entered senescence at early age in the same tissue. This caveat should be properly discussed.

The distinction between intrinsic and extrinsic noise and the impossibility to discern between the two in destructive experiments is a relevant point that we have now included in the Discussion (the newly added text is shown in italics):

"Transcriptional noise could be related to genomic instability [18], epigenetic deregulation [19, 20] or loss of proteostasis [21], all established hallmarks of aging. Some authors consider transcriptional noise to be a hallmark of aging in and of itself [22]. In any case, the origin of transcriptional noise is unclear, as it could arise from many different sources. Most importantly, it not possible to distinguish between intrinsic and extrinsic noise from a snapshot of cellular states, i.e., one cannot tell whether the observed differences between cells in a single-cell RNA experiment reflect time-dependent variations in gene expression or differences between cells across a population [23]. Interestingly, recent work by Liu et al. measuring intrinsic noise in S. cerevisiae showed that aging is associated with a steady decrease in noise, with a sudden increase in soon-to-die cells. Another longitudinal study found an increase extrinsic noise and a lack of change in intrinsic noise in diploid yeast [16]."

Regarding the caveat of cells of individuals in the Young groups showing signs of aging, we can only agree that this is correct: there will be cells sampled that already show signs of cellular damage in the absence of chronological aging. However this applies to every study of aging that samples cells in a destructive manner and it is generally assumed by the field that this is a discrete phenomenon that does not affect the overall results in a meaningful way.

3) Another weakness of this study is that the authors did not show the source/cause of decreasing/stable/increasing noise during aging. Understanding the source of loss of cell type identity is also important but this manuscript was about noise in aging, so it would have been nice if there could be some attempts to explain why noise is having this/that trend in differentially aged cell types in specific tissues.

The reviewer raises here a very important point that we would like to discuss in detail. The papers that we have re-analyzed generally assume that an increase in transcriptional noise and a loss in cell type identity are equivalent terms. However, as this reviewer points out, you could theoretically have cells that lose their cell type identity without a concomitant increase in transcriptional noise, for instance by a sharp decrease in a limited number of marker genes that collectively define that cell within a given cell type/cluster. Thus, transcriptional noise can certainly arise from different sources and several mechanisms have been proposed to explain its presence in the context of cellular aging. We agree with the reviewer that discussing how transcriptional noise could be related to aging is of interest to the readers. However, as pointed out in the responses to similar concerns by the other reviewers, our main finding is that we don’t detect meaningful and reliable increases in transcriptional noise associated with cell aging. Instead, what we see is a number of different technical and biological issues/phenomena that have been interpreted as transcriptional noise. We hope this reviewer will agree that the manuscript now presents a full and robust story and that finding the causes of up/down ”noise” trends in the different datasets may be more appropriately tackled by follow up studies.

4) In the discussion section, the authors say that ”Most importantly, Scallop measures transcriptional noise by membership to cell type-specific clusters which is a re-definition of the original formulation of noise by Raser and O’Shea.” It is not clear what the authors refer to by ”the original formulation of noise by Raser and O’Shea”. Intrinsic/extrinsic noise formulations?? Please be more specific.

We thank the reviewer for pointing this out, since we agree that the sentence needed to be reformulated for the sake of clarity. What we meant by the definition by Raser and O’Shea was ”the measured level of variation in gene expression among cells supposed to be identical”, which does not make any distinction between intrinsic and extrinsic noise. Since their definition is previous to the development of single-cell technologies, we meant to state our attempt to bring this classic concept to the context of single-cell RNAseq. Nowadays, cell clusters produced by a community detection algorithm are given cell type annotations depending on their expression of known cell type markers. What Scallop aims to measure is the extent of membership each individual cell has for their cluster as evidence of its transcriptional stability. In order to make this point more clear, we have now rewritten the paragraph as follows:

Most importantly, Scallop measures transcriptional noise by membership to cell type-specific clusters which is a re-definition of the original formulation of noise by Raser and O’Shea: measurable variation among cells that should share the same transcriptome. This is in stark contrast to measurements of noise including other phenomena (as demonstrated in Figure 5) by the distance-to-centroid methods prevalent in the literature.

References

[1] M. Alex Ascensión, Olga Ibáñez-Solé, Iñaki Inza, Ander Izeta, and Marcos J Araúzo-Bravo. Triku: A feature selection method based on nearest neighbors for single-cell data. GigaScience, 11, 2022. doi: 10.1093/gigascience/giac017.