Reviewer #2:

This manuscript represents a very considerable amount of work, both wet lab and analytic, constituting excellent science. This may be the best paper yet produced on Bdelloids. Despite this glowing recommendation I have some very significant concerns about certain parts, their conclusions section, and the evidence for "enhanced cellular defence mechanisms" in the abstract. Some parts are very rigorous, but others give in to excess speculation. This paper does not really need additional work, it needs some re-writing. Afterwards this important manuscript would be a welcome addition to the field, even without the supposedly unique defence mechanisms.

Substantive concerns:

1) Line 273 onwards: There is a comparison in the manuscript between Bdelloids and Monogonants. It wasn't clear to me however that these groups had been sampled sufficiently. The Monogonants are represented by 5 species (8 genomes) within a single genus in no way representing the diversity of Monogonants and the sampling of Bdelloids is also small. The authors should take a more cautious tone to any conclusions.

2) Line 276-278: The rationale for focussing on this specific group of TEs did not appear robust. The authors say "this class of TEs is thought to be least likely to undergo horizontal transfer and thus the most dependent on sex for transmission". But other groups are not evolving predominantly by horizontal transfer, transposons can change without meiotic sex and this section needs writing a little more clearly. The following lines make a case that some transposon groups increase, and some decrease in frequency. The obvious hypothesis is drift, but the writing was unclear, I always felt that some other mechanism was being proposed but never really stated clearly.

3) Lines 288-300, comparison of TE abundances across animals; this section was very poorly done. I thought the authors could delete this comparison and have a better manuscript. How were these other species chosen? Is C. elegans a good representative of the entire phylum Nematoda? Are the tardigrades representatives of their phylum? Assembly and annotation methods vary enormously across datasets so what can the authors conclude without standardising assembly and annotation for these other animal groups? The authors say "as expected, both the abundance and diversity of TEs varied widely across taxa" This was indeed expected, Figure 2b seems to show noise, and suggests to me that the inclusion of this data was not a good idea. I suggest it is removed, or a very substantive analysis and discussion of the way in which it is an accurate and representative sample of animal transposon loads is written.

4) Line 350-353: This section is weak and needs to be improved. The authors need to make it very clear that this is not a test, it is a single observation. The phrase "as predicted by theory for elements dependent on vertical transmission" seems rather unsupported. Does this relate to the argument put forward in lines 276-278? It was unconvincing at this point also. The current description that some families increase and some decrease is couched in what sounds like too meaningful sounding language, which could be improved to be more consistent with the results. Lines 353-355 here seem to make an argument that the variation of TEs in bdelloids is purely a phylogenetic effect variably present in some bdelloid lineages and related groups. If this is their view (and it seems very reasonable indeed) then the manuscript would be improved considerably if they stated it more clearly.

5) Lines 533-535 "consistent with a high fit of the data to the phylogeny under a Brownian motion model as would be expected if TE load evolves neutrally along branches of the phylogeny." I felt that this was a truly excellent result that needed to be put forward more strongly in other areas of the manuscript. In this area, and some others in this manuscript the authors have truly unique data dramatically improving our understanding of bdelloids. The manuscript would be improved if authors concentrated much less throughout on ideas this data is exceptional and different from other animals, and instead followed their own analysis that this fits with current biological thought.

6) Lines 621-632: "no significant difference between monogononts and bdelloids, or between desiccating and non-desiccating bdelloids" It is not clear to me here what statistical test is being carried out. All tests require phylogenetic control of course. I do agree that they are quite similar, perhaps this should be rewritten to reflect only that?

7) 705-706 The authors look at 3 gene families concerned with transposon control to examine copy number. In one of them they say "the RdRP domain in particular is significantly expanded". I am unclear of what test of significance was carried out and where to find this analysis. Unlike the query concerning desiccating and non-desiccating above I think this analysis is essential. The authors make a really big thing about the expansion of this gene family, including it in the abstract. If they wish to keep its prominence then they need to clearly show whether there is evidence that the size of this domain family is significantly expanded along the branch leading to bdelloids. I understand that this is illustrated in Figure 7 but this is not a test. This needs to be made much clearer in a quantitative rather than descriptive way. There is a need for broad taxonomic sampling, standardisation of assembly and annotation, and a phylogenetic design for this analysis. Else it should be removed or at the least described more conservatively.

8) Line 725: "Why do bdelloids possess such a marked expansion of gene silencing machinery?" There is no evidence presented that they do. There may be a hypothesis that they do it differently, rather than more, but that also needs testing. There is a lot of speculation in this paragraph, and I think removing this whole paragraph would improve the manuscript.

9) If there is an expansion of this family what can we then conclude? The authors say in the abstract "bdelloids share a large and unusual expansion of genes involved in RNAi-mediated TE suppression. This suggests that enhanced cellular defence mechanisms might mitigate the deleterious effects of active TEs and compensate for the consequences of long-term asexuality" yet they also review that animal groups can utilize different gene families for transposon control. Is there evidence that clade 5 nematodes with PIWI have a quantitatively different transposon defence mechanism? No, they just use a different pathway to some other groups, and the default position surely has to be the same for bdelloids, there is no evidence presented that their defence is enhanced. I would strongly recommend that the authors reduce the strength of their claims about the significance of bdelloid transposon control gene families in this manuscript.

10) I felt that the Conclusions (and Abstract) were too speculative and not fully supported by the existing data, though this can easily be addressed by a substantial re-write.

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Reply to the reviewers

Reviewer__ #1 (Evidence, reproducibility and clarity (Required)):__ Septins are highly conserved small GTPase cytoskeletal proteins that function as molecular scaffolds for dynamic cell wall and plasma membrane-remodeling, as well as diffusion barriers restricting movement of membrane and cell wall-associated molecules. Recent work has started to unravel the functional connections between the septins, cell wall integrity MAPK pathway signaling, and lipid metabolism, however most studies have focused on a small sub-set of septin monomers and/or were conducted in primarily yeast-type fungi. Here the authors show in the filamentous fungus A. nidulans that the core hexamer septins are required for proper coordination of the cell wall integrity pathway, that all septins are involved in lipid metabolism. Especially sphingolipid, but not sterols and phosphoinositides, contributes to the localization and stability of core septins at the plasma membrane. The experiments are simple and clear, therefore the conclusion is convincing. Fig.8 model, I would like to see the situation of septin mutant.

We thank the reviewer for the positive comments. In response to the request from this reviewer and a similar one from reviewer 2 for more on the effect of the loss of individual septins, we added text clarifying the roles of core hexamer, core octamer and noncore septins throughout the manuscript including in the legend to Fig 8 (li 439-444) and the discussion (li 388-402). Please see responses to reviewer 2 comments for more detail.

Reviewer #1 (Significance (Required)):

Since localization of cell wall synthesis proteins, lipid domains and septins are likely to depend on each other, sometimes difficult to evaluate the effect is direct or indirect. The comprehensive analyses like performed here are helpful to catch the overview in the field.

Reviewer__ #2 (Evidence, reproducibility and clarity (Required)):__ **Summary** The study by Mela and Momany describes the function of core septins of A. nidulans and links with the requirement of the cell wall integrity pathway and the sphingolipids which, are required for membrane and cell wall stability. The study is of interest for the fungal genetics community, and the authors have conducted a substantial amount of work in a field they have substantial experience. However, one of the main weaknesses of the manuscript is the assumption whether the CWI pathway controls de septin function of if the core septins control it.

We agree that while our data clearly indicate interactions between the septins and the CWI pathway, which component controls the other is not clear. We have modified the text to address this concern in several places as detailed in responses to the reviewer’s specific comments below.

**Major comments** In the abstract, the authors claim that double mutant analysis suggested core septins function downstream of the final kinase of the cell wall integrity pathway. However, from the experiments showed, it is difficult to be convinced about that. The authors should make efforts do make it clear in the manuscript and the discussion. For example: -Line 25-26 (abstract): "Double mutant analysis suggested core septins function downstream of the final kinase of the cell wall integrity pathway."

We agree that while the double mutant analysis shows interaction of septins with the CWI pathway, the evidence for them being downstream is not strong. We have revised the abstract as follows:

Li29-30: Double mutant analysis with Δ**mpkA suggested core septins interact with the cell wall integrity pathway.”

-Line 181-182; 219-220 (results) "Double mutant analyses suggest core septins modulate the cell wall integrity pathway downstream of the kinase cascade." This conclusion is one of the most important of the manuscript. However, this reviewer argues that it cannot be convincingly addressed if at least the phosphorylation ok the MAP kinase MpkA in the septins background is not evaluated under conditions of cell stress and sphingolipid biosynthesis inhibition. The genetic analysis alone maybe not enough to infer if septins control the CWI or the other way around. There may have compensatory effects when the CWI pathway is impaired. For example, most of the septins and mpkA double mutants seems to suppress the defect of the delta mpkA under cell wall stress. The authors should consider this idea.

Although we discuss the epistasis experiments as one possible interpretation, we agree the genetic analysis is not enough to definitively show that the septins are upstream of the CWI pathway or the other way around. The suppression of cell wall defects by deletion of septins in a mpkA null mutant background under cell wall stress suggests a bypass of the CWI pathway for remediation of the cell wall or some other alternate regulatory node. One possible interpretation of these data could be that by inactivation of normal CWI integrity function through deletion of the final kinase, in addition to deletion of septins (possibly acting as negative regulators of CWI components), there may be a parallel node by which cell wall remediation could still occur.

Wording throughout the abstract, results, and discussion has been modified accordingly.

Li 29-30: Double mutant analysis with Δ**mpkA suggested core septins interact with the cell wall integrity pathway.

Li 208-209: Double mutant analyses suggest the core septin aspB cdc3 modulates the cell wall integrity pathway in the ∆mpkA background under cell wall stress.

Li 221-225: When challenged with low concentrations of CASP and CFW, the ∆aspBcdc3**∆mpkAslt2 and ∆aspE ∆mpkA slt2 mutants were more sensitive than ∆aspBcdc3 and ∆aspE single mutants, but suppressed the colony growth defects of ∆mpkA slt2. The novel phenotype of the double mutants shows that septins are involved in cell wall integrity and raises the possibility that they act in a bypass or parallel node for remediation of cell wall defects (Fig 4).

Li 227-228: Fig 4. Double mutant analyses suggest core septins modulate the cell wall integrity pathway.

Li 464-468: Double mutant analyses between septins and CWI pathway kinases also support a role for core septins in maintaining cell wall integrity under stress (Fig 4). Suppression of cell wall defects under cell wall stress by deletion of septins in an ∆mpkA slt2 background suggests a parallel node by which septins negatively regulate cell wall integrity pathway sensors or kinases could exist.

There is no clear evidences on the manuscript that the core septins AspA, AspB, AspC, and ApsD are epithastic in A. nidulans. Therefore, the authors choice of using different Asp deletion mutants as a proxy for all the septins mutants is questionable. For example, there is no mention of why AspB was chosen for Figure 2 (chitin and β-1,3-glucan deposition), and AspA was chosen for Figure 3 (chitin synthase localization) since these experiments are correlated. The same is true for Figure S1 where AspB and AspE were used. One can wonder if some of the core septins would have a major impact in the chitin content.

We agree with the reviewer that not all four core septins are equivalent. Previously published work from our lab shows that AspACdc11, AspBCdc3, AspCCdc12, and AspDCdc10 form octamers and that AspACdc11, AspBCdc3, and AspCCdc12 form hexamers, that both of these heteropolymers co-exist, and that the noncore septin AspE is not part of either core heteropolymer, though it appears to influence them possibly through brief interactions (Lindsay et al., 2010; Hernandez-Rodriguez et al., 2012; Hernandez-Rodriguez et al., 2014). This previous work also clearly shows that strains in which the hexameric septins have been deleted (ΔaspA, ΔaspB, and ΔaspC) have very similar phenotypes while strains in which the octamer-exclusive septin has been deleted (ΔaspD) have different phenotypes.

In our attempt to simplify the current manuscript we discussed the four core septins as a group. In retrospect this caused us to miss important distinctions on the roles of hexamer vs octamer septins and we are grateful to the reviewer for pointing this out. We have modified language throughout the revised manuscript to specify whether results and interpretations apply to core hexamer septins, core octamer septins, the noncore septin, or individual septins. This more detailed analysis has given us several new ideas to test in future work.

While we cannot exclude the possibility that interesting results might be produced by analyzing null alleles of each individual septin gene for all experiments, we agree with the cross-reference by Reviewer #3 that there is a very low likelihood that we would see different results by analyzing all individual septins within each subgroup (hexamer, octamer or noncore).

To the reviewer’s questions on choice of septins for Fig 2, Fig 3, and Fig S1:

ΔaspA, ΔaspB, and ΔaspC showed similar sensitivity to cell wall-disturbing agents in the plate-based assays in Fig 1 and are all part of the core hexamer. We have modified text including the figure legends to make it clear which septins were used in the experiments and which group they belong to.

In a related comment about Figure 3, the reallocation of chitin synthases in the absence of septins is very interesting, but consider that all the core septin genes should be tested. Without a fully functioning cell wall, the formation of septa will be impaired. It makes their results less surprising.

In the case of Fig 3, we were unable to recover ChsB-GFP in the ΔaspB or ΔaspC backgrounds but were able to recover it in the ΔaspA background. We have clarified as follows:

Li184-187: To determine the localization of synthases, a chitin synthase B-GFP (chsB-GFP) strain was crossed with strains in which core hexamer septins were deleted. After repeated attempts, the only successful cross was with core hexamer deletion strain ∆aspA cdc11.

Figure 3, Panels A and B, chitin was also labeled by Calcofluor White which clearly shows that the formation of septa was not impaired even in the septin null mutant background (this is in agreement with previous work form our lab which shows that septa still forms in individual septin null mutants). The results showed that unlike WT cells, chitin synthase is not only absent in most branch tips in the septin null mutant background, but seems to be limited primarily to longer (presumably actively growing/non-aborted) branches; these findings were surprising to us, considering other major cell wall synthesis events, such as targeting of cell wall synthases to septa during septation appeared to be unimpaired (based on the presence of fully-developed, chitin-labeled septa).

The labeling of septa by calcofluor is now noted in the legend to Figure 3 as follows:

Li 201: Calcofluor White labeling shows the presence of the polymer chitin at septa, main hyphal tips, branches, and …

Why was chitin synthase B chosen to be analyzed in terms of reallocation? How many chitin synthases are in the A. nidulans genome. This rationale should be explained in the manuscript.

We have added the following:

Lines 173-182: A. nidulans contains six genes for chitin synthases: chsA, chsB, chsC, chsD, csmA, and csmB. Chitin synthase B localizes to sites of polarized growth in hyphal tips, as well as developing septa in vegetative hyphae and conidiophores, a pattern very similar to septin localization. Deletion of chitin synthase B shows severe defects in most filamentous fungi analyzed thus far, and repression of the chitin synthase b gene expression in chsA, chsC, and chsD double mutants exacerbated growth defects from a number of developmental states observed in each single mutant, suggesting it plays a major role in chitin synthesis at most growth stages (Fukuda et al., 2009). For these reasons, we chose chitin synthase B as a candidate to observe in septin mutant background for possible defects in localization.

Figure 3 and Figure 4. The authors should make efforts to quantify the phonotypes they claim. They are overall very subtle, especially for Figure 3. Also, a decrease of fluorescence is a tricky observation that should be better reported by quantification.

Line scans of aniline blue and CFW label were conducted and added as Fig S1. Quantitation was performed and added as Fig S3. See author’s response to Reviewer #3 below for details.

Again, in Figures 5, 6, and 7, it is clear that the different septins respond differently when ergosterol or sphingolipids synthesis is impaired. It also raises the question again if there are differences in the role of septin genes. Can the authors use previous information about differences in septin function to improve the model (Figure 8)

As described above, we have modified the manuscript throughout to clarify which phenotypes are seen for core hexamer, core octamer, and noncore septin deletions. As the reviewer notes, these are especially relevant for the sphingolipid-disrupting agents. Our model includes interaction of septins with sterol rich domains that contain both sphingolipids and ergosterol. Because it is not yet clear how subgroups of septins interact with each other and are organized at SRDs, we show all core septins in our model without distinguishing hexamers and octamers in the drawing, but we have now added text to clarify roles and outstanding questions.

The changes are summarized in the abstract as follows:

Li 37-40: Our data suggest that the core hexamer and octamer septins are involved in cell wall integrity signaling with the noncore septin playing a minor role; that all five septins are involved in monitoring ergosterol metabolism; that the hexamer septins are required for sphingolipid metabolism; and that septins require sphingolipids to coordinate the cell wall integrity response.

The clarifications are reflected in the Figure 8 legend (and associated sections of the discussion) as follows:

Li 436-441: As described in the text, our data suggest that all five septins are involved in cell wall and membrane integrity coordination. The core septins that participate in hexamers appear to be most important for sphingolipid metabolism while all septins appear to be involved in ergosterol metabolism and cell wall integrity. Because SRDs contain both sphingolipids and ergosterol and because it is not yet clear how subgroups of septins interact with each other at SRDs, we show all core septins in our model without distinguishing hexamers and octamers.

For the above-discussed reasons, the conclusion on lines 384-388 (discussion) is not completely supported by the experiments shown in the manuscript. The authors need to make a better structured and more straightforward story emphasizing the stronger points and reducing descriptions of more speculative points.

As discussed above, we have made changes throughout the manuscript to clarify which subgroups of septins are involved in which process and to refine our conclusions accordingly. The beginning of the discussion section has been changed as follows:

Li 384-399: Our data show that A. nidulans septins play roles in both plasma membrane and cell wall integrity and that distinct subgroups of septins carry out these roles. Previous work has shown that the five septins of A. nidulans septins form hexamers (AspACdc11, AspBCdc3, and AspCCdc12) and octamers (AspACdc11, AspBCdc3, AspCCdc12, and AspDCdc10) and that the noncore septin AspE does not appear to be a stable member of a heteropolymer (20). The current work suggests that though all septins are involved in coordinating cell wall and membrane integrity, the roles of hexamers, octamers, and the noncore septin are somewhat different. Core hexamer septins appear to be most important for sphingolipid metabolism, all five septins appear to be involved in ergosterol metabolism, and core septins are most important for cell wall integrity pathway with the noncore septin possibly playing a minor role. As summarized in Figure 8 and discussed in more detail below, our previous and current data are consistent with a model in which: (A) All five septins assemble at sites of membrane and cell wall remodeling in a sphingolipid-dependent process; (B) All five septins recruit and/or scaffold ergosterol and the core hexamer septins recruit and/or scaffold sphingolipids and associated sensors at these sites, triggering changes in lipid metabolism; and (C) The core septins recruit and/or scaffold cell wall integrity machinery to the proper locations and trigger changes in cell wall synthesis. The noncore septin might play a minor role in this process.

Minor comments Overall the figure caption could be shortened. They are too descriptive and contain details that are easily inferred for the images and from the materials and methods.

Legends to the following figures have been streamlined by removing portions that belong in the methods: Figure 2, Fig 3, and Fig 6

The authors made every effort to cove the precedent literature, but the manuscript has 115 references. The authors should evaluate if all the cited literature is extremely relevant. The manuscript would benefit for that conciseness.

Because this manuscript addresses septins, ergosterol, sphingolipids, cell wall integrity, and multiple different pathways, there is a lot of literature underlying our approaches. Our strong preference is to cite primary literature, however we can shorten our reference list by relying on reviews if requested by the journal.

Line 124, 493: Replace 10ˆ7, 10ˆ4 to 107, 104, etc

“10^7” and all other scientific notation was altered to replace carrots “^7” with superscripts “7” throughout.

The use of fludioxonil as a probe to detect cell wall impairment is perhaps out of context. This drug responds primarily to the HOG pathway and also respond to oxidative damage. So, these results could be suppressed.

Previous work by Kojima et al., 2006 showed that in addition to the HOG pathway, cell wall integrity is required for resistance to fludioxonil treatment. C. neoformans cell wall integrity mutants bck1, mkk1, and mpk1 (Aspergillus nidulans bckA, mkkA, and mpkA homologues) all exhibit hypersensitivity to fludioxonil, and this was shown to be remediated by the addition of osmotic stabilizers, suggesting cell wall impairment was involved in the growth defect produced by this treatment. Although this drug seems to act primarily through the HOG pathway, the CWI and HOG pathways have been shown to antagonize/negatively regulate one another through a parallel pathway (SVG pathway in yeast) (Lee and Elion, 1999). It has been hypothesized that internal accumulation of glycerol by constitutive activation of the HOG pathway causes decreased cell wall integrity. Due to the apparent cross-pathway control between the HOG and CWI pathways, as well as the high level of conservation of these pathway components in filamentous fungi, we thought this treatment was rightfully dual-purposed to investigate both cell wall impairment in the septin mutants and any possible involvement of the HOG pathway. This seems to be would a reasonable drug treatment to look at cell wall impairment that is not likely to be redundant with the modes of action observed in the other Figure 1 treatments (e.g. CFW, Congo Red, and Caspofungin).

The text clarifies this point as follows: li 110-112: Fludioxonil (FLU), a phenylpyrrol fungicide that antagonizes the group III histidine kinase in the osmosensing pathway and consequently affects cell wall integrity pathway signaling (Fig 1)(58-67).

Line 140: "exposure" would be more appropriate than architecture. Please also consider that the difference in the cell wall reported in Figure S1 are very subtle. Are they relevant?

The differences in the cell wall content reported in Figure S1 (Figure S2 in the revised manuscript) showed that the peak for 4-Glc was almost identical in WT and aspB null mutant, however the overall ratio of peaks switched, where 4-GlcNac content exceeded the 4-Glc content in the mutant compared to WT. By comparison, this was not the case with the septin aspE null mutant. Although this could be considered a ‘subtle’ change in chitin content, we believe this was an important unbiased analysis of the cell wall polysaccharide content and addressed some of the cell wall sensitivity phenotypes we observed, not only between WT and the septin mutants, but also between the septin null mutants which showed sensitivity to cell wall disturbing agents (i.e. aspA, aspB, and aspC) vs. those that did not show significant sensitivity (e.g. aspE). For these reasons we believe this warranted at the very least a supplemental figure for these data.

Though our idea of cell wall architecture includes changes in polymer exposure, as pointed out by the reviewer, others might use the phrase to mean only content changes. To avoid this misunderstanding, we have replaced the word “architecture” with “organization” in Li 147-148: These data show that cell wall organization is altered in ∆aspB cdc3 and raise the possibility that it might be altered in other core hexamer septin null mutants as well.

Line 144: explain briefly what it is about and why it was chosen instead of the total detection of chitin sugar monomers. Line 538: Cell wall extraction section. Is this a new method? There is no supporting literature.

We chose this method because it provides an analysis of all cell wall polysaccharide components and associated linkages. Detection of chitin sugar monomers would have also been a reasonable analysis if this were the only component of the cell wall we were investigating initially. The results showed differences in cell wall chitin content, so these were the data we presented.

This was addressed on lines 574-576: “Cell walls were isolated from a protocol based on (Bull, 1970); cell wall extraction and lyophilization were conducted as previously described in (Guest and Momany, 2000) with slight modifications listed in full procedure below.”

The results described on lines 232-257 are marginal to the study and are not exploited by the authors to address the central question of the manuscript, which is the role of the CWI pathway, septins, and sphingolipids. This section could be suppressed or very briefly mentioned in the preceding section.

We agree that these data did not show any additional involvement of septins in the Calcineurin and cAMP-PKA pathways, and the relevance of the TOR signaling pathway connection is still quite unclear. For this reason, these data were added as a supplemental figure. On the other hand, there are a number of important signaling pathways which have been shown to affect the Cell Wall Integrity pathway directly and indirectly (these three pathways in particular), which is part of the central question of the manuscript. Considering such extensive ‘cross-talk’ between pathways (references produced on Line 65) in filamentous fungi, we felt it necessary to inspect possible involvement of these pathways in septin function via plate-based assays and feel that this s most clearly communicated as its own brief section in the text.

Reviewer #2 (Significance (Required)): The topic of the manuscript is highly relevant to the fungal biology field and employs a very important genetic model. The cooperation of signaling pathways in mains aspects of fungal physiology is the main significant contribution of this manuscript. Reviewer__ #3 (Evidence, reproducibility and clarity (Required)):__ **Summary:** In this work the authors use genetic analysis in Aspergillus nidulans to identify phenotypes of septin mutants that point to roles for septins in coordinating the cell wall integrity pathway with lipid metabolism in a manner involving sphingolipids. Most of the major conclusions derive from monitoring the effects of combined genetic or chemical manipulations that target specific components of the pathways of interest. Additionally, the authors monitor the subcellular localization of septins, cell-wall modifying enzymes, and components of the cell wall itself. **Major comments:** The key conclusions are convincing, with the unavoidable caveat that null mutations of this sort and chemical inhibitors of these kinds could have unanticipated effects, such as upregulation of unexpected pathways or other compensatory alterations. The authors qualify their conclusions appropriately in this regard. The methods are explained very clearly and the data are presented appropriately. In some cases results are shown as representative images illustrating altered localization of a protein or a cell wall component. The changes observed in the experimental conditions are fairly obvious, but some quantification would not be difficult and would likely make the results even more obvious. For example, the Calcofluor White staining patterns might be nicely quantified by linescans along the hyphal length, and the same is true for AspB-GFP localization upon addition of drugs.

We thank the reviewer for the positive comments and have made the suggested changes as follows:

Line scans of aniline blue and CFW label were conducted and added as Fig S1. Text has been modified accordingly (Li 140-147).

Quantification of Chitin synthase-GFP localization and CFW staining and statistical analysis have now been added as Figure S3 and main text (Li 187-191) has been modified accordingly.

I could imagine one simple experiment that might generate interesting and relevant results, but by no means would this be a critical experiment for this study. In yeast, exposure to Calcofluor triggers increased chitin deposition in the wall. It would be interesting to know how Calcofluor staining looks in WT or septin-mutant cells that have been growing the presence of Calcofluor for some time, particularly with regard to the localization of chitin deposition in these cells. Such experiments could help connect the idea of septins as sensors of membrane lipid status and also effectors of CWI signaling.

This is a cool idea that we will pursue in future work. Thanks!

**Minor comments:** • Body text refers to Figure 1A and 1B but the figure itself does not have panels labeled A or B.

Figure 1 was revised to show panels A and B labeled clearly.

• Line 885: "S3" is missing from the beginning of the title of the figure.

“S” was added to the figure title.

Reviewer Identity: This is Michael McMurray, PhD, Associate Professor of Cell and Developmental Biology, University of Colorado Anschutz Medical Campus

Reviewer #3 (Significance (Required)): This is an important conceptual advance in our understanding of septin function because previous work in fungal septins mostly points toward them being important in directing or restricting the localization of other proteins that modify the cell wall or plasma membrane. This new work suggests that septins can play a sensing role, as well. As a fungal (budding yeast) septin researcher myself, I think that other fungal septin researchers would be very interested in these results, and I also think the broader septin community would appreciate it. Additionally, those studying fungal cell wall and plasma membrane biogenesis and coordination, including the Cell Wall Integrity Pathway, will be interested. REFEREES CROSS COMMENTING After reading Reviewer #1's comments, I agree that it would be appropriate to modify the wording of the authors' conclusions about where the septins lie in the CWI pathway (upstream or downstream). While they do mention that there may be other ways to interpret their results, a reader would have to search for the mention of these caveats and if the reader did not, then the strong conclusion statements might be taken as fact.

The abstract, main text, and discussion have been modified to show that while there is evidence that the septins interact with the CWI pathway, it is not clear which component is upstream vs downstream. See response to reviewer 2 above for details.

On the other hand, I don't think additional experiments looking at deletions of the other core septins will be worthwhile. I think that there is sufficient evidence to suspect that any single core septin deletion mutant will behave similar to another, and therefore that any one can be taken as representative. While it's possible that the authors might find something informative by looking at other mutants, I personally find the likelihood too low to justify additional experimentation along those lines.

Based on results from previous work from our lab, there are two subgroups of core septins in A. nidulans (hexamer and octamer) and septins within subgroups appear to behave similarly. The results from the current work support this idea with the same groups of mutants behaving in very similar ways. So, the core hexamer septins, AspACdc11, AspBCdc3, and AspCCdc12 can be used to make predictions about each other, but not about the octamer-exclusive septin AspDCdc10 or the noncore septin AspE. We agree with reviewer 3 that repeating analysis on multiple septins within a subgroup is not likely to give new insight. However, we were not careful in the original version of the manuscript to distinguish between core hexamer and octamer septins. As detailed in the response to reviewer 2 above, we have modified the manuscript throughout to make clear which subgroup of septins were being examined and to put conclusions into this context.

Think of the business model as a pure holdings company with many different businesses under it's portfolio.

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Reviewer #1 (Evidence, reproducibility and clarity (Required)):

In this study, the authors use focused-ion beam (FIB) milling coupled with cryo-electron tomography and subtomogram averaging to uncover the structure of the elusive proximal and distal centrioles, as well as different regions of the axoneme in the sperm of 3 mammalian species: pig, horse, and mouse. The in-situ tomograms of the sperm neck region beautifully illustrate the morphology of both the proximal centriole, confirming the partial degeneration of mouse sperm, and intriguingly, asymmetry in the microtubule wall of pig sperm. In distal centrioles, the authors show that in all mammalian species, microtubule doublets of the centriole wall are organized around a pair of singlet microtubules. The presented segmentation of the connecting piece is beautiful and nicely shows the connecting piece forming a nine-fold, asymmetric, chamber the centrioles. The authors further use subtomogram averaging to provide the first maps of the mammalian central pair and identify sperm-specific radial spoke-bridging barrel structures. Lastly, the authors perform further subtomogram averaging to show to the connecting site of the outer dense fibers to the microtubule doublet of the proximal principal piece and confirm the presence of the TAILS microtubule inner protein complex (Zabeo et al, 2018) in the singlet microtubules occupying the tip of sperm tails.

The manuscript provides the clearest insight into flagellar base morphology to date, giving insight into the morphological difference between different mammalian cilia and centriole types. The manuscript is suitable for publication, once the following questions are addressed.

We are ecstatic that the reviewer shares our enthusiasm for this work. We are particularly grateful that the reviewer appreciates the significance of the unique, and hitherto under-explored biology of the sperm centrioles and the flagellar base.

**Major Points:**

How many centrioles and axonemes were used in generating the averages presented in the paper? If too few samples were used, especially in centrioles undergoing dramatic remodeling or degeneration, the reality of MIPs and MAPs being present might be completely affected. For instance, In figure 1d, the authors present a cryoET map of the centriole microtubule triplet. However, centrioles are divided into several regions with different accessory elements. Here, the authors could show the presence of only part of the A-C linker. The A-C linker covers only 40% of the centriole, so does it mean that this centriole is made only of the accessories that characterize the proximal side of the centriole? In the same line, what were the boundaries governing subtomogram extraction? For example, in the distal centriole, were microtubules extracted from just before the start of the transition zone, to the end of the microtubule vaulting, more pronounced at the end of the proximal region? There are known heterogeneities in centriole, as well as flagella, ultrastructure along the proximal distal axis. If no pre-classification was performed for subtomogram longitudinal position along with the centriole and axoneme, structural features may be averaged out, and or present and not reflecting their real longitudinal localization. The classification should be applied here if it was not the case.

These are all valid points. Because there is no easy way to target the PC/DC when cryo-FIB milling, and because there is only one of each structure in every cell, the chances of catching them in ~150-nm-thin lamellae are slim (not to mention the number of things that can and do go wrong when doing cryo-ET on lamellae). As such, the averages of the PC were generated from 3 tomograms (3 cells) and those of the DC from 2 tomograms (2 cells). We do have more tomograms with the PC/DC, but these were used for segmentation/visual inspection since we only used the best tomograms for averaging. These numbers are not entirely atypical for cryo-FIB datasets; the only other in situ centriole structures are from 5-6 centrioles (from Chlamydomonas, from Le Guennec et al 2020 doi: 10.1126/sciadv.aaz4137 and Klena et al 2020 doi: 10.15252/embj.2020106246).

To allow readers to adjust their interpretations according to the small number of cells analysed, we explicitly stated the number of animals/cells/tomograms used to generate averages in Table S1. Furthermore, we amended the text to clarify which regions of the centrioles our averages represent. These changes are detailed below:

(1) proximal centriole

The lamellae used for averaging PC triplets caught mostly the proximal end of the centriole, and essentially all of the particles come from the most proximal ~ 400 nm. In a sense, this was a form of pre-classification. We now state explicitly that our structure represents only the proximal region and that proximal/distal differences may be identified in the future (see section on distal centriole below). Despite the limited particle number, we are confident in the presence of the MIPs as these are also visible in the raw data (the striations in Fig. 1a, now Fig. 1d, for instance). Page 7, Line 165 was edited accordingly as well as the legend to Fig. 1.

(2) distal centriole

The subtomograms used for the DC average were extracted from the region of the distal centriole closest to the base of the axoneme (i.e; the region marked “distal centriole” in Fig. 2h-i). Because the DC doublet average in Fig. 2j was generated from very few particles, we tried to be very conservative when interpreting it. Page 9, Line 216 was edited accordingly likewise the legend to Fig. 2.

(3) axoneme

We did attempt to average the axoneme from different regions of flagella (midpiece, proximal principal piece, distal principal piece). This is shown in Fig. 6d-l. The major difference we found was at the doublet-ODF connection. We did not find any striking differences in MIP densities, or in radial spoke densities along the proximodistal axis. As such, the averages in Fig. 5 are from the entire principal piece (but not the midpiece), which we state in the figure legend.

Because mammalian sperm flagella are very long, it is possible that we missed more subtle differences. We now state this in the Discussion (page 20, line 491):

**Minor Points:**

• In line 3, motile cilia are not only used to swim, they can move liquid or mucus for instance.

Done. Page 3, line 64

• In line 175, the authors stated " a prominent MIP associated with protofilament A9, was also reported in centrioles isolated from CHO cells (Greenan et al. 2018) and in basal bodies from bovine respiratory epithelia (Greenan et al 2020). Actually, this MIP has been seen in many other centrioles from other species, such as Trichonympha (https://doi.org/10.1016/j.cub.2013.06.061 ), Chlamydomonas, and Paramecium ( DOI: 10.1126/sciadv.aaz4137 ). Citing these studies will reinforce the evolutionary conservation of this MIP and therefore its potential crucial role in the A microtubule.

We thank the reviewer for pointing out these very important papers, we added them to the manuscript (page 7, lines 175-176).

• In Line178, the authors stated: "Protofilaments A9 and A10 are proposed to be the location of the seam (Ichikawa et 2017)". High-resolution cryoEM maps confirmed it: https://doi.org/10.1016/j.cell.2019.09.030 . This publication should be cited. Moreover, authors should also refer to this paper when discussing MIPs in the microtubule doublet.

Done (page 7, lines 178-179 and page 13, line 329).

We also now cite Ma et al (along with Ichikawa et al 2019 doi: 10.1073/pnas.1911119116 and Khalifa et al 2020 doi: 10.7554/eLife.52760) in the Discussion when alluding to high-resolution structures as a possible means of identifying MIPs (page 19, lines 479).

• In Line 187-189 the authors stated, "We resolved density of the A-C linker (gold) which is associated with protofilaments C9 and C10." The A-C linker interconnects the triplets of the proximal centriole (Guichard et. al. 2013, Li et. al. 2019, Klena et. al. 2020) with distinct regions binding the C-tubule, as shown by the authors in gold, as well as an A-link, making contact with the A-tubule through various protofilaments in a species-specific manner, but always on protofilament A9. The authors may have identified the A-link, labeled in green, on the outside of protofilament A8/A9 in Figure 1d.

We thank the reviewer for pointing this out. The position of the olive green density associated with A8/A9 is indeed consistent with the A-link, and this is also now illustrated more clearly in the new version of Fig. 1e (now Fig. 1h, see below). We accordingly edited page 8, lines 187-188.

• In figure 1e, the authors provide a 9-fold representation of the centriole based on their map. How relevant is this model ? the distance between triplet is inconsistent here, which has not been observed before. Do they use true 3D coordinates to generate this model? The A-C linker, which is only partially reconstructed, does not contact the A microtubule. Is it really the case? did the authors see that the A-link density of the A-C linker has disappeared? If these points are not clearly specified, this representation might be misleading.

In order to avoid misleading readers, we replaced this panel with a model generated directly by plotting back the averages into their original positions and orientations in the tomogram (new Fig. 1h). This model now shows that the olive green density on A8/A9 is in the right position to form part of the A-C linker (as Reviewer 1 correctly pointed out in their previous point). We have amended the figure legend accordingly. We also described how the plotback was generated in the Materials and Methods section (page 26, line 648).

As the reviewer points out, the distance between triplets does indeed seem inconsistent in the plotback. This is an interesting observation, but we feel it is a bit too preliminary to discuss in detail here. This can be explored in a follow-up study more focused on sperm centriole geometry.

• The nomenclature regarding MIPs is sometimes confusing in this manuscript. For example, in lines 228-229 "We then determined the structure of DC doublets, revealing the presence of MIPs distinct from those in the PC." Does this include the gold and turquoise labeled structures in Figure 2j? These densities appear to correspond to the inner scaffold stem in the gold density presented in Figure 2j, and armA, presented in the turquoise density (Li et. al. 2011, Le Guennec et. al. 2020). The presence of this Stem here is important as it correlates with the presence of the molecular player making the inner scaffold (POC5, POC1B, CENTRIN): https://doi.org/10.1038/s41467-018-04678-8

While we were initially very conservative with interpreting the DC doublet average (as stated above it comes from very few particles), we agree with the reviewer’s assessment that the gold and turquoise densities in Fig. 2j are consistent with the Stem and armA respectively of the inner scaffold. Because the inner scaffold contributes to centriole rigidity, it will be interesting to determine if and how it changes during remodelling of the atypical DC in mammalian sperm. Intriguingly, at least some inner scaffold components (including POC5, POC1B) reorganise into two rods in the mammalian sperm DC (Fishman et al 2018 doi: 10.1038/s41467-018-04678-8). We expanded the section on the DC average (page 9, lines 218-220):

• The connecting piece is composed of column vaults emanating from the striated columns is compelling and beautiful segmentation data. However, it is important to note how many pig sperm proximal centrioles had immediate-short triplet side contact with the Y-shaped segmented column 9, as well as in how many mouse centrioles have the two electron-dense structures flanking the striated columns.

Done. Material and Methods Page 25, lines 615-619.

The resolution of the mammalian central pair is an important development brought by this work. The structural similarity between the central pair of pig and horse is convincing. However, with only 281 subtomograms being averaged for the murine central pair, corresponding to an estimated resolution of 49Å, the absence of the helical MIP of C1 with 8 nm periodicity suggests that there is simply not enough signal to capture it in the average. The same could be said for the smaller MIP displayed in Figure 4 c, panel ii. This point should be clearly stated.

We agree with the reviewer that the quality of the mouse CPA structure is not on par with the pig and horse CPA structures. We now explicitly state this caveat in the text (pages 11, lines 276-277):

Another piece of compelling data presented in this study is the attachment of the outer dense fibers to the axoneme of the midpiece and proximal and distal principal pieces. From the classification data presented along the flagellar length, it is clear that the only ODF contact made with the axoneme is at the proximal principle plate. However, this is far from obvious in the native top view images presented. Is it possible to include a zoomed inset of the connection between the A-tubule and ODF connection?

We are very happy that the reviewer finds this data exciting. As Fig. 6 is quite cluttered as is, we instead tried to better annotate the cross-section views of the axoneme by tracing one doublet-ODF pair in each image (or only a doublet in the case of the distal principal piece). This shows that there is a gap between the doublet and the ODF in the midpiece, and that there is no such gap in the principal piece. We also hope that annotating one doublet-ODF pair helps the reader see that the same pattern holds true for the other doublets/ODFs. The legend to Fig. 6 was changed accordingly.

Reviewer #1 (Significance (Required)):

This work is of good quality and provides crucial information on the structure of centriole and axoneme in 3 different species. This work complements well the previous works.

The audience for this type of study is large as it is of interest to researchers working on centrioles, cilium, and sperm cell architecture.

We are pleased the reviewer appreciate the quality of our work and see the interest for broad audience.

My expertise is cryo-tomography and centriole biology

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

In this study, Leung et al. used state-of-the-art EM imaging techniques, including FIB cryo-milling, Volta Phase plate, cryo-electron tomography and subtomogram averaging, to study the structure of sperm flagella from three mammalian species, pig, horse and mouse. First, they described two unique centrioles in the sperm, the PC and the DC. They found the PCs are composed of a mixture of triplet and doublet MTs. In contrast, the DCs are composed mainly of doublet and singlet MTs. By using subtomogram averaging, they identified a number of accessory proteins, including many MIPs bound to the MT wall. Many are unique to the mammalian sperm. They further described the connecting piece region of the sperm enclosing the centrioles and found an asymmetric arrangement. Furthermore, the authors presented the structure of sperm axonemes from all three species. These include the DMT and the CPA. Finally, they described the tail region of the sperm and described how the DMTs transitioned to the singlet MTs.

This is a beautiful piece of work! It is by far the most comprehensive structural study of mammalian sperm cells. These findings will serve as a valuable resource for structure and function analysis of the mammalian flagella in the future. Now the stage is set for identifying the molecular nature of the structures and densities described in this study.

We thank the reviewer for their positive evaluation! We are very happy that they share our excitement for the work, and that they also see it as “setting the stage” for future studies at the molecular level.

The manuscript is clearly written. The data analysis is thorough. The conclusions are solid and not overstated. I don't have any major issues for its publication. A number of minor suggestions are listed below. Most are related to the figures and figure legends.

Figure 1d, the figure legend should mention this is the subtomogram average of PC triplet MTs from pig sperm, though this is mentioned in the text. Also, for convenience, the color codes for the MIPs should be mentioned in the figure legend.

Done.

Figure 2J, similarly, the figure legend should mention this is the subtomogram average of DC doublets. It also needs a description of the color codes of the identified MIPs. For the DMT, please indicate the A- and B-tubule, which are colored in light or dark blue.

Done, except we would prefer not to enumerate the MIPs as we did not name them nor discuss them extensively in the main text as we do not want to over-interpret the MIPs at this point as the average is from relatively small number of particles. However, we did specify that the gold and turquoise densities on the luminal surface are consistent with the inner scaffold. The figure legend was edited accordingly.

Line 228, "We then determined the structure of DC doublet by subtomogram averaging"

Done.

For both Fig 2 and Fig 3. the DC doublets are colored in dark and light blue, please specify which is the A- or B-tubule in the figure legends.

Done.

Line 273, need space between "goldenrod"

We would prefer to keep “goldenrod” spelled as is since this is how the color is referred to in Chimera and ChimeraX.

Figure 4. need to expand the figure legend. Panels I, ii, iii, iv, are cut-through view of the lumen of CPA microtubules C1 and C2.

Done.

Line 338, Interestingly, the RS1 barrel is radially distributed asymmetrically around the axoneme

Done.

Figure 5, need color codes for the arrowheads (light pink, pink, magenta) in panels i~n,

Done.

Figure 7, (a-c) please use arrowheads to indicate the location of caps in the singlet MT.

Done.

Reviewer #2 (Significance (Required)):

This is a beautiful and significant work - by far the most comprehensive analysis of mammalian sperm structure

We are thrilled the reviewer appreciate the novelty of our work.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

This is a very interesting study that explores the structural diversity of mammalian sperm flagella, in pig, mouse and horse, at high resolution using cryo-FIB milling and cryo-tomography. The study provides the first in situ cryo-EM structure of a mammalian centriole and describes a number of microtubule associated structures, such as MIPs and plugs at the plus-end of microtubules, that were not been reported so far. Additionally, the authors identify several asymmetries in the overall structure of the flagellum in the three species, which have implications for the understanding of the flagellar beat and waveform geometry in sperm, which are discussed by the authors. Although this study does not provide mechanistic novel information on the function of the described structures, it will undoubtedly serve as a reference for future theoretical and empirical work on the role of these structures in shaping the flagellar beat.

With the exception of a couple of "eclectic word choices" in the Introduction (see detailed feedback in Minor Comments), the manuscript is also well written. Image acquisition and analysis are sound.

We thank the reviewer for positively evaluating our work. We are glad that they feel our study will “serve as a reference” to inform future studies.

However, I have some suggestions that should help the authors to strengthen their claims and present their results. The study is in principle suitable to be published, after the following points will be addressed:

**Major comments:**

• A major concern is that it is not clear how many animals, sperms and lamellae the authors used to acquire the data presented in the manuscript. This information needs to be provided, because it not uncommon to encounter aberrant flagella, even in a wildtype animal. The authors should state how many animals, and how many flagella per each animal were analyzed, in order to allow the reader to have an opinion on the reliability of their observations.

• The figures are esthetically pleasing; however, the figures legends should be carefully revised to include necessary information about color codes, image annotations.

We thank the reviewer for raising these points. We completely agree that the numbers of animals and cells are important pieces of information. As such, we now explicitly state the number of animals/cells/tomograms used for each average in Table S1. For more qualitative observations (such as the relationship between the asymmetry of the pig sperm PC and the Y-shaped segmented columns), we now state in the number of cells and animals in which we see each feature (see detailed response to Reviewer 1).

**Minor comments:**

• Line 26. I do not think that the word "menagerie" is properly used in this context.

• Line 29. The same is true for the word "Bewildering" in this sentence.

We apologise for our somewhat eclectic word choice. We see the reviewer’s point that unconventional word choice may distract readers, so we replaced these two words with ‘diverse’ and ‘an extensive’, respectively.

• Line 286 "Our structures of the CPA are the first from any mammalian system, and our structures of the doublets are the first from any mammalian sperm, thus filling crucial gaps in the gallery of axoneme structures." Sentences like this one would fit much better in the Conclusions or at least in the Discussion.

We thank the reviewer for this suggestion, but we would prefer to keep this sentence where it is, if possible. We think it is useful to tell the audience upfront why these structures are significant, especially since readers who aren’t deep in the field may be bogged down by all the details.

• Line 377 "Large B-tubule MIPs have so far only been seen in human respiratory cilia (Fig. 5j) and in Trypanosoma (the ponticulus, Fig. 5n), but the morphometry of these MIPs differs from the helical MIPs in mammalian sperm." Please insert the citations for the studies about respiratory cilia and Trypanosoma flagella.

Done.

• In Figure 1. What do the stars shown in panel a and a' indicate?

We indeed failed to specify what the asterisks/stars indicate. They are meant to emphasise that the electron-dense material in the lumen of the PC is continuous with the CP. We have now specified this in the text (page 10, lines 245).

Given the complexity of the structures that compose the flagellar system of sperms, it would be helpful to add an illustration of the sperm with careful annotation of the centriole structures and the various segments of the flagellum.

This is an excellent suggestion. To help orient readers, we added three panels to Fig. 1 (Fig. 1a-c) showing low-magnification images of whole sperm cells. We annotated different parts of the flagellum (neck, midpiece, principal piece, endpiece) so that readers can refer back to these panels in case they want to know which part of the cell the averages are from.

• Figure 2. Explanation of the used color codes is missing. Additionally, the authors should include an explanation for the black and white arrows and for the 2 insets in i.

Done. For the color code, please see response to Reviewer 2. For the black and white arrows, we edited the figure legend.

• In "(j) In situ structure of the pig sperm DC with the tubulin backbone in grey and microtubule inner protein densities colored individually" ...it should be written "...sperm DC microtubule doublet..."

Done.

• In this figure, but also in every other figure that shows centriole, axoneme, or even microtubule averages it is important to indicate the microtubule polarity. Please add the symbol + and - to indicate microtubule polarity in the figures.

Done. In order to avoid overcrowding, we only labelled the pig structures as the horse and the mouse structures are always shown in the same orientations as the pig.

• Figure 3. Additional to the images in a,b, and c, the original tomographic slices (without segmentation) should be shown here, to allow the reader to visualize the structure.

We now include three additional supplementary movies slicing through the respective tomograms.

• Figure 7. Scale bars are missing in d-f.

Done.

• Scale bars are missing in most Supplementary figures.

Done.

• Table S1. The Information about horse and mouse centriole data is missing.

The reviewer is correct, but this information is missing because we did not average from the horse and the mouse. For the mouse, the triplets were in various stages of degeneration, resulting in heterogeneity that precluded us from averaging. For the horse, we simply did not catch enough centrioles to generate a meaningful structure.

Reviewer #3 (Significance (Required)):

This study provides several novel structural insights in to the sperm flagellum structure that have implications for the understanding of the flagellar beat and waveform geometry in sperm. Although this study does not provide mechanistic novel information on the function of the described structures, it will undoubtedly serve as a reference for future theoretical and empirical work on the role of these structures in shaping the flagellar beat.

Great to see the reviewer appreciate the novelty of our work.

Author Response

1) Please comment on why many of the June samples failed to provide sufficient sequence information, especially since not all of them had low yields (supp table 2 and supp figure 5).

An extended paragraph about experimental intricacies of our study has been added to the Discussion. It has also been also slightly restructured to give a better and wider overview of how future freshwater monitoring studies using nanopore sequencing can be improved (page 18, lines 343-359).

We wish to highlight that all three MinION sequencing runs here analysed feature substantially higher data throughput than that of any other recent environmental 16S rRNA sequencing study with nanopore technology, as recently reviewed by Latorre-Pérez et al. (Biology Methods and Protocols 2020, doi:10.1093/biomethods/bpaa016). One of this work's sequencing runs has resulted in lower read numbers for water samples collected in June 2018 (~0.7 Million), in comparison to the ones collected in April and August 2018 (~2.1 and ~5.5 Million, respectively). While log-scale variabilities between MinION flow cell throughput have been widely reported for both 16S and shotgun metagenomics approaches (e.g. see Latorre-Pérez et al.), the count of barcode-specific 16S reads is nevertheless expected to be correlated with the barcode-specific amount of input DNA within a given sequencing run. As displayed in Supplementary Figure 7b, we see a positive, possibly logarithmic trend between the DNA concentration after 16S rDNA amplification and number of reads obtained. With few exceptions (April-6, April-9.1 and Apri-9.2), we find that sample pooling with original 16S rDNA concentrations of ≳4 ng/µl also results in the surpassing of the here-set (conservative) minimum read threshold of 37,000 for further analyses. Conversely, all June samples that failed to reach 37,000 reads did not pass the input concentration of 4 ng/µl, despite our attempt to balance their quantity during multiplexing.

We reason that such skews in the final barcode-specific read distribution would mainly arise from small concentration measurement errors, which undergo subsequent amplification during the upscaling with comparably large sample volume pipetting. While this can be compensated for by high overall flow cell throughput (e.g. see August-2, August-9.1, August-9.2), we think that future studies with much higher barcode numbers can circumvent this challenge by leveraging an exciting software solution: real-time selective sequencing via “Read Until”, as developed by Loose et al. (Nature Methods 2016, doi:10.1038/nmeth.3930). In the envisaged framework, incoming 16S read signals would be in situ screened for the sample-barcode which in our workflow is PCR-added to both the 5' and 3' end of each amplicon. Overrepresented barcodes would then be counterbalanced by targeted voltage inversion and pore "rejection" of such reads, until an even balance is reached. Lately, such methods have been computationally optimised, both through the usage of GPUs (Payne et al., bioRxiv 2020, https://doi.org/10.1101/2020.02.03.926956) and raw electrical signals (Kovaka et al., bioRxiv 2020, https://doi.org/10.1101/2020.02.03.931923).

2) It would be helpful if the authors could mention the amount (or proportion) of their sequenced 16S amplicons that provided species-level identification, since this is one of the advantages of nanopore sequencing.

We wish to emphasize that we intentionally refrained from reporting the proportion of 16S rRNA reads that could be classified at species level, since we are wary of any automated species level assignments even if the full-length 16S rRNA gene is being sequenced. While we list the reasons for this below, we appreciate the interest in the theoretical proportion of reads at species level assignment. We therefore re-analyzed our dataset, and now also provide the ratio of reads that could be classified at species level using Minimap2 (pages 16-17, lines 308-314).

To this end, we classified reads at species level if the species entry of the respective SILVA v.132 taxonomic ID was either not empty, or neither uncultured bacterium nor metagenome. Therefore, many unspecified classifications such as uncultured species of some bacterial genus are counted as species-level classifications, rendering our approach lenient towards a higher ratio of species level classifications. Still, the species level classification ratios remain low, on average at 16.2 % across all included river samples (genus-level: 65.6 %, family level: 76.6 %). The mock community, on the other hand, had a much higher species classification rate (>80 % in all three replicates), which is expected for a well-defined, well-referenced and divergent composition of only eight bacterial taxa, and thus re-validates our overall classification workflow.

On a theoretical level, we mainly refrain from automated across-the-board species level assignments because: (1) many species might differ by very few nucleotide differences within the 16S amplicon; distinguishing these from nanopore sequencing errors (here ~8 %) remains challenging (2) reference databases are incomplete and biased with respect to species level resolution, especially regarding certain environmental contexts; it is likely that species assignments would be guided by references available from more thoroughly studied niches than freshwater

Other recent studies have also shown that across-the-board species-level classification is not yet feasible with 16S nanopore sequencing, for example in comparison with Illumina data (Acharya et al., Scientific Reports 2019, doi:10.25405/data.ncl.9693533) which showed that “more reliable information can be obtained at genus and family level”, or in comparison with longer 16S-ITS-23S amplicons (Cusco et al., F1000Research 2019, doi: 10.12688/f1000research.16817.2), which “remarkably improved the taxonomy assignment at the species level”.

3) It is not entirely clear how the authors define their core microbiome. Are they reporting mainly the most abundant taxa (dominant core microbiome), and would this change if you look at a taxonomic rank below the family level? How does the core compare, for example, with other studies of this same river?

The here-presented core microbiome indeed represents the most abundant taxa, with relatively consistent profiles between samples. We used hierarchical clustering (Figure 4a, C2 and C4) on the bacterial family level, together with relative abundance to identify candidate taxa. Filtering these for median abundance > 0.1% across all samples resulted in 27 core microbiome families. To clarify this for the reader, we have added a new paragraph to the Material and Methods (section 2.7; page 29, lines 653-658).

We have also performed the same analysis on the bacterial genus level and now display the top 27 most abundant genera (median abundance > 0.2%), together with their corresponding families and hierarchical clustering analysis in a new Supplementary Figure 4. Overall, high robustness is observed with respect to the families of the core microbiome: out of the top 16 core families (Figure 4b), only the NS11-12 marine group family is not represented by the top 27 most abundant genera (Supplementary Figure 4b). We reason that this is likely because its corresponding genera are composed of relatively poorly resolved references of uncultured bacteria, which could thus not be further classified.

To the best of our knowledge, there are only two other reports that feature metagenomic data of the River Cam and its wastewater influx sources (Rowe et al., Water Science & Technology 2016, doi:10.2166/wst.2015.634; Rowe et al., Journal of Antimicrobial Chemotherapy 2017, doi:10.1093/jac/dkx017). While both of these primarily focus on the diversity and abundance of antimicrobial resistance genes using Illumina shotgun sequencing, they only provide limited taxonomic resolution on the river's core microbiome. Nonetheless, Rowe et al. (2016) specifically highlighted Sphingobium as the most abundant genus in a source location of the river (Ashwell, Hertfordshire). This genus belongs to the family of Sphingomonadaceae, which is also among the five most dominant families identified in our dataset. It thus forms part of what we define as the core microbiome of the River Cam (Figure 4b), and we have therefore highlighted this consistency in our manuscript's Discussion (page 17, lines 316-319).

4) Please consider revising the amount of information in some of the figures (such as figure 2 and figure 3). The resulting images are tiny, the legends become lengthy and the overall impact is reduced. Consider splitting these or moving some information to the supplements.

To follow this advice, we have split Figure 2 into two less compact figures. We have moved more detailed analyses of our classification tool benchmark to the supplement (now Supplementary Figure 1). Supplementary Figure 1 notably also contains a new summary of the systematic computational performance measurements of each classification tool (see minor suggestions).

Moreover, we here suggest that the original Figure 3 may be divided into two figures: one to visualise the sequencing output, data downsampling and distribution of the most abundant families (now Figure 3), and the other featuring the clustering of bacterial families and associated core microbiome (now Figure 4). We think that both the data summary and clustering/core microbiome analyses are of particular interest to the reader, and that they should be kept as part of the main analyses rather than the supplement – however, we are certainly happy to discuss alternative ideas with the reviewers and editors.

5) Given that the authors claim to provide a simple, fast and optimized workflow it would be good to mention how this workflow differs or provides faster and better analysis than previous work using amplicon sequencing with a MinION sequencer.

Data throughput, sequencing error rates and flow cell stability have seen rapid improvements since the commercial release of MinION in 2015. In consequence, bioinformatics community standards regarding raw data processing and integration steps are still lacking, as illustrated by a thorough recent benchmark of fast5 to fastq format "basecalling" methods (Wick et al., Genome Biology 2019, doi: 10.1186/s13059-019-1727-y).

Early on during our analyses, we noticed that a plethora of bespoke pipelines have been reported in recent 16S environmental surveys using MinION (e.g. Kerkhof et al., Microbiome 2017, 10.1186/s40168-017-0336-9; Cusco et al., F1000 Research 2018, 10.12688/f1000research.16817.2; Acharya et al., Scientific Reports 2019, 10.1038/s41598-019-51997-x; Nygaard et al., Scientific Reports 2020, doi: 10.1038/s41598-020-59771-0). This underlines a need for more unified bioinformatics standards of (full-length) 16S amplicon data treatment, while similar benchmarks exist for short-read 16S metagenomics approaches, as well as for nanopore shotgun sequencing (e.g. Ye et al., Cell 2019, doi: 10.1016/j.cell.2019.07.010; Latorre-Pérez et al., Scientific Reports 2020, doi:10.1038/s41598-020-70491-3).

By adding a thorough speed and memory usage summary (new Supplementary Figure 1b), in addition to our (mis)classification performance tests based on both mock and complex microbial community analyses, we provide the reader with a broad overview of existing options. While the widely used Kraken 2 and Centrifuge methods provide exceptional speed, we find that this comes with a noticeable tradeoff in taxonomic assignment accuracy. We reason that Minimap2 alignments provide a solid compromise between speed and classification performance, with the MAPseq software offering a viable alternative should memory usage limitation apply to users.

We intend to extend this benchmarking process to future tools, and to update it on our GitHub page (https://github.com/d-j-k/puntseq). This page notably also hosts a range of easy-to-use scripts for employing downstream 16S analysis and visualization approaches, including ordination, clustering and alignment tests.

The revised Discussion now emphasises the specific advancements of our study with respect to freshwater analysis and more general standardisation of nanopore 16S sequencing, also in contrast to previous amplicon nanopore sequencing approaches in which only one or two bioinformatics workflows were tested (page 16, lines 297-306).

They also mention that nanopore sequencing is an "inexpensive, easily adaptable and scalable framework" The term "inexpensive" doesn't seem appropriate since it is relative. In addition, they should also discuss that although it is technically convenient in some aspects compared to other sequencers, there are still protocol steps that need certain reagents and equipment that is similar or the same to those needed for other sequencing platforms. Common bottlenecks such as DNA extraction methods, sample preservation and the presence of inhibitory compounds should be mentioned.

We agree with the reviewers that “inexpensive” is indeed a relative term, which needs further clarification. We therefore now state that this approach is “cost-effective” and discuss future developments such as the 96-sample barcoding kits and Flongle flow cells for small-scale water diagnostics applications, which will arguably render lower per-sample analysis costs in the future (page 18, lines 361-365).

Other investigators (e.g. Boykin et al., Genes 2019, doi:10.3390/genes10090632; Acharya et al., Water Technology 2020, doi:10.1016/j.watres.2020.116112) have recently shown that the full application of DNA extraction and in-field nanopore sequencing can be achieved at comparably low expense: Boykin et al. studied cassava plant pathogens using barcoded nanopore shotgun sequencing, and estimated costs of ~45 USD per sample, while we calculate ~100 USD per sample in this study. Acharya et al. undertook in situ water monitoring between Birtley, UK and Addis Ababa, Ethiopia, estimated ~75-150 USD per sample and purchased all necessary equipment for ~10,000 GBP – again, we think that this lies roughly within a similar range as our (local) study's total cost of ~3,670 GBP (Supplementary Table 6).

The revised manuscript now mentions the possibility of increasing sequencing yield by improving DNA extraction methods, by taking sample storage and potential inhibitory compounds into account in the planning phase (page 18, lines 348-352).

Minor points:

-Please include a reference to the statement saying that the river Cam is notorious for the "infections such as leptospirosis".

There are indeed several media reports that link leptospirosis risk to the local River Cam (e.g. https://www.cambridge-news.co.uk/news/cambridge-news/weils-disease-river-cam-leptosirosis-14919008 or https://www.bbc.com/news/uk-england-cambridgeshire-29060018). As we, however, did not find a scientific source for this information, we have slightly adjusted the statement in our manuscript from referring to Cambridge to instead referring to the entire United Kingdom. Accordingly, we now cite two reports from Public Health England (PHE) about serial leptospirosis prevalence in the United Kingdom (page 13, lines 226-227).

-Please check figure 7 for consistency across panels, such as shading in violet and labels on the figures that do not seem to correspond with what is stated in the legend. Please mention what the numbers correspond to in outer ring. Check legend, where it says genes is probably genus.

Thank you for pointing this out. We have revised (now labelled) Figure 8 and removed all inconsistencies between the panels. The legend has also been updated, which now includes a description of the number labelling of the tree, and a clearer differentiation between the colour coding of the tree nodes and the background highlighting of individual nanopore reads.

-Page 6. There is a "data not shown" comment in the text: "Benchmarking of the classification tools on one aquatic sample further confirmed Minimap2's reliable performance in a complex bacterial community, although other tools such as SPINGO (Allard, Ryan, Jeffery, & Claesson, 2015), MAPseq (Matias Rodrigues, Schmidt, Tackmann, & von Mering, 2017), or IDTAXA (Murali et al., 2018) also produced highly concordant results despite variations in speed and memory usage (data not shown)." There appears to be no good reason that this data is not shown. In case the speed and memory usage was not recorded, is advisable to rerun the analysis and quantify these variables, rather than mentioning them and not reporting them. Otherwise, provide an explanation for not showing the data please.

This is a valid point, and we agree with the reviewers that it is worth properly following up on this initial observation. To this end, our revised manuscript now entails a systematic characterisation of the twelve tools' runtime and memory usage performance. This has been added as Supplementary Figure 1b and under the new Materials and Methods section 2.2.4 (page 26, lines 556-562), while the corresponding results and their implications are discussed on page 16, lines 301-306. Particularly with respect to the runtime measurements, it is worth noting that these can differ by several orders of magnitude between the classifiers, thus providing an additional clarification on our choice of the - relatively fast - Minimap2 alignments.

-In Figure 4, it would be important to calculate if the family PCA component contribution differences in time are differentially significant. In Panel B, depicted is the most evident variance difference but what about other taxa which might not be very abundant but differ in time? One can use the fitFeatureModel function from the metagenomeSeq R library and a P-adjusted threshold value of 0.05, to validate abundance differences in addition to your analysis.

To assess if the PC component contribution of Figure 5 (previously Figure 4) significantly differed between the three time points, we have applied non-parametric tests to all season-grouped samples except for the mock community controls. We first applied Kruskal-Wallis H-test for independent samples, followed by post-hoc comparisons using two-sided Mann-Whitney U rank tests.

The Kruskal-Wallis test established a significant difference in PC component contributions between the three time points (p = 0.0049), with most of the difference stemming from divergence between April and August samples according to the post-hoc tests (p = 0.0022). The June sampled seemed to be more similar to the August ones (p = 0.66) than to the ones from April (p = 0.11), recapitulating the results of our hierarchical clustering analysis (Figure 4a).

We have followed the reviewers' advice and applied a complementary approach, using the fitFeatureModel of metagenomeSeq to fit a zero-inflated log-normal mixture model of each bacterial taxon against the time points. As only three independent variables can be accounted for by the model (including the intercept), we have chosen to investigate the difference between the spring (April) and summer (June, August) months to capture the previously identified difference between these months. At a nominal P-value threshold of 0.05, this analysis identifies seven families to significantly differ in their relative composition between spring and summer, namely Cyanobiaceae, Armatimonadaceae, Listeriaceae, Carnobacteriaceae, Azospirillaceae, Cryomorphaceae, and Microbacteriaceae. Three out of these seven families were also detected by the PCA component analysis (Carnobacteriacaea, Azospirillaceae, Microbacteriaceae) and two more (Listeriacaea, Armatimonadaceae) occured in the top 15 % of that analysis (out of 357 families).

This approach represents a useful validation of our principal component analysis' capture of likely seasonal divergence, but moreover allows for a direct assessment of differential bacterial composition across time points. We have therefore integrated the analysis into our manuscript (page 10, lines 184-186; Materials and Methods section 2.6, page 29, lines 641-647) – thank you again for this suggestion.

-Page 12-13. In the paragraph: "Using multiple sequence alignments between nanopore reads and pathogenic species references, we further resolved the phylogenies of three common potentially pathogenic genera occurring in our river samples, Legionella, Salmonella and Pseudomonas (Figure 7a-c; Material and Methods). While Legionella and Salmonella diversities presented negligible levels of known harmful species, a cluster of reads in downstream sections indicated a low abundance of the opportunistic, environmental pathogen Pseudomonas aeruginosa (Figure 7c). We also found significant variations in relative abundances of the Leptospira genus, which was recently described to be enriched in wastewater effluents in Germany (Numberger et al., 2019) (Figure 7d)."

Here it is important to mention the relative abundance in the sample. While no further experiments are needed, the authors should mention and discuss that the presence of DNA from pathogens in the sample has to be confirmed by other microbiology methodologies, to validate if there are viable organisms. Definitively, it is a big warning finding pathogen's DNA but also, since it is characterized only at genus level, further investigation using whole metagenome shotgun sequencing or isolation, would be important.

We agree that further microbiological assays, particularly target-specific species isolation and culturing, would be essential to validate the presence of living pathogenic bacteria. Accordingly, our revised Discussion now contains a paragraph that encourages such experiments as part of the design of future studies (with a fully-equipped laboratory infrastructure); page 17, 338-341.

-Page 15: "This might help to establish this family as an indicator for bacterial community shifts along with water temperature fluctuations."

Temperature might not be the main factor for the shift. There could be other factors that were not measured that could contribute to this shift. There are several parameters that are not measured and are related to water quality (COD, organic matter, PO4, etc).

We agree that this was a simplified statement, given our currently limited number of samples, and have therefore slightly expanded on this point (page 17, lines 323-325). It is indeed possible that differential Carnobacteriaceae abundances between the time point measurements may have arisen not as a consequence of temperature fluctuations (alone), but instead as a consequence of the observed hydrochemical changes like e.g. Ca2+, Mg2+, HCO3- (Figure 6b-c) or possible even water flow speed reductions (Supplementary Figure 6d).

-"A number of experimental intricacies should be addressed towards future nanopore freshwater sequencing studies with our approach, mostly by scrutinising water DNA extraction yields, PCR biases and molar imbalances in barcode multiplexing (Figure 3a; Supplementary Figure 5)."

Here you could elaborate more on the challenges, as mentioned previously.

We realise that we had not discussed the challenges in enough detail, and the Discussion now contains a substantially more detailed description of these intricacies (page 18, lines 343-359).

What Bush called "associative indexing" is the key idea behind the memex. Any item can immediately select others to which it has been previously linked.

Once two items are linked, tapping a button would take you from one to the other.

Although Bush envisioned associative trails to be navigable sequences of original content and notes interspersed, what seems to make more sense when viewed through today's technology, is a rich document of notes where the relevant pieces from external documents are transcluded.

I find this idea of saved associative trails very interesting. In Roam the equivalent would be that you can save a sequence of opened Pages.

It should be easy to surpass the mind's performance in terms of storage capacity as well as lossiness. It might be more difficult to surpass it in terms of the speed and flexibility with which it "follows an associative trail"

The human mind doesn't work according to the file-cabinet metaphor — it operates by association.

"With one items in its gras, it snaps instantly to the next that is suggested by the association of thoughts, in accordance with some intricate web of trails carried by the cells of the brain."

Bush emphasises the importance of retrieval in the storage of information. He talks about technical limitations, but in this paragraph he stresses that retrieval is made more difficult by the "artificiality of systems of indexing", in other words, our default file-cabinet metaphor for storing information.

Information in such a hierarchical architecture is found by descending down into the hierarchy, and back up again. Moreover, the information we're looking for can only be in one place at a time (unless we introduce duplicates).

Having found our item of interest, we need to ascend back up the hierarchy to make our next descent.

Retrieval is the key activity we're interested in. Storage only matters in as much as we can retrieve effectively. At the time of writing (1945) large amounts of information could be stored (extend the record), but consulting that record was still difficult.

As scientific progress extends into increased specializations, efforts at integrating across disciplines are increasingly superficial.

Bush emphasises the need for notes to not only be stored, but also to be queried (consulted).

The rate at which we're generating new knowledge is increasing like never before (and this was written in 1945), but our ability to deal with that information has remained largely unimproved.

Specialization, although necessary, has rendered it impossible to stay up to date with the advances of a field.

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity):

This manuscript follows on from previous work from the Rhind lab to investigate whether the load of MCMs at origins is a factor in when the origin activate (as a population average) during S phase. The authors use budding yeast and a auxin degron system to modulate the levels of an MCM subunit. This allows them to titrate down the concentration of the MCM hexamer and observe the effect. Crucially, they assay both the reduction in MCM load at origins and the subsequent replication dynamics in the same experiment. This is the power of their approach and allows them to rigorously test their hypothesis.

**Major comments**

1.I found the introductory paragraph discussing the Rhind lab hypothesis about the possibility of multiple MCM being loaded at origins somewhat misleading. The first paragraph of the discussion was much clear. However, I feel that the introductory paragraph should deal with the difference between the two proposals: 0-1 MCM-DH per origin (de Moura et al), vs 0-50+ MCM-DH (Yang et al). It s also important to note that Foss et al find that "In budding yeast, [MCM] complexes were present in sharp peaks comprised largely of single double-hexamers" - i.e. consistent with 0-1 MCM-DH per origin.

To improve the balance of the introduction, I think the authors should briefly introduce the concepts behind the 0-1 MCM-DH per origin; this was defined as origin competence by Stillman and clearly described by McCune et al (2008; see figure 8) prior to the work from de Moura et al.

Furthermore, in the discussion the authors should be more even-handed. To date there is no data to conclusively rule one way or the other in distinguishing between single vs multiple MCMs. The authors cite Lynch et al and state "overexpression of origin-activating factors in S phase causes most all origins to fire early in S phase, consistent with most origins having at least one MCM loaded". However, Lynch et al report equivalent (roughly equal) origin efficiencies, but the assay doesn't distinguish between all going up to high efficiency or all going to a lower intermediary efficiency. Given that fork factors (polymerases, etc) are likely to become limiting at some point (or checkpoints could be activated due to limited dNTP supplies) it would seem plausible that uniform origin efficiency could be a consequence of less than maximal origin firing. As part of this discussion it would be useful for the authors to include what conclusions have been reached on MCM load from in vitro systems (with chromatin substrates).

Because the main focus of the paper is not dependent on whether MCM stoichiometry varies from 0 to 1 or 0 to many, we had relegated our discussion of absolute stoichiometry to the Discussion. However, it is clear from multiple reviewer's comments that it is something very much on readers minds. Therefore, we have now included a brief introduction to the 0-to-1 and 0-to-many scenarios in the Introduction and moved the bulk of the discussion of the data supporting the two scenarios to the Discussion.

2.The authors are not the first to look at the consequence of reduced MCM concentrations on origin function. This was essentially the basis for the MCM screen undertaken by Bik Tye's lab that first identified the MCM genes. In addition to temperature sensitive mutants, the Tye group also examined heterozygotes (Lei et al., 1996) to show differential effect on the ability of two origins to support plasmid replication. The authors finds are entirely consistent with these early studies, particularly since ARS416 (formerly ARS1) was found to highly sensitive to reduced MCM levels and ARS1021 (formerly ARS121) was found to be insensitive to MCM levels. The authors find a signifiant reduction in MCM load at ARS416, but the MCM load at ARS1021 is unaltered by reduced MCM concentration. It would be worth the authors noting this consistency. The authors do cite the Lei study, but not in this context. The original MCM screen was published here:

Maine, G., Sinha, P., Tye, B. (1984). Mutants of S. cerevisiae defective in the maintenance of minichromosomes Genetics 106(3), 365 - 385.

Furthermore, at the end of the discussion the authors state that "it will be interesting to dissect the specific cis- and trans-acting factors that make origins sensitive or resistant to changes in MCM levels". The equivalent effect reported by the Tye lab has already been dissected by the Donaldson lab (Nieduszynski et al., 2006) and perhaps it would be worth briefly mentioning their findings.

We have included both of these literature precedents in the Discussion.

3.The authors should show the flow cytometry data for each of their cell cycle experiments, if only in supplementary figures. This is important to allow a reader (and reviewer) to judge the level of synchrony achieved when interpreting the results.

This data is now included as Figure S1

4.I think the authors should show the ChIP signal at some example origins, including ones sensitive and insensitive to the reduction in MCM concentration. Currently all the high resolution ChIP data (i.e. over 1400 bp, e.g. Fig 3a) is presented as meta-analyses of many origins.

We will include this analysis in a subsequent revision.

5.When describing the results in Fig 4a the authors focus on changes (highlighted in black boxes) that fit their expectation. However, there are other sites that should at least be mentioned that don't seem to fit the authors model, e.g. ARS517, ARS518. It would be worth discussing what fraction of the timing data can be explained by the reduced MCM load.

We now explicitly point out that Figures 4c and 4d address this issue of the robustness of the correlation. Although there is significant variation, as the reviewer points out, the trend is seen genome wide. As it happens, both ARS517 and ARS518 do fit the model reasonably well. They have intermediate loss of MCM signal and intermediate delay in timing.

**Minor comments**

-These data, rather than this data (throughout).

I suspect that the journal style and/or copy editors will make the final call. However, I will point out that although 'data' is most certainly plural in Latin, its predominate modern English usage is as a mass noun, such as water or sand or information. In general, users do not think of, or use, 'data' as a collection of discrete elements, each on being a 'datum', a contention supported by the very infrequent use of the word datum. For instance, in ChIP-seq experiment, what is a datum? Each individual read? Each individual nucleotide in each read? The quality score for each individual nucleotide in each read? Each pixel in each image from the sequencer? When one wants to refer to an individual piece of data, common usage is to refer to a data point, just as one would refer to a grain of sand. Moreover, if 'data' were plural, it would be incorrect to use it in phrases such as "there is very little data available". Would the review really suggest using "there are very few data available"?

-the authors should clearly state in figure legends what window size has been used in analysing genomic data.

All analyses were done using 1kb windows, as now stated in the figure legends.

-in figure 2a the authors show pairwise comparisons between conditions, it would be nice to see the 3rd pairwise comparisons perhaps as a supplementary figure

We have included the third comparison in Figure 2a.

-in figure 2c it would be clearer to use the same colour for the lines and the points

The regression lines are in the same colors as the data points they fit. x=y is shown in blue for comparison, as now noted in the figure legend.

-the authors should avoid the use of red/green colour combinations in their figures (see: https://thenode.biologists.com/data-visualization-with-flying-colors/research/)

All figures will be redrawn in colorblind-accessible colors in a subsequent revision.

-in the text the authors state "ORC binding to the ACS and subsequent MCM loading is a directional process dependent on a ACS- site and a similar but inverted nearby sequence (Xu et al., 2006)". I think it would be more appropriate to cite the following study here:

Coster, G., Diffley, J. (2017). Bidirectional eukaryotic DNA replication is established by quasi-symmetrical helicase loading Science (New York, NY) 357(6348), 314 - 318. https://dx.doi.org/10.1126/science.aan0063

The Coster reference has been included.

-the list of factors that influence replication timing should include Rif1, whereas it is less clear that Rpd3 acts within the unique genome (as opposed to indirectly via repetitive DNA, e.g. rDNA)

Rif1 has been added to the list.

-figure 4 - it might help to mark the centromere on panel a. Also, why do the ChIP peaks and annotated origins appear to line up so poorly?

The shift between the peaks and the ACS positions was introduced during the construction of the figure. Thanks for catching it. The alignment has been corrected and the centromere annotation has been added.

-figure 4d - would it not be better to use fraction of lost MCM signal on the x-axis as in previous figures?

If T_rep was a linear function of MCM stoichiometry, fraction lost would work as well as amount lost. However, we find that there is a lower correlation between fraction of MCM signal lost and T_rep delay than between absolute MCM signal lost and T_rep delay, suggesting a more complicated relationship.

-"with galactose or raffinose, to induce or repress Mcm2-7 overexpression, respectively." This is incorrect, raffinose does not repress this promoter (that requires glucose).

Fixed.

-the S. pombe spike in is a great addition to the over expression experiments. It's a shame that it wasn't included in the auxin experiments.

Yes, we agree.

-why does the data in fig 5d appear to be at much lower resolution that the previous ChIP data?

The resolution was inadvertently reduced during the rendering of the figure. The resolution has restored.

-in the sequencing analysis pipeline for MCM ChIP the authors use a 650 bp upper size limit; why have such a large threshold compared to the size of a nucleosome? Are the analyses and findings sensitive to this size threshold?

Although the MNase digestion was optimized to produce mostly mononucleosomal-sized digestion, some di- and very little tri- nucleosomal fragments still remain. In order to capture as many of the MCM-protected immunoprecipitated fragments as possible, the upper limit was set at 650 bp (up to 4 nucleosomes-worth of DNA). However, there is a very minimal contribution from fragments larger than mononucleosomes, qualitatively as well as quantitatively in 1kb windows around origins. Figure 3a provides a qualitative depiction of the contribution of dinucleosomes (input, ~300bp).

-the repliscope package was published here:

Batrakou, D., Müller, C., Wilson, R., Nieduszynski, C. (2020). DNA copy-number measurement of genome replication dynamics by high-throughput sequencing: the sort-seq, sync-seq and MFA-seq family. Nature Protocols 15(3), 1255 - 1284. https://dx.doi.org/10.1038/s41596-019-0287-7

The reference has been corrected.

Reviewer #1 (Significance):

This work builds upon a body of work from the Rhind group (and others) to determine the contribution of MCM load to replication origin activation dynamics. To my mind this is the most convincing dataset and analysis to date and goes a long way to supporting the model that the efficiency of MCM loading is a major factor in determining the mean replication time of an origin. As the authors state, they are still not able to distinguish between two different models of MCM load (single vs multiple). It would be interesting for the authors to discuss how these two models could be distinguished in the future (perhaps with single cell/molecule experiments).

This study will be of interest to those in the fields of DNA replication and genome stability.

My field of expertise is DNA replication and replication origin function.

Reviewer #2 (Evidence, reproducibility and clarity):

**Summary:**

This is a nice study that characterizes the consequences of limiting or increasing Mcm expression on the replication program. Prior ChIP experiments in yeast have observed that not all origins exhibit the same level of Mcm enrichment and that increased mcm enrichment was correlated with origin activity. These observations led to two different models -- a) that multiple Mcm2-7 double hexamer complexes are loaded at some origins and b) a probabilistic model where the differential enrichment of Mcm2-7 reflected the fraction of cells in a population that had loaded the Mcm2-7 complex at a specific origin. While the titration experiments presented here don't provide any conclusive support for either model, they do provide some novel and relevant insights for the replication field, in part, due to the increased resolution and quantification afforded by the MNase ChIP-seq approach (and S. pombe spike in). The authors very nicely demonstrate that origins are differentially sensitive to Mcm2-7 depletion and that loss of Mcm2-7 loading results in an altered replication timing profile. The origins most impacted by loss of Mcm2-7 are 'weak' origins as described by the Fox group. Intriguingly, the authors find that the 5X overexpression of Mcm2-7 does not perturb the relative Mcm2-7 loading at individual origins, but rather instead globally represses Mcm2-7 association at all origins. They also find that overexpression of both Cdt1 and Mcm2-7 is detrimental to the cell (although no obvious replication phenotype was observed). Finally, the authors present a reasonable interpretation of their data in the context of models for replication timing which was very well articulated.

**Major Comments:**

From the methods it appears that different analyses were performed with different replicates?

"Replicate #1 was used for all analyses except for V plots, for which the higher resolution Replicate #2 was used."

Ideally all of the conclusions should be supported by all the replicates independently, or if the replicates are concordant -- they should be merged (at a similar sequencing depth) prior to doing the analyses.. Even the v-plots with merged replicates will be informative due to the greater sequencing depth.

Though we agree that greater sequencing depth would be informative for aggregation analysis, we think that one of the main strengths of our study is the analysis of MCM quantitation and replication timing in the same population of cells. Although the experiments were performed in exactly the same way, there is always slight biological or temporal differences between the replicates, due to the complicated nature of the experimental design. This variation increases the noise between the MCM ChIP and the replication timing analyses. Therefore, were analyzed the replicates separately. However, we did do all of the analyses on both replicates and got similar results. We have now explicitly stated as much.

The authors should provide a separate analysis for the larger nucleosomal sized fragments and smaller putative MCM double hexamer fragments with regards to the Mcm loading and relationship to ACS and orientation. They may represent an interesting intermediate with mechanistic consequences for the interpretation.

We will include the suggested analysis in a subsequent revision.

The authors should present the v-plots and an analysis of which side the Mcm's load for the overexpression studies. I was surprised that there was no further in-depth analysis for these two extremes. Perhaps similar conclusions will be reached, but it should at least be mentioned/presented as a supplementary figure.

We will include the suggested analysis in a subsequent revision.

**Minor Comments:**

This is largely semantic, but the majority of MNase ChIP-seq signal recovered is associated with the nucleosomes and not in the NDR and as the signal in the NDR is differentially sensitive to digestion, I would suggest rephrasing the following sentence:

"In contrast to previous genome-wide reports (Belsky et al., 2015), but in agreement with recent in-vitro cryo-EM structures (Miller et al., 2019), we also observe MCM signal in the nucleosome-depleted region (NDR) of origins. "

to :

"In agreement with a previous genome-wide report (belsky 2015), we found that the bulk of the MCM signal was associated with nucleosomal sized fragments; however the increased resolution afforded by our approach allowed us to also detect protected fragments in the NDR as predicted by recent in vitro cryo em structures..."

We have modified the sentence as suggested.

As a sanity check, please double check V-plots and presence of small fragments with the digestion conditions. In the Henikoff manuscript the bulk of sub-nucleosomal fragments were lost with the longer digestion time. Specifically, the TF footprints were more pronounced with minimal digestion. While it might be argued that the longer digestion more tightly resolved the binding site, in many cases they were completely lost with the 20 minute digestion. This is just a simple check -- I don't doubt the results as reported given the experimental conditions are very different. For example, the henikoff manuscript did not use cross linking or an antibody enrichment step.

We double checked and confirmed that more small fragments are found in the more digested library. The reason that we see more small fragments when we digest more, in contrast to the contrary observation in the Henikoff paper is presumably because MCM has a larger footprint than a transcription factor and protects that footprint more effectively.

Last paragraph of the "MCM associates with nucleosomes section" which reports that the Mcm2-7 complex is loaded up or downstream from the ACS independent of orientation should cite Belsky 2015 (Figure 5 and discussion) for the initial observation.

Done.

The authors argue that the global reduction in MCM loading associated with overexpression may be a technical artifact given that all origins exhibit a proportional reduction in mcm2-7 loading. However, this is exactly what the S. pombe spike in control is intended for. The relative difference between individual origins resulting from Mcm2-7 depletion would still be evident without the spike in. The authors do discuss different possibilities, but I would not be so keen to discard this as technical artifact.

We, too, are reluctant to dismiss this result as a technical artifact. However, we are at a loss to offer any other explanation. We raise a handful of biological possibilities in the Discussion, but dismiss each one as failing to account for our results. We would be happy to entertain other suggestions.

Reviewer #2 (Significance):

This work has several advances that will be appreciated by the replication field -- including a high resolution view of Mcm2-7 loading in the context of chromatin; the impact of titrating (low and high) MCM expression on MCM loading and replication timing program; and a well reasoned discussion of how different models of MCM loading would impact origin activation and replication timing program. The work builds on prior studies in the field (eg. Belsky 2015), while some of the conclusions regarding the localization of the Mcm2-7 complex relative to the ACS and surrounding nucleosomes are confirmatory, the increased resolution provides new insight (like the enrichment of small fragments in the NDR) that could be further strengthened by additional analysis (see above).

My expertise is DNA replication and chromatin.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

In this study, the authors use Auxin-mediated degradation of Mcm4 to reduce the concentration of the MCM helicase complex in yeast, and determine the effects of this reduction on both MCM-origin association (interpreted as MCM loading) by MNase-MCM-ChIPSeq and on replication origin function by Sync-Seq replication timing experiments (deep sequencing of a yeast population as it progresses through a synchronized S-phase). Complementary experiments testing the effect of induced MCM complex over-expression on MCM-origin association are also performed.

The authors find that reducing Mcm4 levels (and thus loading-competent MCM complexes) causes yeast cells to be more sensitive to DNA replication stress. In addition, not all origins are equally susceptible to reductions in MCM levels; the origins that do lose MCM binding at reduced MCM levels show a reduction in activity and an associated delay in their replication time under those conditions. Finally, over-expression of the MCM complex has no effect on MCM-origin association or origin function, suggesting that MCM levels are not limiting for origin licensing in yeast under normal lab conditions. The strengths of the study are the well-executed experiments and very nice data that are presented. However, there are several weaknesses. The authors make conclusions that are not supported by their data; and several of the outcomes are not at all unexpected based on extensive published studies in yeast and mammalian cells, raising issues about whether this study advances and/or clarifies the current gaps in the field. While some of the relevant past studies were referenced, the authors did not place their own study in the context to published work and current models in the field, which reduced the scholarly value of their study. Because the work was not placed in context of the field, some of the rationale and conclusions were misleading.

**Some specific major comments:**

1,The title is misleading. The authors have clearly shown that when MCM levels are be made limiting in an engineered system, some origins are substantially less active, which means that these origin loci are replicated "passively" (i.e. by a Replication Fork (RF) emanating from a distal origin) rather than actively (i.e. by "firing" and initiating replication). Their own replication data show that. But this competition is only revealed when MCM levels are artificially/experimentally lowered. What is the evidence that competition for MCM complexes among individual origins establishes replication timing patterns in yeast? If anything, the over-expression experiment suggests the opposite--that MCM levels are not limiting and therefore do not play a substantial role in establishing the replication timing patterns that are observed in yeast. Instead those patterns appear to result primarily from the fact that MCM complex activation factors are present in limiting concentrations relative to origins.

We agree with the reviewer's analysis and have revised the title to "The Capacity of Origins to Load MCM Establishes Replication Timing Patterns".

2,The abstract states that "the number of MCMs loaded onto origins has been proposed to be a key determinant of when those origins initiate DNA replication during S-phase". While it is true that this lab has proposed this model in budding yeast, the current study performs no experiments that directly address this model--i.e. that i. individual origins possess a different number of MCM complexes and or ii that these differences underlie timing differences. They acknowledge this point in their Discussion--a ChIPSeq experiment is an ensemble experiment--there is no way to know that differences in MCM signals correspond to a different number of MCM complexes per origin versus a differences in the fraction of cells that contain and MCM complex at all at a given origin . But this statement in the abstract, combined with their conclusion in the same section of the paper: "Our results support a model in which the loading activity of origins, controlled by their ability to recruit ORC and compete for MCM, determines the number of helicases loaded, which in turn affects replication timing" implies that they have tested a model that they have not tested. Given how quickly readers "skim" the literature these days, a misleading abstract can do a lot of damage to a field. The results presented in this study neither support nor refute the model for the number of helicases loaded per origin, and the fact that reducing origin licensing efficiency by making the major substrate limiting reduces the number of licensed origins in a cell population is fully expected based on the current state of the field .

Four questions are addressed in this comment. The first is whether there is variable MCM stoichiometry at origins. The second is whether that variation ranges from 0 to 1 and 0 to many. The third is if the variation is stoichiometry affects replication timing. The fourth is how this variation in stoichiometry comes about.

Our work is based on the conclusion, supported by a substantial body of literature, that MCM loading stoichiometry varies among origins. Our data in this paper further supports this conclusion.

As the reviewer notes, and as we had tried to make clear, the data is this paper does not address the range of the variation. Moreover, as we also tried to make clear, our hypotheses, results and conclusions are not affected by whether the range is 0 to 1 or 0 to many.

This paper focuses on Questions 3 and 4. We have reworked the introduction to make these distinctions more clear.

We have also corrected the abstract to refer to "the stoichiometry", instead of "the number", of MCMs.

3,The rationale for the study as stated in the Introduction: "Although the molecular biochemistry of initiation at individual origins continues to be elucidated in great detail (Bleichert, 2019), the mechanism governing the time at which different regions of the genome replicate has remained largely elusive (Boos and Ferreira, 2019)." Is also misleading. In fact, in budding yeast (and other organisms) there have been several advances in this area particularly with respect to DNA replication origin activation. The S-phase origin activation factors are limiting for origin function, and factors such as Ctf19 at centromeres and Fkh1/2 at non-centromeric early-acting origins help to directly recruit the limiting S-phase factor, Dbf4, to origins. It is misleading to ignore this substantial progress and not make an effort to place this current study, which is important and one of the first to look directly at MCM loading control in yeast, into a relevant context with respect to what is known. What's interesting is that this S-phase model assumes/requires that most origins are, in fact, licensed and thus that differences in licensing efficiency are not a major driving of replication timing patterns in yeast. But we do not know why there are only subtle differences in MCM loading---this study may help explain that.

We have broadened the scope of our Introduction and Discussion to address these points. However, it is not the case that "there are only subtle differences in MCM loading". MCM ChIP-seq (, and this paper) and MCM ChEC-seq both show well over ten-fold variation in MCM stoichiometry at origins. We have now explicitly made this point in the Introduction.

4,The authors link the differential ability of MCM loading deficiencies when MCM is made limiting to differences in ORC binding categories. The "weak" origins, that presumably bind ORC weakly, were most affected by reductions in MCM. Are these origins less efficient than the other categories, DNA and chromatin-dependent (using the origin efficiency metric data from the Whitehouse lab) where MCM binding is not reduced as much? In normal cells are these early or late origins? Is the idea that the role of excess MCM is to achieve a sufficient number or "back up" origins per cell to deal with potential stress, as proposed by the Blow and Schwob labs in tissue culture cells many years ago? It seems likely that the data reported here are in fact confirmations of those early studies in mammalian cells---which is useful to know even if not unexpected.

We will include the suggested analyses in a subsequent revision.

Excess MCM do, as has been long appreciated and as we discuss, contribute to replication-stress tolerance. However, that is not a major point of our paper.

5,Aren't the results that losing MCM signal corresponds to loss of origin activity peaks entirely expected? The same result would be obtained if you made a point mutation in that origin's ACS. Of course preventing an origin from being licensed will delay that region's replication time in S-phase because it now must be replicated passively. Licensing affects replication timing patterns because the MCM complex is the substrate for limiting S-phase factors, but that is far different from concluding that the number of MCMs at an origin is what controls the time in S-phase when an origin is activated.

Yes, "the results that losing MCM signal corresponds to loss of origin activity peaks [are] entirely expected". However, this is not the important result. The key result is that the distribution of MCM at origins is not uniformly affected, which leads to our conclusions that, in wild-type cells, origin capacity dominates MCM stoichiometry and that, when MCM become limiting, origin activity (probably determined by ORC affinity) becomes critical—neither of which were expected results. In any case, the expected correlation between MCM loading and origin activity was observed as a consequence of measuring MCM stoichiometry and replication timing and is an obvious analysis to include, so we did so.

6,The authors stated that the measured MCM abundance for the 43% of origins that are not known to be controlled by the multiple mechanisms that have been shown to control origin replication time. Is this because they think that MCM loading contributes to the timing control of only these origins? Was MCM loading not affected at any of these other origins when MCM levels were reduced? Are those 43% of origins in the "weak" binding category in terms of ORC? The rationale for eliminating so many origins from these analyses were not clear.

We propose that the probability of origin activation is the product of the stoichiometry of MCM at the origin and the rate of MCM activation, which may be affected by trans-acting factors. For the 43% of origins for which there is no known trans-acting regulation, the correlation with stoichiometry is stronger. However, the correlation holds when looking at all origin, too. The suggestion to look at only the 57% of origins with known trans-action regulation is a good one. We will include this analysis and the other suggested analyses in a subsequent revision.

7,Doesn't the data in Figure 4c at 0 mM auxin support the conclusion that differences in MCM ChIP signals have negligible effects on origin activation time, in contrast to the publication by Das, 2015 from this lab? Or is the point that these origins are sensitive to reductions in MCM levels and the more sensitive they are the more delayed their replication time (but again, doesn't that have to be true? If they are losing MCM signals they cannot function as origins, so they are replicated passively and, by definition, will show delayed replication timing. An origin is defined as such by a loaded MCM complex.)

No. The reason the correlation in 4c is not a good as in our previous work is that in Das 2015 we compared origin-activation efficiency (calculated from our stochastic model in Yang 2010), instead of T_rep, which we used here. T_rep is a convolution of origin-activation time and passive-replication time, reducing to correlation. The important observation is that the correlation gets better as MCM levels are reduced.

The correlation between MCM stoichiometry and activation efficiency may seem trivial, but just because a model is simple does not mean it is not correct. If stoichiometry was the only factor regulating origin activation, we would expect a stronger correlation. So, we conclude that there are other factors at play, quite possible the trans-acting factors that the reviewer mentions in their second point. However, if stoichiometry played no role, we would expect no correlation. So, we propose that MCM stoichiometry is "an important determinant of replication timing".

8,I do not understand the conclusions from Figure 4d. There is an extremely small positive correlation between how much of an MCM signal is lost and delay in replication time of an origin, but this correlation is not surprising as an unlicensed origin cannot be an origin and will be replicated passively. What seems most surprising about these data is that the effect is so weak, not that it exists. There is quite a lot of scatter in this plot at 500 uM auxin, with some origins losing a given amount of signal (x) and being only slightly delayed in replication time, and others losing the same amount of signal (x) and being substantially delayed. What underlies this outcome?--Are the ones that are not substantially delayed closer to origins that have not been affected at all by MCM reductions? Why is the correlation so weak? The other regulators of origin activation time have stronger and more precise effects--for example the centromere-control can be precisely eliminated so that only the replication time of the centromere-proximal origins are delayed.

We believe that much of the noise in Figure 4d is due, as the reviewer suggests, to passive replication of origins which lose most of their MCM signal and become inactive but happen to reside next to origins which don’t lost any MCM signal and fire early. And excellent example is ARS 510 (see Figure 4a). ARS510 loses most of its MCM signal and clearly loses its initiation peak in the T_rep plot. However, because it is next to ARS511, which does not lose much MCM signal and which remains a efficient origin, ARS510 is still replicated early. We will include this example in a subsequent revision.

9,Multiple studies in yeast and mammalian cells indicate that MCM subunits are in excess relative to other licensing and S-phase initiation factors, so it is not unexpected that over-expressing MCM did not lead to enhanced levels of licensing. It seems much more plausible that Cdc6 or Cdt1 or both factors are present in limiting amounts for MCM loading, so I did not understand the point of over-producing MCM subunits. If the "weak" origins are the ones that are most dramatically affected by reducing MCM to "limiting" levels, isn't the question whether you can increase licensing at these origins when you over-produce a factor that is likely limiting for licensing, such as Cdt1 or Cdc6 (or both) while leaving MCM at its normal levels. The fact that MCM levels are not limiting for licensing is not surprising and, if anything, argues against these levels having a regulatory role in origin activation timing---which seems to be the opposite of what the authors want to conclude.

Orc1-6, Cdc6 and Cdt1 are all substoichiometric to MCM. However, they all act catalytically to load MCM. So, although they may be kinetically limiting, they do not prevent most or all MCMs being loaded in wild-type cells. The fact that overexpressing MCMs (with or without Cdt1) does not allow for more MCM loading suggests that under normal conditions origins are saturated with MCMs and have little or no capacity to load more MCM, even when given plenty of time to do so. From this result, we conclude that origin capacity is a major determinant of MCM loading in wild-type cells. From our MCM-reduction experiments, we also conclude that, when MCM is limiting, origin competition affects which origins load MCMs faster. However, we agree with the reviewer's first point, that our title gave the incorrect impression that we concluded that origin competition is the primary determinant of MCM loading in wild-type cells. Thus, as suggested, we have changed the title. We have also reworked the Introduction and Discussion to more clearly explain that competition is only a determining factor when MCMs are limited.

In summary, I think the technical aspects of the experiments were quite strong, but I do not think that the experiments answered the question that was posed by the authors.

**Minor points:**

Many places where "This data" should be changed to "These data". Data are plural.

See comments on this point in the response to Reviewer #2.

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Referee #3

Evidence, reproducibility and clarity

In this study, the authors use Auxin-mediated degradation of Mcm4 to reduce the concentration of the MCM helicase complex in yeast, and determine the effects of this reduction on both MCM-origin association (interpreted as MCM loading) by MNase-MCM-ChIPSeq and on replication origin function by Sync-Seq replication timing experiments (deep sequencing of a yeast population as it progresses through a synchronized S-phase). Complementary experiments testing the effect of induced MCM complex over-expression on MCM-origin association are also performed.

The authors find that reducing Mcm4 levels (and thus loading-competent MCM complexes) causes yeast cells to be more sensitive to DNA replication stress. In addition, not all origins are equally susceptible to reductions in MCM levels; the origins that do lose MCM binding at reduced MCM levels show a reduction in activity and an associated delay in their replication time under those conditions. Finally, over-expression of the MCM complex has no effect on MCM-origin association or origin function, suggesting that MCM levels are not limiting for origin licensing in yeast under normal lab conditions. The strengths of the study are the well-executed experiments and very nice data that are presented. However, there are several weaknesses. The authors make conclusions that are not supported by their data; and several of the outcomes are not at all unexpected based on extensive published studies in yeast and mammalian cells, raising issues about whether this study advances and/or clarifies the current gaps in the field. While some of the relevant past studies were referenced, the authors did not place their own study in the context to published work and current models in the field, which reduced the scholarly value of their study. Because the work was not placed in context of the field, some of the rationale and conclusions were misleading.

Some specific major comments:

1,The title is misleading. The authors have clearly shown that when MCM levels are be made limiting in an engineered system, some origins are substantially less active, which means that these origin loci are replicated "passively" (i.e. by a Replication Fork (RF) emanating from a distal origin) rather than actively (i.e. by "firing" and initiating replication). Their own replication data show that. But this competition is only revealed when MCM levels are artificially/experimentally lowered. What is the evidence that competition for MCM complexes among individual origins establishes replication timing patterns in yeast? If anything, the over-expression experiment suggests the opposite--that MCM levels are not limiting and therefore do not play a substantial role in establishing the replication timing patterns that are observed in yeast. Instead those patterns appear to result primarily from the fact that MCM complex activation factors are present in limiting concentrations relative to origins.

2,The abstract states that "the number of MCMs loaded onto origins has been proposed to be a key determinant of when those origins initiate DNA replication during S-phase". While it is true that this lab has proposed this model in budding yeast, the current study performs no experiments that directly address this model--i.e. that i. individual origins possess a different number of MCM complexes and or ii that these differences underlie timing differences. They acknowledge this point in their Discussion--a ChIPSeq experiment is an ensemble experiment--there is no way to know that differences in MCM signals correspond to a different number of MCM complexes per origin versus a differences in the fraction of cells that contain and MCM complex at all at a given origin . But this statement in the abstract, combined with their conclusion in the same section of the paper: "Our results support a model in which the loading activity of origins, controlled by their ability to recruit ORC and compete for MCM, determines the number of helicases loaded, which in turn affects replication timing" implies that they have tested a model that they have not tested. Given how quickly readers "skim" the literature these days, a misleading abstract can do a lot of damage to a field. The results presented in this study neither support nor refute the model for the number of helicases loaded per origin, and the fact that reducing origin licensing efficiency by making the major substrate limiting reduces the number of licensed origins in a cell population is fully expected based on the current state of the field .

3,The rationale for the study as stated in the Introduction: "Although the molecular biochemistry of initiation at individual origins continues to be elucidated in great detail (Bleichert, 2019), the mechanism governing the time at which different regions of the genome replicate has remained largely elusive (Boos and Ferreira, 2019)." Is also misleading. In fact, in budding yeast (and other organisms) there have been several advances in this area particularly with respect to DNA replication origin activation. The S-phase origin activation factors are limiting for origin function, and factors such as Ctf19 at centromeres and Fkh1/2 at non-centromeric early-acting origins help to directly recruit the limiting S-phase factor, Dbf4, to origins. It is misleading to ignore this substantial progress and not make an effort to place this current study, which is important and one of the first to look directly at MCM loading control in yeast, into a relevant context with respect to what is known. What's interesting is that this S-phase model assumes/requires that most origins are, in fact, licensed and thus that differences in licensing efficiency are not a major driving of replication timing patterns in yeast. But we do not know why there are only subtle differences in MCM loading---this study may help explain that.

4,The authors link the differential ability of MCM loading deficiencies when MCM is made limiting to differences in ORC binding categories. The "weak" origins, that presumably bind ORC weakly, were most affected by reductions in MCM. Are these origins less efficient than the other categories, DNA and chromatin-dependent (using the origin efficiency metric data from the Whitehouse lab) where MCM binding is not reduced as much? In normal cells are these early or late origins? Is the idea that the role of excess MCM is to achieve a sufficient number or "back up" origins per cell to deal with potential stress, as proposed by the Blow and Schwob labs in tissue culture cells many years ago? It seems likely that the data reported here are in fact confirmations of those early studies in mammalian cells---which is useful to know even if not unexpected.

5,Aren't the results that losing MCM signal corresponds to loss of origin activity peaks entirely expected? The same result would be obtained if you made a point mutation in that origin's ACS. Of course preventing an origin from being licensed will delay that region's replication time in S-phase because it now must be replicated passively. Licensing affects replication timing patterns because the MCM complex is the substrate for limiting S-phase factors, but that is far different from concluding that the number of MCMs at an origin is what controls the time in S-phase when an origin is activated.

6,The authors stated that the measured MCM abundance for the 43% of origins that are not known to be controlled by the multiple mechanisms that have been shown to control origin replication time. Is this because they think that MCM loading contributes to the timing control of only these origins? Was MCM loading not affected at any of these other origins when MCM levels were reduced? Are those 43% of origins in the "weak"binding category in terms of ORC? The rationale for eliminating so many origins from these analyses were not clear.

7,Doesn't the data in Figure 4c at 0 mM auxin support the conclusion that differences in MCM ChIPsignals have negligible effects on origin activation time, in contrast to the publication by Das, 2015 from this lab? Or is the point that these origins are sensitive to reductions in MCM levels and the more sensitive they are the more delayed their replication time (but again, doesn't that have to be true? If they are losing MCM signals they cannot function as origins, so they are replicated passively and, by definition, will show delayed replication timing. An origin is defined as such by a loaded MCM complex.)

8,I do not understand the conclusions from Figure 4d. There is an extremely small positive correlation between how much of an MCM signal is lost and delay in replication time of an origin, but this correlation is not surprising as an unlicensed origin cannot be an origin and will be replicated passively. What seems most surprising about these data is that the effect is so weak, not that it exists. There is quite a lot of scatter in this plot at 500 uM auxin, with some origins losing a given amount of signal (x) and being only slightly delayed in replication time, and others losing the same amount of signal (x) and being substantially delayed. What underlies this outcome?--Are the ones that are not substantially delayed closer to origins that have not been affected at all by MCM reductions? Why is the correlation so weak? The other regulators of origin activation time have stronger and more precise effects--for example the centromere-control can be precisely eliminated so that only the replication time of the centromere-proximal origins are delayed.

9,Multiple studies in yeast and mammalian cells indicate that MCM subunits are in excess relative to other licensing and S-phase initiation factors, so it is not unexpected that over-expressing MCM did not lead to enhanced levels of licensing. It seems much more plausible that Cdc6 or Cdt1 or both factors are present in limiting amounts for MCM loading, so I did not understand the point of over-producing MCM subunits. If the "weak" origins are the ones that are most dramatically affected by reducing MCM to "limiting" levels, isn't the question whether you can increase licensing at these origins when you over-produce a factor that is likely limiting for licensing, such as Cdt1 or Cdc6 (or both) while leaving MCM at its normal levels. The fact that MCM levels are not limiting for licensing is not surprising and, if anything, argues against these levels having a regulatory role in origin activation timing---which seems to be the opposite of what the authors want to conclude.

In summary, I think the technical aspects of the experiments were quite strong, but I do not think that the experiments answered the question that was posed by the authors.

Minor points:

Many places where "This data" should be changed to "These data". Data are plural.

Significance

Significance: see above

Referees Cross Commenting

Reviewer 3. My overall conclusions about this study are that the data are extremely nice and useful to the field, but that their potential to advance the field or clarify it for 'outsiders' are limited by 1, a biased. model-centric presentation that fails to put the work in context of a lot of strong previous work. Some of the conclusions cannot event be tested by the experimental design 2, some of the data analyses, for example the parsing of origins for analyses of MCM effects versus effects on replication time seem arbitrary and were not clearly justified. 3, The correlation between reductions in MCM loading and Trep delay seemed weak, even after parsing for origins expected to experience the largest effects, which is actually kind of interesting, but was ignored in favor of the pre-determined interpretation.

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Reply to the reviewers

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*Reviewer #1 (Evidence, reproducibility and clarity (Required)):

The manuscript by Abrams and Nance describes how the polarity proteins PAR-6 and PKC-3/aPKC promote lumen extension of the unicellular excretory canal in C. elegans. Using tissue-specific depletion methods they find that CDC-42 and the RhoGEF EXC-5/FGD are required for luminal localization of PAR-6, which recruits the exocyst complex required for lumen extension. Interestingly, they show that the ortholog of the mammalian exocyst receptor, PAR-3, is dispensable for luminal membrane extension. Overall, this is a well-written and interesting manuscript.*

1.Because depletion of PAR-3 in the canal causes milder defects than PAR-6 or CDC-42 the authors suggest that they cannot rule out the possibility that an alternative isoform of PAR-3 is expressed and buffering the defect. They should perform canal-specific RNAi-mediated depletion of the entire PAR-3 gene to determine if this is true.

We agree with Reviewer 1 that it would be useful to provide additional evidence that an alternative isoform of PAR-3 lacking the ZF1 degron is not expressed. While tissue-specific RNAi could be used, we have not been successful obtaining complete knockdown in previous tissue-specific RNAi experiments. Moreover, this approach does not target any maternal PAR-3 protein that may be inherited by the excretory cell. As an alternative approach to address this point, we will analyze par-3::zf1::yfp/par-3(null) worms following excretory-cell-specific expression of zif-1, and compare to par-3::zf1::yfp/par-3::zf1::yfp siblings. We would expect the excretory cell phenotype to become more severe if additional, ‘phenotype-buffering’ forms of PAR-3 were present, or if there was incomplete degradation of PAR-3::ZF1::YFP in our previous experiments.

2.The authors suggest that GTP-loaded (activated) CDC-42 recruits PAR-6 to the luminal membrane. It would be nice if they could use a biosensor, such as the GBD-WSP-1 reagent from Buechner's lab to confirm that EXC-5 depletion also reduces activated CDC-42, as would be expected. This should be achievable since there is strong CDC-42 signal, even in the cytoplasm.

This is an excellent suggestion. We will utilize a CDC-42 biosensor – an integrated cdc42p::gfp::wsp-1(gbd) strain created in our lab and previously validated and characterized (Zilberman et al. 2017). We have confirmed that the biosensor is detected in the excretory canal and appears enriched at or near the lumenal membrane. We will cross the biosensor into the exc-5::zf1::mScarlet background. This will allow us to assess lumenal enrichment, and using heat shock inducible ZIF-1, determine if there is a reduction in biosensor lumenal enrichment when EXC-5::ZF1::mScarlet is acutely degraded.

If the biosensor is difficult to measure at the canal lumen, an alternative approach would be to use an available exc-5 null allele to examine genetically if cdc-42 and exc-5 are acting in the same pathway. We could cross CDC-42exc(-) larvae into exc-5(rh232) and quantify excretory canal phenotypes. If CDC-42 and EXC-5 are indeed functioning in the same pathway we would expect no enhancement of the CDC-42exc(-) phenotype.

3.Related to point 2, (i) does mutation of the CRIB domain of PAR-6 impair its recruitment to the luminal membrane, and (ii) does this mutant exacerbate canal defects when PAR-3 is depleted?

(i) Our lab has previously generated and characterized a transgenic par6P::par-6(**CRIB)::gfp strain (Zilberman et al., 2017). We will examine this strain to determine if expression is detectable in the excretory canal, and if so, we will compare lumenal enrichment of PAR-6(CRIB)::GFP to control worms expressing wild-type PAR-6::GFP.

(ii) This is a very interesting experiment, as it would help address if the mild phenotype observed in PAR-3 depleted animals is due to the remaining PAR-6 that is recruited by CDC-42. Our lab has previously shown that par6P::par-6(**CRIB)::gfp cannot rescue the embryonic lethality of a par-6 mutant, in contrast to par-6::gfp (Zilberman et al. 2017). This indicates that the CRIB domain is needed for PAR-6 function during embryogenesis and suggests that CRIB domain mutations introduced by CRISPR would almost certainly be lethal, precluding analysis of the excretory cell.

As an alternative experiment, we would determine if PAR-3 localizes to the lumenal membrane independently of CDC-42; such a finding would imply that PAR-3 and CDC-42 likely have independent contributions to PAR-6 localization (rather than CDC-42 promoting PAR-6 localization by localizing PAR-3). To do this, we will degrade ZF1::YFP::CDC-42 in the excretory cell and examine the localization of PAR-3::mCherry compared to controls. We have all of the strains needed for this experiment.

4.The authors hypothesize that partial recruitment of PAR-6 by CDC-42 is sufficient for luminal membrane extension to explain the mild defects caused by PAR-3 depletion. Since depletion of PAR-6 and CDC-42 alone causes milder canal truncations the authors should co-deplete these proteins (as well as PAR-3 and CDC-42) to determine if there is an additive effect.

This is an excellent suggestion in principal. However, it is not possible to know in any given degradation experiment whether the targeted protein is completely degraded; we can only say it is no longer detectable by fluorescence. Thus, any degron allele (in the presence of ZIF-1) could behave like a strong hypomorph rather than a null. It would not be possible to interpret double degradation experiments in such a case, as a more severe phenotype in the double could simply be a result of combining two hypomorphic alleles, further reducing pathway activity even if the genes function together in the same pathway. To interpret this experiment properly, a null allele of at least one of the genes would have to be used. This is not possible since par and cdc-42 null mutants are lethal and there is also maternal contribution. As an alternative to these double depletion experiments, we will deplete PAR-6::ZF1::YFP or PAR-3::ZF1::YFP in exc-5 null mutant larvae, as unlike cdc-42, exc-5 is not an essential gene.

5.In figure 2, the authors show that depletion of PKC-3 causes more severe canal truncations than PAR-6. Since these proteins function in the same complex what do they think is the reason for this difference? This point could be discussed more in the manuscript.

As described in the previous point, incomplete degradation could produce modestly different phenotypes even for genes that act in the same pathway. Therefore, it is not possible to determine whether PAR-6 and PKC-3 have different roles using this approach. We will add text to the discussion bringing up this point.

6.Related to point 5, more experiments with PKC-3 should be done to determine if, for example, localization of SEC-10 is similarly affected as ablation of PAR-3, PAR-6 and CDC-42.

We agree, and will address this point by acutely degrading ZF1::GFP::PKC-3 and examining transgenic SEC-10::mCherry, as we have done for other par genes.

Reviewer #2 (Evidence, reproducibility and clarity (Required)): The manuscript by Abrams & Nance describes a precise investigation of the role of PAR proteins in the recruitment of the exocyst during and after the extension of the C. elegans excretory canal. State-of-the-art genetic techniques are used to acutely deplete proteins only in the targeted cell, and examine the localization of endogenously expressed markers. Experiments are well described and carefully quantified, with systematic statistical analysis. The manuscript is easy to follow and the bibliography is very good. Most conclusions are well supported.

1) I am not entirely convinced by the presence of CDC-42 at the lumenal membrane (Fig3G); it seems to be more sub-lumenal that really lumenal. It peaks well before PAR-6 (Fig3H) which itself seem slightly less apical that PAR-3 (Fig3F). Could you use super-resolution microscopy (compatible with endogenous expression levels) to more precisely localize CDC-42? Similar point for PAR-3 and PAR-6 which do not seem to colocalize completely - a longitudinal line scan along the lumenal membrane might provide the answer even without super-resolution; this could help explain why these two proteins do not have the same function. These suggestions are easy to do provided the authors can have access to super-resolution (Airyscan to name it; although other methods will be perfectly acceptable I believe it is the most simple one).

We agree that the CDC-42 localization peak does not precisely match the PAR-6 peak. As the reviewer notes, resolving the subcellular localization of these two proteins will not be feasible using standard confocal microscopy. We will image the ZF1::YFP::CDC-42; PAR-6:mKate strain using a Zeiss LSM 880 with Airyscan to determine if their subcellular localization patterns are distinct.

To examine PAR-3 and PAR-6 colocalization at the lumen, we will acquire additional confocal images of the PAR-6-ZF1-YFP; PAR-3-mCherry strain and examine colocalization of the clusters along the lumenal membrane. As a positive control for two proteins that should co-localize, we will image ZF1::GFP::PKC-3; PAR-6-mKate; these two proteins bind directly and co-localize in nearly all cells in which they have been examined.

2) The same group has described a CDC-42 biosensor to detect its active form. It could be used here to precisely pinpoint where active CDC-42 is required: in the cytoplasm? At the lumenal membrane? colocalizing with what other protein? This will require the expression of a transgene under an excretory cell specific promotor and a simple injection strategy while helping to strengthen the description of the CDC-42 role.

See Reviewer 1 point #2.

3) As the authors certainly know, there is a PAR-6 mutation which prevents its binding to CDC-42. They could express this construct in the excretory canal a simple extrachromosomal array should be sufficient) to validate the direct interaction between these proteins in this cell.

See Reviewer 1 point #3.

4) What is the lethality of ZIF-1-mediated depletion of the various factors under the exc promoter? Can homozygous strains be maintained? Authors just have to add a sentence in the Mat&Met section.

All of the strains with excretory cell-specific degradation we have examined are viable when grown on NGM plates. We will add this point to the materials and methods.

Provided that the authors have access to an Airyscan, all the questions asked here can be answered in two months (one month for constructs, one month for injection and data analysis) at a very minor cost.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

Strengths of this manuscript include the use of endogenously tagged proteins (rather than over-expressed transgenes) for high resolution imaging and a cell-type specific acute depletion strategy that avoids complicating pleiotropies and allows tests of molecular epistasis. While some results were fairly expected based on prior studies of Cdc42, PAR proteins, and the exocyst in other tissues or systems, differences in the requirements for par-6 and pkc-3 vs. par-3 strongly suggest that the former genes play more important roles in exocyst recruitment. I was also excited to see a connection made between EXC-5 and PKC-3 localization.

1.Lumen formation vs. lumen extension. The abstract and introduction use these two terms almost interchangeably, but they are not the same and more care should be taken to avoid the former term. The data here do not demonstrate any roles for par or other genes in lumen formation, but do demonstrate roles in lumen extension and organization/shaping.

We agree and will correct wording to indicate that lumen extension is affected.

2.Related to the above, mutant phenotypes here are surprisingly mild and variable. The authors discuss possible reasons for the particularly mild phenotype of par-3 mutants, but don't specifically address the mild phenotypes of the others. Clearly quite a bit of polarization and apical membrane addition occurs in ALL of the mutants. Is this because those early steps use other/redundant molecular players, or is depletion too late or incomplete to reveal an early role?

We agree with Reviewer 3 and will bring up these points in the discussion. Degradation of proteins strongly predicted to function together (RAL-1 and SEC-5; PAR-6 and PKC-3) produce similar although not identical phenotypes; as discussed above we consider it likely that these differences reflect minor differences in degradation efficiency below our ability to detect by fluorescence. As Reviewer 3 points out, the excretory-specific driver we use to express ZIF-1 may not be active at the very earliest stages of lumen formation, and degradation could take 45 minutes or more after the promoter becomes active (Armenti et al, 2014). Thus, we agree that phenotypes could be more severe if it were possible to completely deplete each tagged protein prior to the onset of lumen formation. However, this caveat does not change the interpretations of our experiments since all proteins are degraded with the same driver. We have avoided mentioning that the phenotypes we observe reflect the ‘null’ phenotype for these reasons. We will emphasize these points in the discussion.

The authors introduce a new reagent, "excP" (the promoter for T28H11.8), which they use to drive canal cell expression of ZIF-1 for their degron experiments. Please provide more information about when in embryogenesis this promoter becomes active, how that compares to when the par genes, sec-5, ral-1 and cdc-42 are first expressed, and what canal length is at that time. It would also be helpful to show the timeframe for degron-based depletion using this reagent (Figure 1C shows only depletion at L4, days later).

Publicly available single cell RNA seq data (https://pubmed.ncbi.nlm.nih.gov/31488706/ and https://cello.shinyapps.io/celegans_explorer/) suggest that canal expression of the endogenous T28H11.8 gene doesn't really ramp up until the 580-650 minute timepoint, which is several hours after par gene canal expression (270-390 minutes) and the initiation of canal lumen formation (bean stage, 400-450 minutes). These data suggest that excP might come on too late to test requirements in lumen formation and early stages of extension. This caveat should be at least mentioned.

See point #2 above. We agree that providing more information on expression from the T28H11.8 promoter would be important for interpreting the severity of phenotypes. We will raise this point in the discussion, and include existing published expression data and a more detailed analysis of the excP::mCherry transgene.

3.There are two major aspects to the mutant phenotypes observed here: short lumens and cystic lumens. A short lumen makes sense intuitively, but the cysts could use a little more explanation. (What are cysts? What is thought to be the basis of their formation?). It is intriguing that cysts in sec-5 vs. ral-1 mutants (Figure 1) and par-6 vs. pkc-3 mutants (Figure 4) seem to have a very different size and overall appearance. Are these consistent differences, and if so, what could be the explanation for them?

This is an interesting point. Since it is not practical to perform time-lapse imaging to watch canal cysts form, we analyzed only L1 and L4 larvae. We believe from our imaging that these are discontinuous regions of the lumen. One explanation for the expansion and dilation of the cystic lumens by L4 stage could be that the canal lumen has been expanded by fluid buildup resulting from a defect in canal function in osmoregulation, but we have not tested this directly. The reviewer also raises an interesting point regarding different appearances of cysts in SEC-5 and RAL-1 depleted larvae compared to PAR-6 and PKC-3. It is possible that these differences arise because SEC-5 and RAL-1 might direct whether vesicles will fuse at all, whereas PAR proteins direct where they will fuse in the cell (i.e. there could be fusion at basal surfaces, or just reduced apical fusion). We will bring up these points in the discussion.

4.The authors did not test if PKC-3, like PAR-6, is required to recruit exocyst to the canal cell apical membrane, but their prior studies in the embryo suggested that it is (Armenti et al 2014). They also did not test if EXC-5 is required to recruit PAR-6 and the exocyst (along with PKC-3), or if CDC-42 is required to recruit PKC-3 (along with PAR-6). There seems to be an assumption that PAR-6 and PKC-3 are regulated and function in a common manner (as is often the case), but that has not been demonstrated here specifically. The basis for this assumption and alternatives to the linear model should be acknowledged.

As discussed above (Reviewer 1 point #6), we will directly test whether PKC-3 is required to recruit SEC-10::mCherry to the lumenal membrane. We agree with Reviewer 3 that we have not shown that PAR-6 and PKC-3 always function similarly, although this is expected based on their similar phenotypes and co-dependent functions in other cells. We will mention this caveat in the discussion.

5.EXC-5 is presumed to act upstream of CDC-42 based on shared phenotypes and the known Rho GEF activity of its mammalian homologs. However, direct evidence for this is currently lacking. In future, the authors might test if depleting EXC-5 affects CDC-42 activation/GTP-loading by using CDC-42 biosensors that have been reported in the literature (e.g. Lazetic et al 2018).

See Reviewer 1 point #2.

\*Minor comments:** Figure 1, Figure 4, Figure S3, Figure S4 Blue color/CFP indicates the apical/luminal membrane or the apical region of the canal cytoplasm, not the actual lumen as the labels suggest. The lumen is a hollow cavity on the opposite side of the plasma membrane from these markers, and it is shown as white in the Figure 1A upper right cartoon.*

Thank you for pointing this out. We will correct the figure labelling.

Figure 2, Figure S2 I'm not confident in the statistical analysis used here (Fisher's Exact test on two bins, 50% canal length), given that four length bins (not two) were defined. I recommend consulting a statistician.

Our rationale for using two bins for the statistical analysis was because control larvae nearly all have a similar canal length (L1 stage: 99% of larvae have canal length that is 51-75% of body length; L4 stage: 98% of larvae have canal length that is 76-100% of body length), making it straightforward to ask if mutants are shorter. We chose not to make more granular phenotypic comparisons, as we cannot rule out that subtle differences in degradation efficiency, rather than differences in biological function, underlie any differences in canal length of the degron mutants. We will consult with a statistician to determine if this is an acceptable way to statistically compare controls and mutants.

p.3 "Born during late embryogenesis..." Actually, the canal cell is born at ~270 minutes after first cleavage, which is in the first half of embryogenesis, not what I would call "late".

We agree and will correct the wording.

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

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Reply to the reviewers

We are grateful to Review Commons for the opportunity to get valuable comments on our manuscript “Trim39 regulates neuronal apoptosis by acting as a SUMO-targeted E3 ubiquitin-ligase for the transcription factor NFATc3”. We would like to acknowledge the very nice and constructive reviews that our manuscript received. We found all of the reviewer comments well founded and we are taking them into careful consideration in preparing the revised version. We are currently performing additional experiments to address the questions raised by the reviewers. We are not yet able to provide a revised version of the manuscript, but you will find below our response to the reviewers and our plan of revision. It is difficult to anticipate exactly how much time we will need to get the requested results and to prepare a complete revised version, as it will depend on whether we can work normally and whether we encounter technical problems. However, it should be possible within a few months.

Reviewer #1

**Summary:**

Desagher and co-workers investigate the regulation of the NFAT family member NFATc3, a transcription factor in neurons with a pro-apoptotic role. They identify TRIM39 as a ubiquitin E3 ligase regulating NFATc3. They demonstrate that TRIM39 can bind and ubiquitinate NFATc3 in vitro and in cells. They identify a critical SUMO interaction motif in TRIM39, that is required for its interaction with NFATc3 and for its ability to ubiquitinate NFATc3. Moreover, mutating sumoylation sites in NFATc3 reduces the interaction with TRIM39 and reduces its ubiquitination. Silencing TRIM39 increases the protein levels of NFATc3 and its transcriptional activity, leading to apoptosis of neurons. TRIM17 modulates the TRIM39-NFATc3 axis. Combined, TRIM39 appears to be a SUMO-targeted ubiquitin ligase (STUbL) for NFATc3 in neurons.

**Major points:**

1.This manuscript containing two stories: the rather exciting story that TRIM39 is a STUbL for NFATc3 (as mentioned in the title) and the second less exciting story: TRIM17 modulates the regulation of NFATc3 by TRIM39. These stories are now mixed in a confusing manner, disrupting the flow of the first story. It would be better to focus the current manuscript on the first story and strengthen it further and develop the second story in a second manuscript.

We understand that the reviewer is more interested in the part of our manuscript related to the characterization of Trim39 as a STUbL due to his/her field of expertise. However, the two other reviewers are also interested in the other parts of our work. Notably the third reviewer would like us to highlight the physiological importance of our findings. Indeed, the main goal of this article is to describe the mechanisms regulating the stability of the transcription factor NFATc3. Trim17 plays a role in this regulation by inhibiting Trim39. It is particularly important for understanding the impact of these mechanisms on neuronal apoptosis as Trim17 is induced in these conditions. As we want to reach a wide audience, we prefer not to focus our manuscript on the identification of a new STUbL. However, we agree with the reviewer that it would be very interesting to strengthen this part of our work and we are grateful for his/her suggestions.

2.Whereas the cellular experiments to indicate that TRIM39 acts as a STUbL are properly carried out, the observed effects are not necessarily direct. Direct evidence that TRIM39 is indeed a STUbL for sumoylated NFATc3 needs to be obtained in vitro, using purified recombinant proteins. Does TRIM39 indeed preferentially ubiquitinate sumoylated NFATc3? Is ubiquitination reduced for non-sumoylated NFATc3? Is ubiquitination of sumoylated NFATc3 dependent on SIM3 of TRIM39? Do other SIMs in TRIM39 contribute?

We agree with the reviewer that additional in vitro experiments using purified recombinant proteins would strengthen the characterization of Trim39 as a STUbL. In order to answer the specific questions of the reviewer, we propose to perform in vitro ubiquitination using different forms of GST-Trim39 (WT/mSIM3/mSIM1&2) following in vitro SUMOylation (or not) of NFATc3 produced by TnT (wheat germ) and purified by immunoprecipitation. Preliminary results using WT Trim39 show that indeed the in vitro ubiquitination of NFATc3 is improved by prior in vitro SUMOylation. We have to confirm these results and to test the SIM mutants of Trim39 in the same conditions.

3.Rule out potential roles for other STUbLs by including control knockdowns of RNF4 and RNF111 and verify the sumoylation of NFATc3 and ubiquitination of wildtype and sumoylation-mutant NFATc3.

Our data show that silencing of Trim39 deeply decreases the ubiquitination level of NFATc3 in Neuro2A cells, indicating that Trim39 plays a major role in this process. We agree that this does not exclude the possible involvement of other STUbLs in NFATc3 ubiquitination in this model but their potential contribution would be limited. This point will be better addressed in the discussion.

4.Figure 6B: use SUMO inhibitor ML-792 to demonstrate that ubiquitination of wildtype NFATc3 by TRIM39 is dependent on sumoylation.

We thank the reviewer for suggesting this experiments that can easily improve the strength of our demonstration. Our preliminary results indeed indicate that in vivo ubiquitination of NFATc3 by Trim39 is strongly decreased following treatment with the SUMO inhibitor ML-792. We have to confirm these results.

**Minor points:**

5.Figure 1A and B: demonstrate by immunoprecipitation and Western that the endogenous counterparts indeed interact.

We are currently setting the conditions to immunoprecipitate endogenous NFATc3 and Trim39 in order to demonstrate that they indeed interact.

6.Figure 1C and 1E: Quantify the PLA results properly and perform statistics.

We will perform these quantification and statistical analysis as requested.

7.Figure 2B: Correct unequal loading of samples.

We agree with the reviewer (as with reviewer #2) that the blots showing the total lysates of this experiment are confusing. As mentioned in the legend, some material has been lost during the TCA precipitation resulting in unequal loading. However, these experiments have been performed a very long time ago and we do not have the protein extracts anymore. We are currently trying to produce efficient shRNA-expressing lentiviruses to reproduce this experiment and provide a better figure.

8.Figure 6B: proper statistics are needed here from at least three independent experiments.

The reviewer is right. Statistics are needed to reinforce the significance of these results. We have quantified three independent experiments and made graphs and statistics that will be presented in the revised version of the manuscript. They better support our conclusion.

Reviewer #1 (Significance (Required)):

Humans have over 600 different ubiquitin E3s. Currently, RNF4 and RNF111 are the only known human SUMO-Targeted Ubiquitin Ligases (STUbLs). Here, the authors present evidence that the ubiquitin E3 ligase TRIM39 is a STUbL for sumoylated NFATc3. Identification of a new STUbL is an exciting finding for the ubiquitin and SUMO field and for the field of ubiquitin-like signal transduction in general, but needs to be strengthened as outlined above. My field of expertise is SUMO and ubiquitin signal transduction.

Reviewer #2

In this manuscript, the authors analyze the effect of TRIM39, a ubiquitin E3 ligase, on NFATc3, a transcription factor that regulates apoptosis in the nervous system. The authors show that TRIM39 can promote the ubiquitination of NFATc3 and regulate its half-life. Furthermore, ubiquitination depends on the SUMOylation state of NFATc3, which suggests that TRIM39 could be a new example of SUMOylation-dependent ubiquitin ligase or STUbL. **In addition, the authors show that TRIM17 interferes with TRIM39 ubiquitination, representing a new regulatory level for NFATc3 degradation. This has consequences on the regulation of apoptosis in cells derived from the nervous system.

The authors show well-controlled, sound results for the most part. The manuscript is well written, and argumentation is convincing. Given the fact that only 2 STUbLs were previously characterized in mammals, the results are relevant and represent an advance in the field. Overall, this is a nice piece of work. Here are some comments.

**Major comments**

-In Fig. 2B, the levels of material loaded are uneven, which difficult the interpretation.

We agree with the reviewer (as with reviewer #1) that the blots showing the total lysates of this experiment are confusing. As mentioned in the legend, some material has been lost during the TCA precipitation, resulting in unequal loading. In the other experiments, we have the same problem or the background is too high. We are currently trying to produce efficient shRNA-expressing lentiviruses to reproduce this experiment and provide a better figure.

However, it seems that the control shRNA also has an effect on NFATc3 ubiquitination, which should not be the case.

It is true that, in the present figure, the ubiquitination signal is decreased in cells transduced with the control shRNA. However, this is likely due to reduced expression of transfected NFATc3 following lentiviral infection, as it can be seen on the western blot of total lysates.

Also, by reducing ubiquitination by TRIM39, shouldn't you expect an increase in the levels of NFATc3, if this ubiquitination was driving degradation? The authors do not specify whether those cells were treated or not with proteasomal inhibitor.

We agree that an increase in the protein level of NFATc3 is expected following silencing of Trim39. However, in the assay presented in Figure 2B, NFATc3 is transfected and the part of overexpressed NFATc3 that is ubiquitinated by endogenous Trim39 is certainly low. Therefore, silencing of Trim39 cannot have a visible impact on the total protein level of NFATc3.

Indeed, cells were treated with proteasome inhibitor. It is mentioned in the legend of Figure 2A. To avoid repeating it in the legend of Figure 2B, we just wrote that, after 24h transfection, cells were treated as in A, with includes MG-132 treatment for 6h.

Same applies in Figure 4B, where no reduction in NFATc3 are seen after including TRIM39 in the reaction (beyond the fact that it looks reduced because the presence of ubiquitinated forms).

In Figure 4B, the reaction of ubiquitination is performed in an acellular medium with purified recombinant proteins. Although NFATc3 is produced by in vitro transcription/translation in wheat germ extract, it is purified by immunoprecipitation before in vitro ubiquitination. Therefore, the reaction does not contain any proteasome and NFATc3 should not be degraded following its ubiquitination by TRIM39.

-After the experiments in vitro shown in Fig. 2C, the authors conclude that the NFATc3 is a direct substrate of TRIM39. I think the authors used the right approach by using bacterially produced GST-TRIM39 for the ubiquitination reaction. However NFATc3 is produced by an in vitro transcription-translation system, which could in principle provide other contaminant proteins to the reaction. Did the authors try to use bacterially produced NFATc3? This might be difficult in the case of big proteins, in which case the authors could add some caution note in the text. Same applies in Figure 4B.

The reviewer is right. It would have been preferable to use NFATc3 produced in bacteria. Indeed, we started with this approach. However, it was very difficult to get NFATc3 expressed in bacteria, and when we succeeded, most of the protein was degraded. We tried different protease inhibitor cocktails and we used a strain of bacteria (BL21-CodonPlus(DE3)-RP) that is mutated on the genes coding for the proteases Lon and OmpT and is further engineered to express tRNAs that are often limiting when expressing mammalian proteins. Unfortunately, this did not improve our production enough.

We agree that, in principle, in vitro transcription-translation (TnT) systems can include contaminant proteins. However, we used wheat germ extract to produce NFATc3 by TnT. Moreover, we immunopurified NFATc3 from the TnT reaction prior to the ubiquitination reaction. The probability that proteins modifying NFATc3 are expressed in plants and are co-purified with NFATc3 is low. Nevertheless, we will discuss this point in the result section of the revised version of the manuscript, when describing results of Figure 2B and 4B.

-In Fig. 6B, higher levels of ubiquitination in the different SUMOylation mutants are shown. Is this effect consistent? How this can be explained?

We are grateful to the reviewer for pointing out this inconsistency in our manuscript. It will be corrected. Indeed, the values indicated in red in Figure 6B are confusing and are certainly not consistent. We calculated them by normalizing the intensity of the ubiquitination signal by the intensity of NFATc3 in total lysates, which seems to have introduced a bias. Variations in NFATc3 levels are probably responsible for the artificially higher levels of ubiquitination for different SUMOylation mutants after normalization. When quantifying three independent experiments, as requested by reviewer #1, we realized that results are much more consistent without normalization. Therefore, in the revised version of manuscript, we will add a graph showing the average and standard deviation of three independent experiments quantified without normalization. We will also replace the experiment currently presented in Figure 6B by another one in which the levels of NFATc3 show lower variations in the total lysates.

In addition, variations in the levels of NFATc3 are shown in the total lysate, despite the use of proteasomal inhibitors. How the author explain this effect?

These variations in NFATc3 levels in the total lysates may be due to differential protein precipitation by TCA. That is why, in more recent experiments, we collected a portion of the homogenous cell suspension before lysis in the guanidinium buffer, to assess the expression level of transfected proteins (as presented in Figures 4A and 7E).

It is true that treatment with proteasome inhibitor should attenuate differences in protein level due to different ubiquitination levels. However, cells are transfected for 24h and then treated with MG-132 for 6h before lysis. Proteasome inhibition cannot compensate for what occurred in the cells during the 24h transfection. It is added essentially to accumulate poly-ubiquitinated forms of NFATc3.

Somehow, this is contradictory with the general message of SUMOylation-dependent ubiquitination.

The reduced levels of SUMOylation mutants in total lysates may appear to be contradictory with SUMOylation-dependent ubiquitination. However, as mentioned above, this could be due to differential protein precipitation by TCA or to different transfection efficiencies. In contrast, the half-life measurement of WT and EallA mutant, that does not rely on initial expression levels, clearly shows a stabilization of the SUMOylation mutant. Moreover, the average of the three ubiquitination experiments is really convincing. Therefore, we believe that the data that will be presented in the revised manuscript will strongly support our hypothesis.

-In Fig. 7E, not clear to me what the big bands above 130 KDa is after the nickel beads. Do they correspond to monoUb NFATc3 or to the unmodified protein that is sticky to the beads? Do the authors have side-by-side gels of the initial lysate next to the nickel beads eluates to show the increase in molecular weight?

The big bands above 130 kD among nickel bead-purified proteins in Figure 7A are unlikely to be unmodified NFATc3 sticking to the beads. Indeed, in the control condition, in which NFATc3 is overexpressed in the absence of His-ubiquitin, these bands are not visible. Therefore, they might be mono-ubiquitinated forms of NFATc3, or degradation products of poly-ubiquitinated NFATc3. We will correct the figure to clarify this point. Unfortunately, we do not have a gel with nickel bead eluates and total lysates side by side for this experiment.

-Quantifications in some pictures (i.e. Figures 5A, 5B, 6B, 7) is shown in red above or below the bands. Not clear whether the quantifications shown correspond to that single experiment or is the average of several experiments. In the first case, the number would not be very valuable. Authors could add quantification graphs with standard deviations or error bars to the experiments if they want to make the point of changes (significant or not) in the levels. Alternatively, indicate in the Figure legends whether the numbers correspond to the average of several experiments.

These quantifications correspond to the representative experiments shown in the different figures. We will clarify this point in the Figure legends of the revised manuscript. We added these quantifications to normalize the amount of co-precipitated proteins by the amount of the precipitated partner (Fig 5A, 5B, 7B, 7C, 7D) which is not always precipitated with the same efficiency in the different conditions. We think that it should help the reader to assess the degree of interaction. We also added quantifications to Figure 7E to normalize the ubiquitination signal by the amount of NFATc3 expressed in the total lysate. However, we did not want to overload the figures by adding too many graphs.

For Figure 6B, where TCA precipitation of total lysates created an inconsistency, we will provide a graph with the average and standard deviation of three independent experiments, as requested by reviewer #1.

-In Fig. 8, the quantification of apoptotic nuclei has been done just based on the morphology after DAPI staining. Could you use an apoptosis marker (i.e. cleaved caspase Abs) to label the apoptotic cells?

We have been using primary cultures of cerebellar granule neurons (CGN) as an in vitro model of neuronal apoptosis for many years. Nuclear condensation, visualized after DAPI staining, is very characteristic in these neurons and allows a reliable assessment of neuronal apoptosis. In a previous study (Desagher et al. JBC 2005), we have shown that the kinetics of apoptosis in CGN is the same whether we measure cytochrome c release, active caspase 3 or nuclear condensation (Fig 1b). We therefore believe that the counting of apoptotic nuclei is sufficient to support our conclusions, notably for transfection experiments in Figure 8A which would require a lot of work to be repeated with active caspase 3 staining. However, if we can produce efficient shRNA-expressing lentiviruses, we will reproduce the experiment presented in Figure 8B and we will perform a western blot using anti-active caspase 3 to confirm our conclusion.

**Minor comments**

-In Figs. 1 and 5, the red channel should be put in black and white, as it is much easier to see the signal. Not relevant to have DAPI alone in B&W (it does not hurt either), as it is well visible in the merge picture. Also, quantification of the PLA positive dots should be shown in Fig. 1.

We thank the reviewer for these suggestions. We will modify the figures and we will quantify the PLA dots in Figure 1 as requested.

-In Fig. 3C, is the difference in TRIM17 expression between empty plasmid and NFATc3 plasmid significant? If so, indicate it in the graph. The same in panels D, E, indicate all significant differences. Same in other Figures.

No, the difference in Trim17 expression is not statistically significant between NFATc3 and empty plasmid although it clearly increases. However, we agree with the reviewer that more significant differences could be shown in the figures, particularly in Figure 3. Nonetheless, we will try not to overload the figures and will restrict ourselves to comparisons that make sense.

-It would be nice to show a scheme on the location of SIMs in TRIM39 in relation to the other feature of the protein.

We are grateful to the reviewer for this suggestion. We will be happy to add a scheme of Trim39 showing its different domains and the location of its SIMs in the revised Figure 7.

-In Fig. 2 legend, "Note that in the presence of ubiquitin the unmodified form of WT GST-Trim39 is lower due to high Trim39 ubiquitination." Please change to "...in the presence of ubiquitin the levels of the unmodified form..."

-In Fig. 7 legend, the phrases "The intensity of the bands ... " are not clear. Please rephrase.

-In Fig. 8 legend, "\** * PWe thank the reviewer for pointing out typographical errors and awkward sentences in our manuscript. Changes will be made as requested.

Reviewer #2 (Significance (Required)):

In this manuscript, the authors analyze the effect of TRIM39, a ubiquitin E3 ligase, on NFATc3, a transcription factor that regulates apoptosis in the nervous system. The authors show that TRIM39 can promote the ubiquitination of NFATc3 and regulate its half-life. Furthermore, ubiquitination depends on the SUMOylation state of NFATc3, which suggests that TRIM39 could be a new example of SUMOylation-dependent ubiquitin ligase or STUbL. In addition, the authors show that TRIM17 interferes with TRIM39 ubiquitination, representing a new regulatory level for NFATc3 degradation. This has consequences on the regulation of apoptosis in cells derived from the nervous system.

The authors show well-controlled, sound results for the most part. The manuscript is well written, and argumentation is convincing. Given the fact that only 2 STUbLs were previously characterized in mammals, the results are relevant and represent an advance in the field. Overall, this is a nice piece of work.

Audience: researchers interested on proteostasis in general and on nervous system regulation

My expertise: postranslational modifications

Reviewer #3

**Summary:**

In this study, Shrivastava et al. elucidated the previously unknown function of TRIM39 in regulating protein stability of NFATc3, the predominant member of the NFAT family of transcription factor in neurons, where it plays a pro-apoptotic role. NFATs have been shown to be regulated by multiple mechanisms, including at the level of protein stability. In this study, the authors identify TRIM39 as the E3 ligase for NFATc3. Interestingly, TRIM39 recognizes the SUMOylated form of NFATc3 and the interaction facilitates its ubiquitylation and subsequent proteasomal degradation. They further showed that binding of TRIM39 to NFATc3 can also be regulated by TRIM17. Like TRIM39, TRIM17 is a ring-finger containing protein previously shown by this group that it binds NFATc3 but the interaction resulted in an up- rather than down-regulation of NFATc3. In this study, they offer insight to the paradox that overexpression of TRIM17 binding to TRIM39 is to inhibit TRIM39-mediated ubiquitylation of NFATc3. Furthermore, they showed activation of NFATc3 transcriptionally activates TRIM17 expression, thus forming a feedback loop between NFATc3 and TRIM17. Hence, an TRIM17-TRIM39-NFATc3 signaling axis for modulating the protein stability for promoting the activity of NFATc3 in regulating apoptosis in the cerebellar granule neurons induced by KCl deprivation is proposed

The key conclusions are convincing. The data in general are of good quality and with many of the key interactions vigorously documented **by conducting reciprocal interaction analysis. For knockdown expeRIMents, two shRNA independent sequences were used. However, some issues remain to be addressed:

**Major comments:**

1.Figure 1D - the authors should demonstrate that the depletion of TRIM39 expression by shRNA in Neuro2A by Western blotting

We agree with the reviewer that it would be better to provide this control. Unfortunately, we have never been able to observe a convincing decrease in the protein level of Trim39, following knockdown, by Western blotting in Neuro2A cells. This is surprising because the decrease is clearly visible by immunofluorescence in Neuro2A cells, and by western blotting in neurons (see Figure 8C). It is possible that Neuro2A cells, but not neurons, express a protein that is non-specifically recognized by our best anti-Trim39 antibody in western blots and that migrates at the same size as Trim39, thus preventing the investigator to detect the depletion of Trim39. We will test additional anti-Trim39 antibodies to address this question.

2.Figure 3 - the author should show overexpression of TRIM39 resulted in reduction of basal level of endogenous NFATc3 due to its effect on protein stability by using CHX or other pulse chase method.

This is an important point and we have performed many experiments using cycloheximide to measure the half-life of NFATc3 in the presence or the absence of overexpressed Trim39. The results were neither consistent nor reproducible. This is certainly due to the fact that the half-life of endogenous NFATc3 is longer than that of overexpressed Trim39 and that cycloheximide inhibits the expression of both proteins. Therefore, we will perform pulse-chase experiments after metabolic labelling of cells with [35S]-Met. We are currently setting up the conditions to immunoprecipitate endogenous NFATc3 to be able to perform these experiments.

3.Figure 3 - Does overexpression or knockdown of TRIM39 has an effect on affecting levels of NFATc3 mRNAs?

The reviewer is right. It is important to control that overexpression and knockdown of Trim39 do not modify the mRNA level of NFATc3. Therefore, we are currently measuring NFATc3 mRNA levels in all the experiments used to make the graphs of Figure 3. These results will be added to the revised version of the manuscript as supplemental data. First results show no significant change of NFATc3 mRNA levels in these experiments.

4.Figure 6A - the authors should confirm the multiple bands that are slower migrating are SUMO form of NFATc9 by demonstrating the presence of SUMO in these forms of NFATc3, or alternatively, perform His-SUMO pull-down and probe for NFATc3.

The reactions shown in Figure 6B have been performed in vitro, with purified recombinant proteins and with NFATc3 produced by in vitro transcription/translation. The wheat germ extract used to produce NFATc3 is unlikely to provide the material needed for post-translation modification of a mammalian protein. However, we agree that it would be better to confirm that slower migrating bands are indeed SUMOylated forms of NFATc3. We may hybridize the membranes with an anti-SUMO antibody but it would give a smear as the enzymes added to the reaction mix are themselves SUMOylated. Therefore, we will show an experiment in which the reaction mix has been incubated with and without SUMO. The results show no slower migrating bands in the absence of SUMO although all conditions were otherwise identical. This will be added to the revised Figure 6.

5.Figure 7C - the quantification for mSIM1 does not seem to agree with the band intensity.

Yes, we agree with the reviewer that the quantification (122%) does not seem to reflect the amount of SUMO-chains bound to GST-Trim39 mSIM1. This is due to the normalization of the SUMO signals by the intensity of GST-Trim39 bands. Indeed, it is difficult to control exactly how much recombinant protein is used. GST-Trim39 mSIM1 was slightly less abundant than the other GST-Trim39 proteins in this experiment, explaining why less SUMO-chains were eluted in this condition. The normalization is mentioned in the legend of Figure 7C.

6.TRIM17 reduces TRIM39/NFATc3 interaction and inhibits TRIM39 E3 activity, which results in stabilization of NFATc3. NFATc3 in turn transcriptionally induces TRIM17 expression, thus forming a feedback loop between NFATc3 and TRIM17. It will be good if the authors can discuss the possibility of the existence of this feedback mechanism in physiological context? Is the protein level of NFATc3 level, which should be low abundance at the resting state, elevated by KCI deprivation? If so, can the authors discuss the possible signalling event(s) that that lead to activation of NFATc3 upon KCI deprivation? For instance, does KCL deprivation cause de-SUMOylation of NFATc3?

We thank the reviewer for these suggestions. Our preliminary results suggest that the protein level of NFATc3 is increased in neurons following KCl deprivation. We are currently performing additional experiments to confirm this result. If proved, this increase may be due to the transcriptional induction of Trim17 that should result in the stabilization of NFATc3 through the inhibition of Trim39. It may also be due to a possible deSUMOylation of NFATc3 following apoptosis induction, as suggested by the reviewer. To address the latter point, we are currently setting up PLA using anti-NFATc3 and anti-SUMO antibodies to assess the SUMOylation level of endogenous NFATc3 in neurons. If they are of good quality, we will add these data to Figure 8 and we will discuss the possible existence of feedback loops in neuronal apoptosis, as suggested by the reviewer.

**Minor comments:**

1.Line 294 - it should be "SUMOylation" instead of "SUMO".

We thank the reviewer for pointing out this typographical error that will be corrected.

2.Figure 8 - to include TRIM39/NFATc3 double knockdown to show the effect on increased neuronal apoptosis in the cells with TRIM39 knocked down was due to elevation of NFATc3 rather than other target(s) of TRIM39.

We agree that it would be interesting to test whether the increase on neuronal apoptosis following Trim39 silencing is mainly due to its effect on NFATc3. We will therefore perform double silencing of Trim39 and NFATc3 in neurons in order to address this point.

3.The discussion may be shortened and revised to highlight the physiological importance of the findings linked to cerebellar granule neurons survival.

As suggested by the reviewer, we will modify the discussion to better highlight the physiological implications of our data, particularly by discussing the results of the additional experiments we will conduct in neurons.

Reviewer #3 (Significance (Required)):

Prior to this study, the mechanism by which protein stability of NFATc3, the pre-dominant member of the NFAT family of transcription factor in neurons, is regulated remains poorly understood. Shrivastava et al. have unravelled the interplay between ubiquitylation and SUMOylation involving TRIM39 and TRIM17 to have an important role in regulating protein stability of NFATc3. The work is interesting and bears significance towards understanding how apoptosis could be finely controlled in cerebellar granule neurons. Furthermore, the study has also expanded the understanding of the role and regulation of the TRIM family of proteins. The senior author is an expert in this field and over the years, her group has contributed many key discoveries on the function of TRIM family of E3 ubiquitin ligases and their critical ubiquitylation substrates in neuronal survival and its relevance to neuronal biology and diseases.

The referee's field of expertise in in the field of mitochondrial apoptosis signalling. The referee extensively involved in studying how protein stability of regulators in apoptosis signalling are regulated by the ubiquitin-proteasome system (UPS) and how does the regulation play a role in physiology and diseases.

Key words: apoptosis, ubiquitylation, cell signaling, liver diseases

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity):

**A. Summary:**

In this modeling study, the authors devised a multicellular model to investigate how circadian clocks in different parts (organs) of plants coordinate their timing. The model uses a plausible mechanism to explain how having a different sensitivity to light leads to different phase and period of circadian clock, which is observed in different plant organs. The model allows for entrainment in Light-Dark (LD) cycles and then a release in always-light (LL) environments. The model disentangles numerous factors that have confounded previous experiments. In one instance, the authors assigned different light sensitivities to the different organs (e.g., root tip, hypocotyl, etc.) which unambiguously show that this one element alone - spatially differing sensitivity to light - is sufficient for recapitulating experimentally observed differences in periods and phases between plant organs. The model also recapitulates the spatial waves of gene expression within and between organs that experimentalists reported. At the sub-tissue level, the model-produced waves have similar patterns as the experimentally observed waves. This confirmation further validates the model. By having the cells share clock mRNA, from any clock component genes, showed the same, experimentally observed spatial dynamics. The main conclusion of the study is that regional differences (e.g., between different organs) in light senilities, when combined with cell-to-cell sharing of clock-gene mRNAs, enables a robust, yet flexible, circadian timing under noisy environmental cycles.

Thank you for your assessment of our work. We plan to make the following revisions based on your feedback.

**B. Specific points:**

1.Lines 125-127: "To simulate the variability observed in single cell clock rhythms, we multiplied the level of each mRNA and protein by a time scaling parameter that was randomly selected from a normal distribution." - Why not add a white (Gaussian) noise term to these equations? How does multiplying by a random variable (for rescaling time) different from my proposal? Some explanation should be given in the text here.

We opted for a time scaling approach as this generates between-cell period differences but avoids within-cell period differences. This is consistent with single cell experiments (S1 Fig; Gould et al., 2018, eLife). We will provide an explanation of this in the text.

2.Does the spatial network model simplify calculations by assuming separations of timescales (e.g., for equilibration in concentrations of mRNAs that diffuse between cells)? If so, it would be good to spell these out in the beginning of the Results section (where the model is described).

We agree that a more detailed discussion of the model assumptions would be beneficial and we will provide this in the text.

3.Lines 161-162: "....in a phase only model by local...." should be "....in a phase model only by local...."

Thank you for your correction.

4.Lines 188-190: The authors observed that qualitatively similar/indistinguishable behaviors arose regardless of which elements are varied (e.g., global versus local cell-cell coupling, setting light input to be equal in all regions of the seedling, etc.). Then they claim here that "...these results show that the assumptions of local cell-to-cell coupling and differential light sensitivity between regions are the key aspects of our model that allow a match to experimental data." - I don't see how this follows from the observation almost any of the variations lead to the same behaviors in this section (spatial waves). Show the reasoning in the text here.

We observed spatial waves with different local coupling regimes (4 v. 8 nearest neighbours). However, we did not observe spatial waves with global coupling (S10 Fig). This led us to conclude that local coupling is a key aspect. In addition, we do not observe waves when setting the light input to be equal in all regions of the seedling (S11 Fig). This confirms that local differences in light sensitivity are also required in our simulations to generate spatial waves. We will clarify these points with revisions to the text.

5.Pgs. 9-10: Section on "Cell-to-cell coupling maintains global coordination under noisy light-dark cycles": The simulation results rigorously support the authors' main conclusion here, which is that local cell-to-cell coupling allows for global coordination under noisy LD cycles. But I'm missing an intuitive explanation (or just any explanation) for why this is. At the end of this section, the authors should provide some intuition or qualitative explanation for the observations that they produced using their model in this section.

We will revise the text to provide an intuitive explanation of these results. The coupling decreases the within-region phase differences. Despite the between-regions phase differences persisting, this effect is sufficient to improve the overall global synchrony.

6.Lines 261-262: Replace the present tenses with past tenses.

Thank you for your correction.

7.Is the main idea that cell-to-cell coupling allows for averaging of fluctuations, between organs or cells within the same organ, while allowing for coordination of the average quantities? Is this responsible for both the flexibility and robustness observed under noisy environmental cycles?

The cell-to-cell-coupling allows for the averaging of fluctuations between cells and the regional flexibility arises from the different light sensitivities in each region. What was interesting to us was that under light-dark cycles the regional flexibility was not lost due to either the noise in the light or the averaging effect of the cell-to-cell coupling. We will revise the text to emphasize these points. Thank you for your prompts.

8.Line 304: Is it really true that the mammalian circadian rhythm is centralized? Don't some parts of our bodies have different circadian clock (e.g., slight differences in phase) than some other parts of our bodies?

There are indeed some small phase differences between parts of our bodies because the mammalian system, like the plant system, is imperfectly coupled. However, the mammalian system is considered more centralized because the suprachiasmatic nucleus in the brain receives the key entraining signal of light and then coordinates rhythms across the body (Bell-Pedersen et al., 2005, Nat Rev Gen; Brown & Azzi, 2013, Circadian Clocks). We will expand on these interesting points by adding a paragraph to the discussion.

Reviewer #1 (Significance):

**Overall assessment:**

I enthusiastically recommend this work for publication after the authors address my comments below (please see "Specific points").

The model's main strength is that the authors could vary each ingredient separately - light sensitivity of each cell/organ, which gene's mRNA diffuses between cells, cellular noise, local versus global cell-cell coupling, etc. Afterwards, the authors could determine which of these variations produces which experimentally observed behaviors. Another strength of the model is that it can reproduce not just one, but numerous, experimentally observed behaviors that are important for understanding circadian clocks in plants. Thus, the model is grounded in experimental truth and produces experimentally observed results. Crucially, since the authors could vary every single element in the model independently of the other elements, the authors are able to provide plausible explanations for why the experiments produced the results that they did (experimentally, a number of confounding factors prevented one from pinpointing to which element produced which observation).

Another strength of the model is also extendable, by other researchers to investigate other plant physiologies in the future (e.g., circadian clock's influence on cell division). The authors highlight these future uses in the discussion section. Therefore, I believe that this work will be valuable to plant biologists, non-plant biologists who are interested in circadian clocks, and systems biologists in general.

The manuscript is also well written and relatively easy to follow, even for non-plant biologists like myself.

Thank you for the positive feedback - we are pleased that you find the manuscript of broad interest to a range of readers.

Comment on Reviewer #2:

I agree with his/her major criticism #3 (ELF4 long-distance movement). I find this to be a reasonable request. Fulfilling it would increase the paper's impact.

Please see our response to reviewer #2.

Comment on Reviewer #3:

The reviewer's point (1) asks for a reasonable request.

Regarding his/her point (2): This is also reasonable. I'd recommend his/her suggestion (a). In the end, I'd be interested to see how the authors respond to this (what function they choose to let adjacent cells be subjected to some correlated light-input intensity. I'd be happy with something simple such as + noise, where is a deterministic term that, for example, decreases exponentially as one moves away from some central cell. Basically, I'd let the authors decide how to implement this and accept their current implementation - no correlation in light-intensity between adjacent cells - as an extreme scenario, as this reviewer points out.

Please see our response to reviewer #3.

Reviewer #2 (Evidence, reproducibility and clarity):

**Summary:**

The manuscript presents an improved model of the circadian clock network that accounts for tissue-specific clock behavior, spatial differences in light sensitivity, and local coupling achieved through intercellular sharing of mRNA. In contrast to whole-plant or "phase-only" models, the authors' approach enables them to address the mechanism behind coupling and how the clock maintains regional synchrony in a noisy environment. Using 34 parameters to describe clock activity and applying the properties mentioned above, the authors demonstrate that their model can recapitulate the spatial waves in circadian gene expression observed and can simulate how the plant maintains local synchrony with regional differences in rhythms under noisy LD cycles. Spatial models that incorporate cell-type-specific sensitivities to environmental inputs and local coupling mechanisms will be most accurate for simulating clock activity under natural environments.

Thank you for your assessment of our work. We plan to make the following revisions based on your feedback.

*We have the following **major criticisms** as follows*

1) When assigning light sensitivities in different regions of the plant, the authors assign a higher sensitivity value to the root tip (L=1.03) than they do to the other part of the root (L=0.90). We are curious why the root tip would have higher light sensitivity than the rest of the root. Is this based on experimental data (if so, please cite in this section or methods)? It seems that these L values were assigned simply to make sure they recapitulated the period differences observed in Fig. 2A. Are these values based on PhyB expression in those organs? Or perhaps based on cell density in those locations?

We assign the light sensitivity to match observed experimental period differences across the plant (Fig 2A,B). This is based on previous experiments demonstrating that experimental period differences are dependent on light input through the light sensing gene PHYB (Greenwood et al., 2019, PLoS Bio; Nimmo et al., 2020, Physiologia Plantarum). For example, in WT seedlings, the root tip oscillates faster than the root, but this difference is lost in the phyb-9 mutant (Greenwood et al., 2019). Thus, we assume the root tip to be more sensitive to light than the roots.

Further supporting this assumption, there is evidence that expression of phytochromes and cryptochromes are increased in the root tip relative to the root (e.g., Somers & Quail, 1995, Plant J; Bognar et al., 1999, PNAS; Toth et al., 2001, Plant Physiol), as the reviewer proposes. However, further experiments would be needed to verify that these differences in expression are what lead to the differences in clock timing. We will add a discussion of these experiments to the text.

2) In the discussion of the test where they set the "light inputs to be equal" in all regions to simulate the phyb-9 mutant, could the authors please clarify whether that means they set the L light sensitivity value equal in all regions?

This is indeed what we mean, we will rephrase the text for clarity.

a. If they are referring to setting the L value equal to all regions, we suggest that this discussion be moved to the section about different light sensitivities instead of the local sharing of mRNA section.

Thank you for your suggestion, we agree and will move this discussion.

b. Additionally, is it possible to set the light sensitivity to zero for all parts of the plant? We think this would be more suitable to simulate the phyb-9 mutant phenotype.

We thank the reviewer for this suggestion. We will include a simulation with light sensitivity set to zero in the revised manuscript, in addition to the existing simulations with light sensitivity set to 1.

3) Based on the recent Chen et al. (2020) paper showing ELF4 long-distance movement, we think it would be of great interest for the authors to model ELF4 protein synthesis/translation as the coupling factor, in addition to the modeling using CCA1/LHY mRNA sharing. We understand you may be saving this analysis for a future modeling paper, but this addition to the paper could increase the impact of this paper.

Thank you for the suggestion to improve our manuscript. We agree it will be of interest to model ELF4 protein as the local coupling factor. In the revision, we will simulate each clock protein (including ELF4) as the local coupling factor and compare.

In addition, we will also modify the coupling mechanism to simulate the long-distance transport of ELF4 proposed by Chen et al., 2020. Our preliminary simulations show that we can couple shoot rhythms to those in the root tip, but that this long range coupling can not on its own generate the spatial structure observed in experiments. We agree with the reviewers that this analysis and an associated discussion will further increase the impact of the paper.

4) This model is able to simulate circadian rhythms under 12:12 LD cycles, which represents two days of the year-the equinoxes. We are curious if the model can simulate rhythms under short days and long days as well. We understand this analysis may be outside the scope of this paper and may require changing the values of the 34 parameters used but think it could be a useful addition here or in future work.

We agree it would be interesting to observe the behavior of the model under different day lengths. We will include simulations under short and long days in the revision.

*And **minor criticisms** as follows*

1) In the first paragraph of the results section, it would be helpful for the authors to reference Table S1 when they mention the 34 parameters used to model oscillator function

We agree and we will implement this helpful suggestion.

2) In the first paragraph of the section titled "Local flexibility persists under idealized and noisy LD cycles", it would be helpful for the authors to reference S12 Fig after the last sentence that starts "However, ELF4/LUX appeared more synchronized..."

We agree and we will implement this helpful suggestion.

3) In the first paragraph of the section titled "Cell-to-cell coupling maintains global communication under noisy light-dark cycles", the authors refer to a "Table 1" but I think they mean to refer to Table S1"

Thank you, we will implement this helpful suggestion.

4) In Fig. 1, panel C is described as demonstrating the cell-to-cell coupling through the "level of CCA1/LHY". This phrasing is vague and we think could be improved to the "mRNA level of CCA1/LHY".

We agree and will implement this helpful suggestion.

Reviewer #2 (Significance (Required)):

This work would be broadly interesting to other researchers studying cell-to-cell signaling and coupling of circadian rhythms in plants and other species where spatial waves of gene expression have been observed (i.e., mice and humans). Additionally, the computational modeling aspect of this work was easily interpretable for someone outside this expertise. Our expertise lies in plant circadian biology.

We thank the reviewer for recognising the broad appeal of our work.

Reviewer #3 (Evidence, reproducibility and clarity):

**Summary:**

The authors start by taking a previously published model of the plant circadian clock and implement five changes: 1) updating the network topology to reflect some recent experimental findings, 2) make a spatial model loosely based on a seedling template 3) introduce coupling between cells based on shared levels of CCA1/LHY 4) randomly rescale time in each cell to induce inter-cell differences in period, 5) include a light sensitivity that depends on the region considered.

For a certain configuration of light sensitivities/intensities, the different periods of oscillations in each seedling region roughly match that of experiments. With a sufficiently high coupling between cells, the system can also generate spatial waves, which are also observed in the experimental system.

With pulsed light inputs the spatial pattern is still produced. The authors then investigate the robustness to environmental noise by generating stochastic light signals and show that the global synchrony, as measured with a synchronisation index, increases with cell-to-cell coupling strength. The paper is overall well-written, and the background and details of the analysis are well presented.

Thank you for your assessment of our work. We plan to make the following revisions based on your feedback.

**Major comments:**

For the first part of paper, the output of the model is certainly the focus. There is virtually no discussion of the inferred parameters and how much confidence the authors have in their values.

Thank you for this point. We will add discussion of the inferred parameters to the initial part of the results.

My main issue with the paper is about the section with noisy light signals, which is included in the title and is ultimately one of the main themes of the article.

Specifically, on line 224:

"This decrease in cell-to-cell variation revealed an underlying spatial structure (Fig 4D, middle and right, and S13 Fig), comparable to that observed under idealized LD cycles (Fig 4B, middle and right, and S12 Fig)."

Firstly, I don't feel these conclusions match with the data presented. Comparing figure 4D middle and right with figure 4B middle and right shows a clear and pronounced loss in spatial structure. In its current form, this statement has to change, but I believe there are at least two other major issues with this figure:

We agree there are some differences in the spatial structure between idealized (Fig 4B) and noisy (Fig 4D) LD cycles. Preliminary simulations suggest that this is due to the way the noisy LD cycles are programmed.

In the current implementation of noisy LD cycles, the maximum intensity of L, L**max, differs between each region, such that relative differences in light sensitivity between regions are maintained. This means that some phase differences between regions are maintained. However, as the reviewer correctly points out in point 1 below, due to the noise fluctuations, the average level of light is lower than under idealized LD cycles, and with considerable day-to-day variation. We believe this is why the spatial structure differs.

Preliminary simulations suggest that if we normalize the mean light intensity such that the mean is equal between the two conditions (as the reviewer suggests in point 1 below), the spatial structure appears similar. We will present this analysis in the revision.

1) The figure is clearly designed to invite a comparison between the noise-free light cycles on the left with the noisy cycles on the right. However, due to how the noisy light is simulated, the variance of light signal increases AND the average intensity of light decreases by 50%. When comparing the left and the right, we therefore don't know whether the changes are due to differences in the average signal or differences from the stochasticity. I think the authors should simulate a noisy light signal with the same mean intensity level as the deterministic signal.

As discussed above, we agree that the average intensity of the light decreases due to the noise, and this complicates interpretation. We will simulate idealized and noisy light cycles with the same mean light level upon revision.

2) The noise model for the light doesn't seem realistic. On line 484 is says:

"We made the simplifying assumption that each cell is exposed to an independent noisy LD cycle due to their unique positions in the environment. LD cycles were input to the molecular model through the parameter L".

In fact, this could be considered as an incredibly complex signal, because for 800 cells it means drawing 800 random light signals. The implication is that two adjacent cells receive statistically independent light signals. Depending on chance, one cell might receive tropical levels of light while its neighbour experiences a cloudy day. This affects the interpretation and conclusions from figures 4 and 5. I propose two different ways of improving the simulation of the noisy light signal:

a) In one extreme case, all cells receive the same noisy light signal, and the other extreme, they all receive independent signals. You could consider a mixture model of light signals, where each cell receives \lambda L_global(t) + (1-\lambda) L_individual(t), where L_global(t) is a global light signal that is shared by all cells and L_individual(t) is a light signal unique to an individual cell. The mixing parameter \lambda controls how similar the light signal is between cells

b) Clearly the light signal will differ depending on the region, but there will be some spatial correlation. You could also consider methods of simulating light such that neighbouring cells receive correlated signals, although this might be difficult.

Thank you for your proposals. We agree that our current implementation of noisy LD cycles represents an extreme scenario. Given that there is no environmental data at sufficient resolution to reliably evaluate which implementation is most realistic, we will explore different approaches based on your suggestions and present them in our revision.

Assuming that the problem with the mean signal is corrected, do you expect the average spatial pattern to be the same between figure 4 B and D with no coupling (J=0) (although an increase in the variance between cells)? Perhaps not (owing to nonlinearities in the system), but it would be interesting to comment.

We agree that the decreased light intensity complicates interpretation of the spatial structure. Although in the current implementation relative light differences between regions are maintained, the spatial structure is altered because the mean intensities are lower. Preliminary simulations with the mean intensity fixed do result in spatial patterns more similar to that seen in Fig 4B, but with increased variance. Comprehensive simulations will be included in the revised manuscript.

The different periods in the different regions of the seedling are caused by differences in light sensitivity, which the authors claim is justified from refs 12-15. An alternative hypothesis is the that biochemical parameters such as degradation rates are different between regions. This is briefly alluded to in the introduction, but I think it would be interesting to discuss further. What would be the pros and cons of the two different mechanisms?

We agree that an alternative hypothesis is that biochemical parameters such as degradation rates may differ between regions. Experimental evidence, however, more supports the light sensitivity hypothesis. This is because, for example, mutations in light signalling remove the spatial differences between regions. We agree though that this is an important point, and will add a paragraph to the discussion discussing the pros and cons of the two different mechanisms.

I understand that the authors used a pre-existing model, but I must say that I find the way that light is incorporated into the model a bit confusing.

On line 345 it says:

"L(t) represents the input light signal (L = 0, lights off; L > 0, lights on) and D(t) denotes a corresponding darkness input signal (D = 1, lights off; D = 0, lights on)."

Surely the only thing that matters biophysically is the number of photons hitting the plant? Could you explain why the model needs to have a separate "darkness signal" compared to just a single light signal?

A darkness signal has been introduced in many circadian clock models because degradation rates of the clock genes can depend upon the light or dark condition. We agree with the reviewer that we should explain this clearer in the text.

In the model, the light intensity changes depending on the region. It might make more sense for interpretability if instead there is an additional light-sensitivity coefficient that depends on the region, because at the moment I'm not sure what units L(t) is supposed to take.

Thank you for your suggestion. We will try to implement this approach.

**Minor comments**

Could you more explicitly describe a possible molecular mechanism through which the coupling acts?

Thank you for your suggestion. We will more explicitly discuss likely transport mechanisms in the text.

In Figure 1C it looks like different genes are coupling to different genes, so you may need to rearrange it.

In our model, the level of CCA1/LHY is shared. Thus, CCA1/LHY from one cell can be considered to repress the expression of other interacting genes in the neighbour cell.

Line 103: "We found that regional differences persist even under LD cycles, but cell to-cell minimized differences between neighbor cells." Missing word.

Thank you for your correction.

Line 124: "The coupling strength was set to 2 (Methods)." This is meaningless in isolation, so it would be better to briefly explain what the coupling parameter is before mentioning its value.

Thank you for your suggestion, we will describe the coupling function in more detail.

Through the text, I think De Caluwe should be corrected to De Caluwé

Thank you for your correction.

Typo line 493

Thank you for your correction.

Code and data are not made available.

Model code will be made available from our project GitLab page: https://gitlab.com/slcu/teamJL/greenwood_tokuda_etal_2020

Output of analysis of experimental data and simulations will also be made available on the GitLab page.

Reviewer #3 (Significance (Required)):

The authors motivate the paper by highlighting that their proposed model improves on phase-based models in that it describes underlying molecular mechanisms.

From an experimental side, it's interesting that a model is developed and directly compared with measured spatio-temporal waves of gene expression. From a theoretical side, the authors address questions relating to oscillations, multi-scale modelling and noise robustness that also generalise to other systems. I therefore expect that both experimental and theoretical audiences will be interested in the results.

There are many possible additions and modifications that could be made to the model, and so the model and analysis could provide a platform for future research. However, I can't comment on whether there are similar pre-existing models of the plant circadian clock that contain both a molecular description of the circadian clock as well as a spatial scale.

We appreciate the reviewer’s view that the work is interesting to both experimental and theoretical audiences.

Comments on Review #1:

The time is rescaled in each cell, meaning that each cell has a unique period, but the dynamics remain deterministic and hence the peak-to-peak times will be exactly the same for each cell. I imagine this isn't completely consistent with single-cell data (if available), where peak-to-peak times are very likely to be variable due to noisy gene expression. In a future paper it would be interesting to analyse the system using stochastic differential equations.

Please see our response to reviewer #1.

Comments on Review #2:

I agree on the following two points:

1) It would add value to discuss whether the different ranking of light sensitivities by organ matches any available experimental data.

Please see our response to reviewer #2.

2) As the Reviewers point out, there are many possibilities for testing the robustness of the system to light clues, including varying the length of the day. Although outside of the scope of this paper, I wonder if it's possible to find data from a light sensor measuring light intensity across an entire year? Plugging such data into the model and measuring how the amplitude and period changes would be really interesting, in my opinion.

Thank you for your suggestion. We also see this as an interesting future direction.

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Referee #3

Evidence, reproducibility and clarity

Summary:

The authors start by taking a previously published model of the plant circadian clock and implement five changes: 1) updating the network topology to reflect some recent experimental findings, 2) make a spatial model loosely based on a seedling template 3) introduce coupling between cells based on shared levels of CCA1/LHY 4) randomly rescale time in each cell to induce inter-cell differences in period, 5) include a light sensitivity that depends on the region considered.

For a certain configuration of light sensitivities/intensities, the different periods of oscillations in each seedling region roughly match that of experiments. With a sufficiently high coupling between cells, the system can also generate spatial waves, which are also observed in the experimental system.

With pulsed light inputs the spatial pattern is still produced. The authors then investigate the robustness to environmental noise by generating stochastic light signals and show that the global synchrony, as measured with a synchronisation index, increases with cell-to-cell coupling strength. The paper is overall well-written, and the background and details of the analysis are well presented.

Major comments:

For the first part of paper, the output of the model is certainly the focus. There is virtually no discussion of the inferred parameters and how much confidence the authors have in their values.

My main issue with the paper is about the section with noisy light signals, which is included in the title and is ultimately one of the main themes of the article.

Specifically, on line 224:

"This decrease in cell-to-cell variation revealed an underlying spatial structure (Fig 4D, middle and right, and S13 Fig), comparable to that observed under idealized LD cycles (Fig 4B, middle and right, and S12 Fig)."

Firstly, I don't feel these conclusions match with the data presented. Comparing figure 4D middle and right with figure 4B middle and right shows a clear and pronounced loss in spatial structure. In its current form, this statement has to change, but I believe there are at least two other major issues with this figure:

1) The figure is clearly designed to invite a comparison between the noise-free light cycles on the left with the noisy cycles on the right. However, due to how the noisy light is simulated, the variance of light signal increases AND the average intensity of light decreases by 50%. When comparing the left and the right, we therefore don't know whether the changes are due to differences in the average signal or differences from the stochasticity. I think the authors should simulate a noisy light signal with the same mean intensity level as the deterministic signal. . 2) The noise model for the light doesn't seem realistic. On line 484 is says:

"We made the simplifying assumption that each cell is exposed to an independent noisy LD cycle due to their unique positions in the environment. LD cycles were input to the molecular model through the parameter L".

In fact, this could be considered as an incredibly complex signal, because for 800 cells it means drawing 800 random light signals. The implication is that two adjacent cells receive statistically independent light signals. Depending on chance, one cell might receive tropical levels of light while its neighbour experiences a cloudy day. This affects the interpretation and conclusions from figures 4 and 5. I propose two different ways of improving the simulation of the noisy light signal:

a) In one extreme case, all cells receive the same noisy light signal, and the other extreme, they all receive independent signals. You could consider a mixture model of light signals, where each cell receives \lambda L_global(t) + (1-\lambda) L_individual(t), where L_global(t) is a global light signal that is shared by all cells and L_individual(t) is a light signal unique to an individual cell. The mixing parameter \lambda controls how similar the light signal is between cells

b) Clearly the light signal will differ depending on the region, but there will be some spatial correlation. You could also consider methods of simulating light such that neighbouring cells receive correlated signals, although this might be difficult.

Assuming that the problem with the mean signal is corrected, do you expect the average spatial pattern to be the same between figure 4 B and D with no coupling (J=0) (although an increase in the variance between cells)? Perhaps not (owing to nonlinearities in the system), but it would be interesting to comment.

The different periods in the different regions of the seedling are caused by differences in light sensitivity, which the authors claim is justified from refs 12-15. An alternative hypothesis is the that biochemical parameters such as degradation rates are different between regions. This is briefly alluded to in the introduction, but I think it would be interesting to discuss further. What would be the pros and cons of the two different mechanisms?

I understand that the authors used a pre-existing model, but I must say that I find the way that light is incorporated into the model a bit confusing.

On line 345 it says: "L(t) represents the input light signal (L = 0, lights off; L > 0, lights on) and D(t) denotes a corresponding darkness input signal (D = 1, lights off; D = 0, lights on)."

Surely the only thing that matters biophysically is the number of photons hitting the plant? Could you explain why the model needs to have a separate "darkness signal" compared to just a single light signal?

In the model, the light intensity changes depending on the region. It might make more sense for interpretability if instead there is an additional light-sensitivity coefficient that depends on the region, because at the moment I'm not sure what units L(t) is supposed to take.

Minor comments

Could you more explicitly describe a possible molecular mechanism through which the coupling acts?

In Figure 1C it looks like different genes are coupling to different genes, so you may need to rearrange it.

Line 103: "We found that regional differences persist even under LD cycles, but cell to-cell minimized differences between neighbor cells." Missing word.

Line 124: "The coupling strength was set to 2 (Methods)." This is meaningless in isolation, so it would be better to briefly explain what the coupling parameter is before mentioning its value.

Through the text, I think De Caluwe should be corrected to De Caluwé

Typo line 493

Code and data are not made available.

Significance

The authors motivate the paper by highlighting that their proposed model improves on phase-based models in that it describes underlying molecular mechanisms.

From an experimental side, it's interesting that a model is developed and directly compared with measured spatio-temporal waves of gene expression. From a theoretical side, the authors address questions relating to oscillations, multi-scale modelling and noise robustness that also generalise to other systems. I therefore expect that both experimental and theoretical audiences will be interested in the results.

There are many possible additions and modifications that could be made to the model, and so the model and analysis could provide a platform for future research. However, I can't comment on whether there are similar pre-existing models of the plant circadian clock that contain both a molecular description of the circadian clock as well as a spatial scale.

REFEREE'S CROSS-COMMENTING

Comments on Review #1:

The time is rescaled in each cell, meaning that each cell has a unique period, but the dynamics remain deterministic and hence the peak-to-peak times will be exactly the same for each cell. I imagine this isn't completely consistent with single-cell data (if available), where peak-to-peak times are very likely to be variable due to noisy gene expression. In a future paper it would be interesting to analyse the system using stochastic differential equations.

Comments on Review #2:

I agree on the following two points:

1) It would add value to discuss whether the different ranking of light sensitivities by organ matches any available experimental data.

2) As the Reviewers point out, there are many possibilities for testing the robustness of the system to light clues, including varying the length of the day. Although outside of the scope of this paper, I wonder if it's possible to find data from a light sensor measuring light intensity across an entire year? Plugging such data into the model and measuring how the amplitude and period changes would be really interesting, in my opinion.

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Referee #2

Evidence, reproducibility and clarity

Summary:

The manuscript presents an improved model of the circadian clock network that accounts for tissue-specific clock behavior, spatial differences in light sensitivity, and local coupling achieved through intercellular sharing of mRNA. In contrast to whole-plant or "phase-only" models, the authors' approach enables them to address the mechanism behind coupling and how the clock maintains regional synchrony in a noisy environment. Using 34 parameters to describe clock activity and applying the properties mentioned above, the authors demonstrate that their model can recapitulate the spatial waves in circadian gene expression observed and can simulate how the plant maintains local synchrony with regional differences in rhythms under noisy LD cycles. Spatial models that incorporate cell-type-specific sensitivities to environmental inputs and local coupling mechanisms will be most accurate for simulating clock activity under natural environments.

We have the following major criticisms as follows

1) When assigning light sensitivities in different regions of the plant, the authors assign a higher sensitivity value to the root tip (L=1.03) than they do to the other part of the root (L=0.90). We are curious why the root tip would have higher light sensitivity than the rest of the root. Is this based on experimental data (if so, please cite in this section or methods)? It seems that these L values were assigned simply to make sure they recapitulated the period differences observed in Fig. 2A. Are these values based on PhyB expression in those organs? Or perhaps based on cell density in those locations?

2) In the discussion of the test where they set the "light inputs to be equal" in all regions to simulate the phyb-9 mutant, could the authors please clarify whether that means they set the L light sensitivity value equal in all regions? a. If they are referring to setting the L value equal to all regions, we suggest that this discussion be moved to the section about different light sensitivities instead of the local sharing of mRNA section. b. Additionally, is it possible to set the light sensitivity to zero for all parts of the plant? We think this would be more suitable to simulate the phyb-9 mutant phenotype.

3) Based on the recent Chen et al. (2020) paper showing ELF4 long-distance movement, we think it would be of great interest for the authors to model ELF4 protein synthesis/translation as the coupling factor, in addition to the modeling using CCA1/LHY mRNA sharing. We understand you may be saving this analysis for a future modeling paper, but this addition to the paper could increase the impact of this paper.

4) This model is able to simulate circadian rhythms under 12:12 LD cycles, which represents two days of the year-the equinoxes. We are curious if the model can simulate rhythms under short days and long days as well. We understand this analysis may be outside the scope of this paper and may require changing the values of the 34 parameters used but think it could be a useful addition here or in future work.

And minor criticisms as follows

1) In the first paragraph of the results section, it would be helpful for the authors to reference Table S1 when they mention the 34 parameters used to model oscillator function

2) In the first paragraph of the section titled "Local flexibility persists under idealized and noisy LD cycles", it would be helpful for the authors to reference S12 Fig after the last sentence that starts "However, ELF4/LUX appeared more synchronized..."

3) In the first paragraph of the section titled "Cell-to-cell coupling maintains global communication under noisy light-dark cycles", the authors refer to a "Table 1" but I think they mean to refer to Table S1"

4) In Fig. 1, panel C is described as demonstrating the cell-to-cell coupling through the "level of CCA1/LHY". This phrasing is vague and we think could be improved to the "mRNA level of CCA1/LHY".

Significance

This work would be broadly interesting to other researchers studying cell-to-cell signaling and coupling of circadian rhythms in plants and other species where spatial waves of gene expression have been observed (i.e., mice and humans). Additionally, the computational modeling aspect of this work was easily interpretable for someone outside this expertise. Our expertise lies in plant circadian biology.

Reviewer #2:

Extracting ion channel kinetic models from experimental data is an important and perennial problem. Much work has been done over the years by different groups, with theoretical frameworks and computational algorithms developed for specific combinations of data and experimental paradigms, from single channels to real-time approaches in live neurons. At one extreme of the data spectrum, single channel currents are traditionally analyzed by maximum likelihood fitting of dwell time probability distributions; at the other extreme, macroscopic currents are typically analyzed by fitting the average current and other extracted features, such as activation curves. Robust analysis packages exist (e.g., HJCFIT, QuB), and they have been put to good use in the literature.

Münch et al focus here on several areas that need improvement: dealing with macroscopic recordings containing relatively low numbers of channels (i.e., hundreds to tens of thousands), combining multiple types of data (e.g., electrical and optical signals), incorporating prior information, and selecting models. The main idea is to approach the data with a predictor-corrector type of algorithm, implemented via a Kalman filter that approximates the discrete-state process (a meta-Markov model of the ensemble of active channels in the preparation) with a continuous-state process that can be handled efficiently within a Bayesian estimation framework, which is also used for parameter estimation and model selection.

With this approach, one doesn't fit the macroscopic current against a predicted deterministic curve, but rather infers - point by point - the ensemble state trajectory given the data and a set of parameters, themselves treated as random variables. This approach, which originated in the signal processing literature as the Forward-Backward procedure (and the related Baum-Welch algorithm), has been applied since the early 90s to single channel recordings (e.g., Chung et al, 1990), and later has been extended to macroscopic data, in a breakthrough study by Moffatt (2007). In this respect, the study by Münch et al is not necessarily a conceptual leap forward. However, their work strengthens the existing mathematical formalism of state inference for macroscopic ion channel data, and embeds it very nicely in a rigorous Bayesian estimation framework.

The main results are very convincing: basically, model parameters can be estimated with greater precision - as much as an order of magnitude better - relative to the traditional approach where the macroscopic data are treated as noisy but deterministic (but see my comments below). Estimate uncertainty can be further improved by incorporating prior information on parameters (e.g., diffusion limits), and by including other types of data, such as fluorescence. The manuscript is well written and overall clear, and the mathematical treatment is a rigorous tour-de-force.

There are several issues that should be addressed by the authors, as listed below.

1) I think packaging this study as a single manuscript for a broad-audience is not optimal. First, the subject is very technical and complex, and the target audience is probably small. Second, the study is very nice and ambitious, but I think clarity is a bit impaired by dealing with perhaps too many issues. The state inference and the bayesian model selection are very important but completely different issues that may be better treated separately, perhaps for a more specialized readership where they can be developed in more detail. Tutorial-style computational examples must be provided, along with well commented/documented code. The interested readers should be able to implement the method described here in their own code/program.

2) The authors should clearly discuss the types of data and experimental paradigms that can be optimally handled by this approach, and they must explain when and where it fails or cannot be applied, or becomes inefficient in comparison with other methods. One must be aware that ion channel data are very often subject to noise and artifacts that alter the structure of microscopic fluctuations. Thus, I would guess that the state inference algorithm would work optimally with low noise, stable, patch-clamp recordings (and matching fluorescence recordings) in heterologous expression systems (e.g., HEK293 cells), where the currents are relatively small, and only the channel of interest is expressed (macropatches?). I imagine it would not be effective with large currents that are recorded with low gain, are subject to finite series resistance, limited rise time, restricted bandwidth, colored noise, contaminated by other currents that are (partially) eliminated with the P/n protocol with the side effect of altering the noise structure, power line 50/60 Hz noise, baseline fluctuations, etc. This basically excludes some types of experimental data and experimental paradigms, such as recordings from neurons in brain slices or in vivo, oocytes, etc. Of course, artifacts can affect all estimation algorithms, but approaches based on fitting the predicted average current have the obvious benefit of averaging out some of these artifacts.

The discussion in the manuscript is insufficient in this regard and must be expanded. Furthermore, I would like to see the method tested under non-ideal but commonly occurring conditions, such as limited bandwidth and in the presence of contaminating noise. For example, compare estimates obtained without filtering with estimates obtained with 2, 3 times over-filtering, with and without large measurement noise added (whole cell recordings with low-gain feedback resistors and series resistance compensation are quite noisy), with and without 50/60 Hz interference. How does the algorithm deal with limited bandwidth that distorts the noise spectrum? How are the estimated parameters affected? The reader will have to get a sense of how sensitive this method is to artifacts.

3) A better comparison with alternative parameter estimation approaches is necessary. First of all, explain more clearly what is different from the predictor-corrector formalism originally proposed by Moffatt (2007). The manuscript mentions that it expands on that, but exactly how? If it is only an incremental improvement, a more specialized audience is more appropriate.

Second, the method proposed by Celentano and Hawkes, 2004, is not a predictor-corrector type but it utilizes the full covariance matrix between data values at different time points. It seems to me that the covariance matrix approach uses all the information contained in the macroscopic data and should be on par with the state inference approach. However, this method is only briefly mentioned here and then it's quickly dismissed as "impractical". I am not at all convinced that it's impractical. We all agree that it's a slower computation than, say, fitting exponentials, but so is the Kalman filter. Where do we draw the line of impracticability? Computational speed should be balanced with computational simplicity, estimation accuracy, and parameter and model identifiability. Moreover, that method was published in 2004, and the computational costs reported there should be projected to present day computational power. I am not saying that the authors should code the C&H procedure and run it here, but should at least give it credit and discuss its potential against the KF method.

The only comparison provided in the manuscript is with the "rate equation" approach, by which the authors understand the family of methods that fit the data against a predicted average trajectory. In principle, this comparison is sufficient, but there are some issues with the way it's done.

Table 3 compares different features of their state inference algorithm and the "rate equation fitting", referencing Milescu et al, 2005. However, there seems to be a misunderstanding: the algorithm presented in that paper does in fact predict and use not only the average but also - optionally - the variance of the current, as contributed by stochastic state fluctuations and measurement noise. These quantities are predicted at any point in time as a function of the initial state, which is calculated from the experimental conditions. In contrast, the KF calculates the average and variance at one point in time as a projection of the average and variance at the previous point. However, both methods (can) compare the data value against a predicted probability distribution. The Kalman filter can produce more precise estimates but presumably with the cost of more complex and slower computation, and increased sensitivity to data artifacts.

Fig. 3 is very informative in this sense, showing that estimates obtained with the state inference (KF) algorithm are about 10 times more precise that those obtained with the "rate equation" approach. However, for this test, the "rate equation" method was allowed to use only the average, not the variance.

Considering this, the comparison made in Fig 3 should be redone against a "rate equation" method that utilizes not only the expected average but also the expected variance to fit the data, as in Milescu et al, 2005. Calculating this variance is trivial and the authors should be able to implement it easily (and I'll be happy to provide feedback). The comparison should include calculation times, as well as convergence.

4) As shown in Milescu et al, 2005, fitting macroscopic currents is asymptotically unbiased. In other words, the estimates are accurate, unless the number of channels is small (tens or hundreds), in which case the multinomial distribution is not very well approximated by a Gaussian. What about the predictor-corrector method? How accurate are the estimates, particularly at low channel counts (10 or 100)? Since the Kalman filter also uses a Gaussian to approximate the multinomial distribution of state fluctuations, I would also expect asymptotic accuracy. Parameter accuracy should be tested, not just precision.

5) The manuscript nicely points out that a "rate equation" approach would need 10 times more channels (N) to attain the same parameter precision as with the Kalman filter, when the number of channels is in the approximate range of 10^2 ... 10^4. With larger N, the two methods become comparable in this respect.

This is very important, because it means that estimate precision increases with N, regardless of the method, which also means that one should try to optimize the experimental approach to maximize the number of channels in the preparation. However, I would like to point out that one could simply repeat the recording protocol 10 times (in the same cell or across cells) to accumulate 10 times more channels, and then use a "rate equation" algorithm to obtain estimates that are just as good. Presumably, the "rate equation" calculation is significantly faster than the Kalman filter (particularly when one fits "features", such as activation curves), and repeating a recording may only add seconds or minutes of experiment time, compared to a comprehensive data analysis that likely involves hours and perhaps days. Although obvious, this point can be easily missed by the casual reader and so it would be useful to be mentioned in the manuscript.

6) Another misunderstanding is that a current normalization is mandatory with "rate equation" algorithms. This is really not the case, as shown in Milescu et al, 2005, where it is demonstrated clearly that one can explicitly use channel count and unitary current to predict the observed macroscopic data. Consequently, these quantities can also be estimated, but state variance must be included in the calculation. Without variance, one can only estimate the product i x N, where i is unitary current and N is channel count. This should be clarified in the manuscript: any method that uses variance can be used to estimate i and N, not just the Kalman filter. In fact, the non-stationary noise analysis does exactly that: a model-blind estimation of N and i from non-equilibrium data. Also, one should be realistic here: in some circumstances it is far more efficient to fit data "features", such as the activation curve, in which case the current needs to be normalized.

7) I think it's great that the authors develop a rigorous Bayesian formalism here, but I think it would be a good idea to explain - even briefly - how to implement a (presumably simpler) maximum likelihood version that uses the Kalman filter. This should satisfy those readers who are less interested in the Bayesian approach, and will also be suitable for situations when no prior information is available.

8) The Bayesian formalism is not the only way of incorporating prior knowledge into an estimation algorithm. In fact, it seems to me that the reader would have more practical and pressing problems than guessing what the parameter prior distribution should be, whether uniform or Gaussian or other. More likely one would want to enforce a certain KD, microscopic (i)reversibility, an (in)equality relationship between parameters, a minimum or maximum rate constant value, or complex model properties and behaviors, such as maximum Popen or half-activation voltage. A comprehensive framework for handling these situations via parameter constraints (linear or non-linear) and cost function penalty has been recently published (Salari et al/Navarro et al, 2018). Obviously, the Bayesian approach has merit, but the authors should discuss how it can better handle the types of practical problems presented in those papers, if it is to be considered an advance in the field, or at least a usable alternative.

9) Discuss the practical aspects of optimization. For example, how is convergence established? How many iterations does it take to reach convergence? How long does it take to run? How does it scale with the data length, channel count, and model state count? How long does it take to optimize a large model (e.g., 10 or 20 states)? Provide some comparison with the "rate equation method".

10) Here and there, the manuscript somehow gives the impression that existing algorithms that extract kinetic parameters by fitting the average macroscopic current ("fitting rate equations") are less "correct", or ignorant of the true mathematical description of the data. This is not the case. Published algorithms that I know of clearly state what data they apply to, what their limitations are, and what approximations were made, and thus they are correct within that defined context and are meant to be more effective than alternatives. Some quick editing throughout the manuscript should eliminate this impression.

11) The manuscript refers to the method where the data are fitted against a predicted current as "rate equations". I don't actually understand what that means. The rate equation is something intrinsic to the model, not a feature of any algorithm. An alternative terminology must be found. Perhaps different algorithms could be classified based on what statistical properties are used and how. E.g., average (+variance) predicted from the starting probabilities (Milescu et al, 2005), full covariance (Celentano and Hawkes, 2004), point-by-point predictor-corrector (Moffatt, 2007).

CONTEXTUALIZE:

In an interview with Landscape Architecture Magazine, Jedidiah Purdy discusses two statements in the preface of his book, This Land is Our Land. The first: "Land is perennially the thing we share that holds us apart." Second: "We have made a world that overmasters us." He explains in the interview, "Who people are on the land and how they can use it, what claims they have to it- is, in our history- the original way that people get sorted into different social fates. Do you own? Do you take the profit? Do you labor? Are you tied to the land?...That division is a way of sorting out and ranking interdependence. Together and apart are inseparable there"(LA MAG, July 2020). "It is the great achievement of human beings to build a world in which we have all these powers that we don't naturally have- we're so helpless- and yet that built world tells us how to live in it in a way that actually radically constrains and gives a very damaging form to our inhabiting the kind of larger living world" (LA MAG, July 2020). In this interview Purdy refers to the land as "...what determines circumstance of individuals' socioeconomic conditions; forming and modifying class, labor, economics, and value of the human race. In After Nature, Purdy describes human beings as what determines the formation of landscape according to what is valued and what is ignored. The two relationships described embody the definition of the Anthropocene era, which, according to Purdy in After Nature, is to emphasize what we think is most important in that relationship (between humans and nature)... Because we shape everything, from the upper atmosphere to the deep seas, there is no more nature that stands apart from human beings" (Purdy, 2015).

RELATE: "A brief sampling might note the ill-fated hydrological reengineering of Tenochtitlan, the replacement of community forests by scientifically managed imperial woodlots, the substitution of Cartesian-grid, monocrop planting for native polycultures adapted to local soils and rains, the violent suppression of women's practical healing knowledge by an all-male elite, the new enclosures of landscapes and forests by today's agro-efficiency engineers and would-be "global" conservation organizations acting in the name of nature and the best interests of "humanity" (McAfee, 2016). In the era of the Anthropocene, both scarcity and abundance are caricatured into megaprivelege and megapoverty more than ever before. The impact of land and the reciprocated impact on the land is more obvious and more likely to be either addressed or ignored by the multiplicity of divisions within the human race, globally. Even if the changing landscape is ignored, the dependence human beings have on the land for natural resources, for space, and for inspiration is only increasing. The land, in response, relies on the honorable actions of human beings. The Anthropocene era defines the transition from reciprocity in relationship to toxic codependence.

McAfee, Kathleen. “The Politics of Nature in the Anthropocene” In: “Whose Anthropocene? Revisiting Dipesh Chakrabarty’s ‘Four Theses,’” edited by Robert Emmett and Thomas Lekan, RCC Perspectives: Transformations in Environment and Society 2016, no. 2, 65–72.

Maybe robot rights is the wrong question, or even in the short term dangerous, but it may be heading in the right direction. If robots can do these things, then why don't they get rights...

What about the biosphere, or communities?

Why are we even having this debate about robot rights? If that's the wrong question, then maybe it's still trying to address a serious issue that needs to be addressed sooner rather than later. Cog Sci, computer science, and so on, affect the foundations of what humans can do. Literally speaking we don't have it but as a thought experiment it's valid b/c we have things that are close enough.

As a philosophical issue, if we respond to this as trolling, then the whole thing becomes a flame war rather than thinking about how Cog Sci and so on has helped us think about what it means to be human.

What then does it mean to have human dignity in a situation where we have current technology? Where do things like rights go w/ embeddedness?

Maybe there's some continuous thread from rights of kings to rights of man and beyond — what if we take the fundamental unit to be the community, in which case, then we get different conclusions. Maybe even Burke has something like this — the thing about the isolated individual was the community. Communities can have have special communities this is why you get such things as rights of kings: this is why the king gets special rights. It wasn't just that it was exploiting kings rampaging around with other responsibilities.

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

The authors generated and analyzed a great amount of single-cell RNA FISH data over time on circadian genes (Nr1d1, Cry1, Bmal1), and performed model selection/fitting to explain the observed mRNA distributions. They decomposed the mRNA variability into distinct sources, and showed that intrinsic noise (transcription burst) dominates the variance. Therefore, looking at transcript counts may not be feasible to estimate single-cell circadian phase. However, the study is quite descriptive and ends up being a bit dissatisfying, so if the authors could improve this aspect by perhaps analyzing a mechanism on cell-specific burst size (F5), gene-specific dependence on cell size (beta), or the positive/negative gene-pair correlations (rho), it would help quite a bit in this regard. The model selection/fitting itself was not really sufficient to compensate for this, as it stands .

We thank the reviewer for appreciating the new smFISH data, the analyses performed, and the consequences regarding phase inference from single cell snapshots.

The reviewer suggests “perhaps analyzing a mechanism on cell-specific burst size (F5), gene-specific dependence on cell size (beta), or the positive/negative gene-pair correlations (rho)”, and we have thus added a new Results paragraph (lines 281-316) and two new Supp Figures 13 and 14 to directly address this point.

Specifically, we have added a dynamic, stochastic model of the circadian clock in order to add mechanistic insight into the parameters of the preferred model M4. Concerning \rho, in the initial manuscript we suggested that the correlations of cell-specific burst sizes (described by the parameter \rho) in the preferred model M4 could result from the underlying network topology. To substantiate this claim, we have now added an analysis of a stochastic model of the clock that includes gene-gene interaction amongst the core-clock genes. The core-clock network involves variables (such as protein levels), parameters (such as mRNA/ protein half-lives) and additional genes (such as Clock) that are not directly measurable in our experiments; and thus offering a detailed mechanistic mathematical model for our data is therefore not realistic. We therefore developed a simplified mathematical model for the three measured genes to explore the underlying mechanisms that could control the parameter \rho, as the referee suggests. As a starting point, we used the circadian clock gene network topology for Nr1d1, Cry1 and Bmal1 as modelled in Relógio et al. (Relógio et al., 2011) (see new Supplementary Material). To keep the model close to the inference framework, we used oscillatory functions for the burst frequency while the transcription rate (and hence the burst size) for each gene is affected by the protein levels of the other genes in the network. Using stochastic simulations we show that, for particular configurations of feedback where the negative repression of Nr1d1 by CRY1 is high, the network can generate positive mRNA correlation between Bmal1/Cry1 mRNA and negative correlation between Nr1d1/Cry1mRNA, as observed in our data (Figure 2C). Furthermore, using the same inference framework as for our data on the simulated mRNA distributions, the obtained \rho is positive for Bmal1/Cry1 and negative for Nr1d1/Cry1, which was also found for our data (Figure 3C). Even though the model is clearly a simplified representation of the clock, these simulations give credence to the scenario that the \rho parameter obtained from the data is a signature of the underlying network topology.

While the emphasis of the paper is certainly on parameter inference of the single-cell RNA FISH data, we believe the addition of this dynamic model provides more mechanistic insight into the results of the model fitting and hence significantly more depth to the article.

\*Specific comments:** *

1.It is hard to distinguish the RNA FISH signals (Figure 1A, 2B). It is probably technically challenging as the mRNAs are of low abundance. I think it may help if they adjust the contrast for the cytoplasm stain or just delineate the cell boundaries.

Thank you for pointing this out, and we agree that our rendering of the FISH images was not optimal and have now significantly improved it (see new Figure 1A and 2B). Considering the other reviewers’ comments related to the images, we have now 1) added the cell contours as requested; 2) use red/green for the smFISH signal in the pairs of genes; 3) we have improved the contrast to make it easier to distinguish the RNA FISH signals.

2.In Figure 2C, the authors showed gene-pair correlations with cells of all sizes. Could the authors do a size-dependent extrinsic-noise filtering (Padovan-Merhar, Dev. Cell, 2015; Hansen et al., 2018, Cell Systems) to better dissect the correlations?

We used negative binomial distributions to directly model the number of mRNA in the cells, which is a natural choice given that the raw smFISH are integer counts. The model incorporates cell size dependencies in a unified framework, which predicts the joint distribution of raw counts, which is why we showed raw counts in the main figure. That being said, as the referee suggests, it can be useful for exploratory purposes to see the relationship between the measured genes while regressing out the contribution of cell area, and we have now added this analysis as Supp Figure 9. On line 156-161 we write:

“To also estimate the correlation between genes while accounting for cell area, we regressed out the area for each gene and recalculated the correlation coefficients [37,38]. Since all genes are positively correlated with area (Fig. 2A), this processing shifted the correlations for both pairs of genes. Specifically, the correlation coefficients for the area-filtered mRNA counts decreased but remained positive for Bmal1/Cry1 and became more negative for Nr1d1/Cry1(Supp Figure 9).”

3.For fitting model M3, as the authors pointed out, there are many local minima. Is the fitting score truly sufficient to eliminate the possibility for partial synchrony especially considering that the authors didn't show how effective the Dex treatment was to synchronize the circadian phase?

Thank you for this comment. In fact, we didn't mean to fully eliminate the possibility of imperfect synchronization, but have tried our best to address it both experimentally and with modeling.

Experimentally, in addition to the Dex treatment, we also compared with a condition in which we entrained the cells using temperature cycles, which is a standard in the field to achieve the best synchronization. We obtained a fold change of 2.1, which was in the range of previous studies (Saini, et al, 2012) and was slightly higher than with Dex synchronisation (1.6). Given that the improvement was not high and that it was important for us to study the system under free-running conditions and not in an entrained state (i.e. phase locking, which distorts the free dynamics and noise characteristics of the oscillator), we used the Dex protocol.

Model 3 was used as a computational approach to correct for the individual phases. In addition to the difficult optimisation landscape, the challenge with model M3 also resides in the difficulty of estimating an individual phase for each cell, as the two mRNA counts measured in each cell do not contain sufficient phase information. This could potentially be resolved by either measuring more genes simultaneously, but is, however, beyond the scope of the present manuscript. We have added discussion on this to the text on lines 244-248:

“Thus, it was apparently difficult to use model M3 to correct the individual phase for each cell, likely due to the fact that the two mRNA counts measured in each cell do not contain sufficient phase information, and that the global optimisation problem contains many local minima. This could potentially be improved by measuring more genes simultaneously.”

We have also added a new Results section (lines 305-316) and Supp Figure 14 to show that imperfect synchrony alone cannot explain the correlation structure observed in our data. Indeed, if two genes have a similarly phased oscillation, the expression of the two genes will be positively correlated (as shown in the new Supp Figure 14). Similarly, when the oscillations are in anti-phase, negative correlations will be found. Given that Nr1d1 and Cry1 are closer in phase than Bmal1 and Cry1, one would expect that the correlation between Nr1d1 and Cry1 (once accounting for area) would be more positive than for Bmal1 and Cry1, which was not found in the data (area-corrected correlations shown in Supp Figure 9). It therefore seems unlikely that the observed correlations could be caused by imperfect synchrony alone. Together with our simulations of the gene network (described above), we therefore argue that gene-gene interactions are a more plausible mechanistic explanation of the correlations observed in our measured bivariate mRNA distributions.

4.Regarding model M4, the authors added a cell-specific noise term without specifying the contributing factors. Typically adding degrees of freedom should improve fitting and make it easier for a model to fit, why not in this case? Can the authors provide some explanations/mechanisms.

We believe there has been a misunderstanding regarding model M4. By adding parameters, model M4 is indeed easier to fit. There is even a problem of overfitting whereby the burst frequency becomes unrealistically high and the model effectively fits a Poisson distribution to each individual cell. To avoid this, we lock the burst frequency values to the posterior mean values from model M2. After describing model M4, we write (lines 260-265):

“When all parameters are free, we noticed that the burst frequency can become unrealistically high due to a tendency to overfit to individual cells, and we therefore locked the burst frequency to the posterior mean values from model M2. The PSIS-LOO scores overall favoured model M4 (Fig. 3B), and the predicted joint probability density shows good similarity to the observed data (Fig. 3D) (all time points shown in Supp figure 11).”

Regarding the above comment in the reviewer’s summary on contributing factors of model M4 we added a simple dynamical model that attempts to explain at least one possible mechanism of generating correlations in cell-specific bursting parameters (see above).

5.The authors should include the number (range) of cells analyzed in the figure legends.

We have now added the number of cells used at each time point to the legend of Figure 1D. To respond to Reviewer #2 we have also added details on the number of smFISH replicates used at each time point. The number of cells for each replicate is shown in Supp Figures 2-5.

Reviewer #1 (Significance (Required)):

Overall, we felt conflicted about the manuscript. On one hand, the authors generated and analyzed a great amount of single-cell RNA FISH data over time on circadian genes. On the other hand, the manuscript was a bit dissatisfying/descriptive. If the authors could provide and analyze some sort of mechanisms on cell-specific burst size (F5), gene-specific dependence on cell size (beta), or the positive/negative gene-pair correlations (rho) it should help improve the manuscript.

We thank the review for the suggestion to expand on the mechanistic interpretation, which we have followed. In addition, we would like to emphasise that a similar smFISH analysis of the core circadian oscillator has never been done, and we believe our data represents a significant contribution to the field. Moreover, our quite generic probabilistic inference framework for smFISH using mixture models to describe intrinsic (transcriptional bursting) and extrinsic fluctuations is also novel and the code provided (written using the Stan probabilistic programming language) might find a wide applicability.

Concerning the mechanistic description, as described above, we added a stochastic, dynamic model of gene expression and propose that gene-gene interactions within the core-clock network topology represent a plausible mechanism for generating correlated burst parameters between genes, which are a feature of the preferred model M4 found during inference. We additionally added an explanatory figure to argue that, given the phase relationship between genes, imperfect synchronisation alone cannot explain the observed correlations that we observe between the pairs of genes. Together, this analysis provides more mechanistic insight into the underlying factors controlling the gene-gene relationships in our measured bivariate mRNA distributions.

\*Referees cross-commenting** *

I agree with Reviewer #3 regarding expanding the discussion to include the Shah & Tyagi and Raj et al citations on buffering. However caution should be exercised regarding ref 26 as it is quite controversial and subsequent analyses came to different conclusions (PMID: 30359620 and 30243562). The general consensus is that nuclear buffering of transcript noise (proposed in ref 26) is not a general phenomenon (ref 27 is specific to the calcium response pathway). In fact, the presence and evolution of specific pathways to buffer transcriptional noise, such as protein-protein mechanisms (Shah & Tyagi) or extended half-life proteins (Raj et al. and others), argues that transcript fluctuations are not probably buffered in general.

Following the suggestion of Reviewer #3, we have expanded the Discussion to include the references cited (Shah & Tyagi, Raj and others).

Previous work from our lab is also nuancing the conclusions from references 26 and 27. Specifically, buffering effects are expected to be highly gene-specific (3’UTR), and in fact we have not seen those with our unstable construct during live-cell imaging (Suter et al., 2011; Zoller et al., 2015). We have also added text in order to explicitly state that subsequent papers have nuanced the general claims in references 26 and 27. In the text we write (lines 335-342):

“One explanation for the low intrinsic fluctuation in these studies is that transcriptional fluctuations are filtered by nuclear retention, though other reports suggest that Fano factors (variance/mean, a measure of overdispersion compared to the Poisson distribution) can be even larger in the cytoplasm than in the nucleus [38]. In the cells used here, the strong signature of transcriptional bursting and high intrinsic noise is consistent with live imaging of a Bmal1transcriptional reporter in the same cell line under similar growth conditions, where intrinsic noise was estimated to be 4-times larger than extrinsic noise [23].”.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

\*Summary:** *

The authors study experimentally and computationally the dynamic transcription of circadian clock genes over time in individual cells with single molecule RNA-FISH with the aim to understand how different noise sources contribute to single cell transcription variability and basic functions of circadian clocks. The authors integrate experiments with computational modeling to understand biology.

\*Major comments:** *

This study has some major limitations that need to be addressed to test the model usefulness, to understand noise sources and to gain biological insights into circadian clocks.

We thank this reviewer for the constructive feedback which enabled us to significantly strengthen the revised manuscript.

The limitations are on the experiments, the computational implementation of the modeling and the integration of experiments with models.

Although the experimental datasets contain several hundred cells per time point for multiple time points, only a single replica experiment is presented. From the presented data it is not clear how reproducible these temporal patterns are and if indeed differences between timepoints can be resolved if multiple biological replica experiments have been analyzed. To address this point at least three biological experiments needs to be presented and analyzed for each of the genes. Plotting the SEM on the means in figure 1B is misleading because several hundred cells have been measured which automatically makes the error small. The SEM just describes how well we can determine the mean from a distribution. Instead a mean and std from the biological replicas need to be plotted to show how experimental variability in experiments is resulting in the described expression pattern. This is similar to RNA-seq data or RT-PCR from multiple replica.

We certainly agree that demonstrating reproducibility is important. Note that our smFISH data is from three independent cell culture dishes and microscopy slides, which included independent cell synchronization. This was described in the Methods but we agree that the data presentation was not showing the individual replicas, which we have now added. In Figure 1B, we now show the mean of each replicate for each time point. While the reviewer suggested displaying the mean and standard deviation across replicates, we show all data points at each time point to make it even more transparent. The mRNA distribution of each replicate is also shown in Supp Figures 2-5, together with individual quantification of mean, coefficient of variation and number of cells.

In addition, to further demonstrate the reproducibility of the temporal patterns we have performed an additional independent experiment on four time points. This experiment shows that the oscillatory patterns for Nr1d1 and Cry1are clearly significant and reproducible (new Supp Figure 7). The combination of the replicates shown for the main experiment (Supp Figures 2-5) and the new replicate experiment (Supp Figure 7) shows that the oscillatory temporal patterns for the mean mRNA levels are robust and reproducible, and in fact similar as those found in bulk analyses (Ukai-Tadenuma et al., 2011; Hughes et al., 2009), which is expected.

It is also not clear how good the cell segmentation works and how does cell segmentation influence the analysis. In figure 1A show the segmentation of the cell boundary together with the membrane stain.

Thanks to this and other reviewers’ comments, we have now significantly improved the presentation of the FISH images. We have now 1) added the cell contours as requested; 2) used red/green for the smFISH signal in the pairs of genes; 3) we have improved the contrast to make it easier to distinguish the RNA FISH signals.

We have also added Supp Figure 1 to show that the cell segmentation we used is reliable. In fact, as we had described, we used the sum Z-stack projections of the red channel (Wu et al., 2018), which we found provides the most accurate cell segmentation. We now show in Supp Figure 1 that the obtained segmentation shows convincing agreement with the cell autofluorescence .

The authors use the RNA mean and RNA-FISH distributions and combine this data to build and compare different models. How do you know that the given data fulfils the central limit so that a model describing the mean is an adequate approach? To test this point, the authors should show through subsampling from the data and the model that indeed their data sets have enough cells to fulfil the central limit theorem.

This comment reflects a misunderstanding of our approach, which we now try to better explain. In our inference framework we use a negative binomial (NB) distribution (and mixtures of NBs) to model the full distribution of mRNA counts, and our approach is therefore not based exclusively on the mean of the distribution. The estimation of model parameters and comparison of models is performed using the PSIS-LOO optimisation procedure (see below). The mixture model of NB binomials makes a few assumptions which we had clearly stated. In fact it captures both bursty transcription (in the limit of short bursts as is biologically plausible, which yields the NB distribution), and cell-to-cell variability (extrinsic noise) captured by the mixture. The suitability of the NB to model bursty transcription is established (Raj et al., 2006), and it is parameterized by a mean and a dispersion coefficient, such that the CV of the distribution is the inverse of the burst frequency (Zoller et al., 2015). Therefore the mean is indeed an important parameter of the model, but we do not see the relationship with the CLT. The used probabilistic inference (PSIS-LOO: Pareto-Smoothed Importance Sampling Leave-One-Out, Vehtari et al. 2017, see below) is established and state-of-the-art for selecting models of the appropriate complexity and we are not aware of a similar previous quantitative model for smFISH analysis.

We have now added significantly more explanations both on the general approach as well as the methodological details in a fully-revised Methods section to avoid further misunderstanding.

A strength of the manuscript is that several competing and biologically meaningful models have been generated. However, the manuscript lacks rigor in terms of how fitting and model selection is performed. It is not clear how good the models fit the data. To address this point, the authors should visually compare the model fits to the data and plot their fit errors as a function of model complexity.

We fully agree that comparing different models using a model selection approach is a powerful methodology, in fact it is arguably the most systematic way to approach modeling problems in quantitative biology. Model selection is an active research area and there have been significant developments recently. Here, we used a state-of-the-art and established Bayesian approach (PSIS-LOO: Pareto-Smoothed Importance Sampling Leave-One-Out, Vehtari et al. 2017), which is certainly rigorous and more objective than visual comparison. The PSIS-LOO is conceptually similar to other approaches of model performance such as AIC or WAIC, and the entire field of model selection aims at establishing rigorous methods to assess the tradeoff between fit errors and model complexity. In PSIS-LOO, this is done by using pareto-smoothed importance sampling to estimate the expected log pointwise predictive density for a new dataset using leave-one-out cross-validation. The PSIS-LOO is the currently recommended metric for measuring model performance in Bayesian analysis (Vehtari et al., 2017) and is considered superior to other approaches such as computations of Bayes factors since it is less sensitive to model priors (Gelman et al. 2013). The performance of the models as measured with PSIS-LOO is shown in Figure 3B. As already mentioned, we have added further details as to how the fitting and model selection is performed in a revised Methods section. We agree that visual comparison is useful to gain intuition and this is why we showed the bivariate distributions in Figure 3D and in Supp Figure 11.

Regarding the comment on “fit error”, note also that we probabilistically model the full mRNA distribution for each gene. In each cell, there is a likelihood score that measures the likelihood of observing the measured mRNA count given the modelled probability distribution. As our approach is based on this likelihood, the notion of “fitting error” needs to be replaced by the log likelihood (‘fitting error’ is mathematically equivalent to a log-likelihood when the noise model is Gaussian, which is not the case here).

Another limitation is that the models have not been validated for example by using them to make predictions. One type of prediction could be to fit the model to one biological replica and then predict the other replica (cross validation). Another prediction would be to take the distribution fitted to the experimental data and then compare the model mean to the experimental mean.

Thank you for this comment. As explained above, we used the state-of-the-art PSIS-LOO to measure the predictive performance of the models, which approximates the result of leave-one-out cross-validation using the full data set. To further assess the predictive capabilities of the model, we have now also added a “leave-replicate-out” cross-validation, as the reviewer suggests (new Supp Figure 12). The aim of our “leave-replicate-out” cross-validation was to test how well the predictions of each model generalise to independent cells that are not in the training set. To do this, we trained each model while omitting the data from one gene on a test slide. We then calculated the likelihood score of the test slide using the parameters from the training set, and repeated this for all slides. Similarly to the PSIS-LOO, the results of the leave-replicate-out cross-validation convincingly show that model M4 has the highest predictive performance. This is now described in the updated text on lines 265-271.

The results from fitting and prediction should be plotted as a function of model complexity. This kind of analysis will illustrate how model complexity is supported by the data.

As already mentioned, we used state-of-the-art algorithms to analyze prediction vs. complexity. With the above addition, we now have two methods of calculating the predictive performance of each model: the approximate leave-one-out score as measured with PSIS-LOO and the leave-replicate-out cross-validation. For each model, the PSIS-LOO score is plotted in Figure 3B and the leave-replicate-out cross-validation score is shown in Supp Figure 12.

In the method section on models, a biological motivation must be presented to justify the different model assumption.

Thank you for pointing out that the biological justification of the models needed to be expanded. In addition to the improved justifications already provided in the Results section, we have now updated the Methods section such that a biological motivation is included for each model.

How do the models that fit the distributions describe the mean?

As explained above, the inference is performed on the entire distributions, using a family of distributions (mixtures of NBs) which are parameterized in a biologically relevant manner (transcriptional bursting + extrinsic noise). The mean and variance of the distribution are now described on lines 585-586 in addition to Figure 3A.

It is necessary to list model parameters for each of the models, their description, their parameter values, their parameter uncertainty and units of each parameter.

Thank you, this has now been added as Supplementary Tables 2-5.

It is not clear to me how the joint probability in figures 2,4, S2 and S4 have been used to fit the model.

Again, the joint distributions are modeled using mixtures of NBs and the inference is performed on the entire dataset at once using a log-likelihood approach. This uses all the data at once, and it is embedded in a Bayesian model selection method. The way that the joint probability is used is now clarified in the revised Methods section and in the Results section (lines 208-214):

“For both models M1 and M2, the likelihood of observing the data given the parameters of the model is evaluated using the model-specific NB distribution and the mRNA counts for both genes in each cell. This is performed for both Bmal1/Cry1 and Nr1d1/Cry1 pairs across all time points, and this likelihood is combined with model priors to define the posterior parameter distribution for each model (Methods). We applied Hamiltonian Monte Carlo sampling within the STAN probabilistic programming language to sample the posterior distribution and infer model parameters 40.”

How do the models make sense in the context of the fact that human genes exist as a diploids?

This is a good point, although note though that the 3T3 cells are from mice and not humans. 3T3 cells are tetraploid, and it turns out that under the justified assumption that the bursts are short (Zoller et al., 2015; Suter et al., 2011), the number of alleles rescales the burst frequency, i.e. the effective (observed) burst frequency equals the number of alleles times the burst frequency per allele, but it does not change the shape of the distributions. On line 580-582 we have now written: “Since 3T3 cells are tetraploid, and, again assuming that the bursts are short, the inferred burst frequency for tetraploid cells will be approximately four times that of a single allele.”

The variance decomposition is shortly described but no results are presented to show how this is done. This should be better explained.

The variance decomposition we used is not a new result; in fact, we used the analytical results of Bowsher, C. G. & Swain, P. S. “Identifying sources of variation and the flow of information in biochemical networks” (PNAS, 2012). The mathematical proofs of the formula we use are contained within that reference; however, we have re-written this section to make it clearer to the reader (lines 688-718).

\*Minor comments:** *

In figure 3A, it is not clear to me what these different plots relate to the models. It is also not clear what are equations that describe each model.

The Methods section has now been improved to show the full data-generating mechanism for each model, and each model has its own section title to make it easier to find. We have also improved the legend for Figure 3 to make the relationship to each model clearer.

The legends in figure 3 are not very informative. More details need to be presented to understand this figure.

Thank you for pointing this out, and we have now re-written the figure legend for Figure 3 to make the figure clearer.

Reviewer #2 (Significance (Required)):

This is an interesting and important topic with the potential to have general implication of how to model periodic single cell gene expression data and eventually better understand circadian clocks. This study will expand on other modeling studies of circadian clocks and has the potential to advance the field (PMCID: PMC7229691). I personally have done similar analysis and experiments in another system and biological context which has demonstrated the power of this approach if implemented rigorously. I am not an expert in circadian clocks in human cells.

We thank the reviewer for appreciating the implications for the circadian and single cell gene expression community. Note that to our knowledge, modeling smFISH counts using mixtures of negative binomials combined with Bayesian model selection has not been done. It is both highly relevant biologically (combines intrinsic and extrinsic fluctuations in a rigorous way), general and its applicability extends far beyond the circadian oscillator. Therefore, this approach for quantitative smFISH data analysis also fills an important methodological gap.

\*Referees Cross commenting** *

Reviewer #1:

I agree with the assessment that model fitting and model selection was not sufficient. But I disagreed that the data is enough. Although many cells and time points are analyzed, there is no evidence of how reproducible each mRNA distribution can be measured at each time point. I think reproducibility is key and will also help with the model fitting and identification.

Regarding the point on reproducibility, we have made the following four changes:

1. We have added an independent 4 time-point experiment to show that the oscillatory patterns of the distributions are reproducible (Supp Figure 7).
2. In Figure 1 we now also show the mean of each replicate for the main experiment (Figure 1B).
3. We also show the mRNA distributions of each replicate in Supp Figures 2-5.
4. We have added the “leave-replicate-out” cross-validation to show that that the model performance of the preferred model generalises to independent slides that were not included in training (Supp Figure 12). In responding to Reviewer #1 regarding the modeling, we have now also added a simplified dynamical model of circadian clock expression to add mechanistic insight into our proposed models. Overall, we have significantly expanded the description of the model selection approaches to help readers who are less familiar with Bayesian model selection methods.

Reviewer #3:

Regarding the red background, my understanding is that this comes from the probe hybridization. This is maybe because the probe concentration has not been optimized or the number of probes per gene is low and the signal to noise is not so good.Or it could be auto fluorescent background. In this case a different fluorophore needs to be used to avoid this problem.

Thank you for those comments, and we agree with all reviewers that the presentation of the images needed to be improved. It turned out that in Figure 1, we had shown the cell mask in red so it is clearly not related to probe concentration or autofluorescence. We have now removed the cell mask channel from the main images which allows highlighting better the smFISH signals. All smFISH images for Figures 1 and 2 have been much improved, and we’ve added a new Supp Figure 1 to show the performance of our cell segmentation.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

In this paper Nicholas et al image mRNAs encoding the key controllers of circadian rhythms, Rev-erba, Cry and Bmal1 in single cells over time. It was shown earlier that single cells exhibit circadian rhythms using reporter genes. A large number of studies have shown that transcription is an inherently stochastic process, which raises a question as to how single cells are able to achieve their rhythms on the face of this noise. Their results show that the number of mRNAs for the three genes exhibit the expected periodicity, but this periodicity is associated with significant cell-to-cell variation. They also explore to what extent this variability derives from stochastic transcription vs other sources of variation that are extrinsic to the genes. The results are interesting and experimental and modeling results are important (however this reviewer is not able to judge the veracity of mathematics that underlay the models).

We thank this reviewer for appreciating the importance of our work.

\*Some of the concerns that arose are listed below:** *

1.The images show an annoying red background. If the red is HCS cell mask, it should be removed, and RNA presented on grey scale. This will make a better presentation. The red hue also appears in fig 2 b but here it is one of the RNA. I suggest in Fig 2 one RNA can be presented in green and the other in red, while the nuclei in blue.

Thank you for this comment. We had indeed shown the cell mask in the red channel and now removed it. Together with the other suggestions and comments from the reviewers, we implemented the following changes: 1) added the cell contours as requested; 2) use red/green for the smFISH signal in the pairs of genes; 3) we have improved the contrast to make it easier to distinguish the RNA FISH signals. The presentation of the images is now much improved.

2.This paper and a few others talk about the cell size contributing to the cell-to-cell variability in mRNA numbers. Where does it come from physically? One can imagine based on the cell cycle stage there could be more than two copies of then gene in a cell, which will yield more RNAs, but they say that their cells don't have much cell cycle variability. Perhaps a clearer discussion is called for rather than just being polite to other investigators.

The referee is right that several studies observed empirically that larger cells show more mRNA molecules in smFISH experiments (Padovan et al., 2015; Kempe et al., 2015). In Padovan et al. (2015), the authors found that transcriptional burst size changes with cell volume and burst frequency with cell cycle. The main theory for transcription scaling with cell volume is to maintain transcript concentration. Using cell fusion experiments, they showed that cellular size can directly and globally affect gene expression by modulating transcription. Furthermore, they proposed that the mechanism underlying the global regulation integrates both DNA content and cellular volume to produce the appropriate amount of RNA for a cell of a given size, which is consistent with a model whereby a factor limiting for transcription is sequestered to the DNA. We used these results to propose a model whereby burst size scales with area, and we found an increase in predictive performance (compare M2 with M1 in Figure 3B). While our model selection supported the inclusion of cell area, the variance decomposition showed that the fraction of variance due to cell area ranged from 4.2% for Nr1d1 to 17.6% for Bmal1. We have now expanded the introduction to discuss this in more depth (lines 73-80) as requested.

3.References 26 and 27 are cited for 10-80% of variance due to gene extrinsic sources. These references actually deny that there is a significant transcriptional noise in most genes. Again, stronger discussion is called for.

As mentioned in the reply to Reviewer 1, previous work from our lab is also nuancing the conclusions from references 26 and 27. Specifically, buffering effects are expected to be highly gene-specific (3’UTR), and in fact we have not seen those with our unstable construct during live-cell imaging (Suter et al., 2011; Zoller et al., 2015). We have also added text in order to explicitly state that subsequent papers have nuanced the general claims in references 26 and 27. In the text we write (lines 335-342):

“One explanation for the low intrinsic fluctuation in these studies is that transcriptional fluctuations are filtered by nuclear retention, though other reports suggest that Fano factors (variance/mean, a measure of overdispersion compared to the Poisson distribution) can be even larger in the cytoplasm than in the nucleus [38]. In the cells used here, the strong signature of transcriptional bursting and high intrinsic noise is consistent with live imaging of a Bmal1transcriptional reporter in the same cell line under similar growth conditions, where intrinsic noise was estimated to be 4-times larger than extrinsic noise [23].”.

4.The results raise a very important question, whether and to what extent the transcriptional noise propagates to the next step of gene regulation and are there buffering mechanisms in the cell. For example, Raj et al, Variability in gene expression underlies incomplete penetrance, Nature 2010, show that alternative pathways serve to buffer the impact of gene expression noise. Similarly, Shah and Tyagi, Barriers to transmission of transcriptional noise in a c-fos c-jun pathway, Mol Syst Biol, 2013, show that variability in mRNA is buffered at protein level and the level of protein-protein complexes. Furthermore, they show that to the extent those vary, the chromatin intrinsically buffers against the fluctuations in numbers of transcription factors. Mention of these and other studies will enrich the paper.

We have modified the Discussion section and now discuss these papers (and a few more). We thank the reviewer for the suggestions, which will help the reader to have a broader overview of noise buffering in gene expression and indeed enrich the paper.

Reviewer #3 (Significance (Required)):

Significance is high. Quality is high.

\*Referees Cross-Commenting** *

I agree with the comments made by other reviewers particularly about references 26 and 27. The major conclusions of reference 26 were questioned by Hansen et al 2018. At the bottom of page 7 the authors are qualifying their results in the light of references 26 and 27. Perhaps now there is less of a need to do so.

As mentioned above, we have added the following sentence citing the Hansen paper to make it clear to the reader that key conclusions of the references 26 and 27 are disputed (lines 335-342):

“One explanation for the low intrinsic fluctuation in these studies is that transcriptional fluctuations are filtered by nuclear retention, though other reports suggest that Fano factors (variance/mean, a measure of overdispersion compared to the Poisson distribution) can be even larger in the cytoplasm than in the nucleus [38].

References

Gelman A, Carlin JB, Stern HS, Dunson DB, Vehtari A, Rubin DB. 2013. Bayesian Data Analysis, 3rd edn. CRC Press, London.

Hughes ME, DiTacchio L, Hayes KR, Vollmers C, Pulivarthy S, Baggs JE, Panda S, Hogenesch JB. 2009. Harmonics of circadian gene transcription in mammals. PLoS Genet 5. doi:10.1371/journal.pgen.1000442

Kempe H, Schwabe A, Cremazy F, Verschure PJ, Bruggeman FJ. 2015. The volumes and transcript counts of single cells reveal concentration homeostasis and capture biological noise. Mol Biol Cell 26:797–804. doi:10.1091/mbc.E14-08-1296

Padovan-Merhar O, Nair GP, Biaesch AG, Mayer A, Scarfone S, Foley SW, Wu AR, Churchman LS, Singh A, Raj A. 2015. Single Mammalian Cells Compensate for Differences in Cellular Volume and DNA Copy Number through Independent Global Transcriptional Mechanisms. Mol Cell 58:339–352. doi:10.1016/j.molcel.2015.03.005

Raj A, Peskin CS, Tranchina D, Vargas DY, Tyagi S. 2006. Stochastic mRNA synthesis in mammalian cells. PLoS Biol4:e309. doi:10.1371/journal.pbio.0040309

Relógio A, Westermark PO, Wallach T, Schellenberg K, Kramer A, Herzel H. 2011. Tuning the mammalian circadian clock: Robust synergy of two loops. PLoS Comput Biol 7:1–18. doi:10.1371/journal.pcbi.1002309

Saini C, Morf J, Stratmann M, Gos P, Schibler U. 2012. Simulated body temperature rhythms reveal the phase-shifting behavior and plasticity of mammalian circadian oscillators. Genes Dev 26:567–580. doi:10.1101/gad.183251.111

Suter DM, Molina N, Gatfield D, Schneider K, Schibler U, Naef F. 2011. Mammalian Genes Are Transcribed with Widely Different Bursting Kinetics. Science (80- ) 332:472–474. doi:10.1126/science.1198817

Ukai-Tadenuma M, Yamada RG, Xu H, Ripperger JA, Liu AC, Ueda HR. 2011. Delay in feedback repression by cryptochrome 1 Is required for circadian clock function. Cell 144:268–281. doi:10.1016/j.cell.2010.12.019

Vehtari A, Gelman A, Gabry J. 2017. Practical Bayesian model evaluation using leave-one-out cross-validation and WAIC. Stat Comput 27:1413–1432. doi:10.1007/s11222-016-9696-4

Wu C, Simonetti M, Rossell C, Mignardi M, Mirzazadeh R, Annaratone L, Marchiò C, Sapino A, Bienko M, Crosetto N, Nilsson M. 2018. RollFISH achieves robust quantification of single-molecule RNA biomarkers in paraffin-embedded tumor tissue samples. Commun Biol 1:1–8. doi:10.1038/s42003-018-0218-0

Zoller B, Nicolas D, Molina N, Naef F. 2015. Structure of silent transcription intervals and noise characteristics of mammalian genes. Mol Syst Biol 11:823. doi:10.15252/msb.20156257

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Referee #1

Evidence, reproducibility and clarity

The authors generated and analyzed a great amount of single-cell RNA FISH data over time on circadian genes (Nr1d1, Cry1, Bmal1), and performed model selection/fitting to explain the observed mRNA distributions. They decomposed the mRNA variability into distinct sources, and showed that intrinsic noise (transcription burst) dominates the variance. Therefore, looking at transcript counts may not be feasible to estimate single-cell circadian phase. However, the study is quite descriptive and ends up being a bit dissatisfying, so if the authors could improve this aspect by perhaps analyzing a mechanism on cell-specific burst size (F5), gene-specific dependence on cell size (beta), or the positive/negative gene-pair correlations (rho), it would help quite a bit in this regard. The model selection/fitting itself was not really sufficient to compensate for this, as it stands .

Specific comments:

1.It is hard to distinguish the RNA FISH signals (Figure 1A, 2B). It is probably technically challenging as the mRNAs are of low abundance. I think it may help if they adjust the contrast for the cytoplasm stain or just delineate the cell boundaries.

2.In Figure 2C, the authors showed gene-pair correlations with cells of all sizes. Could the authors do a size-dependent extrinsic-noise filtering (Padovan-Merhar, Dev. Cell, 2015; Hansen et al., 2018, Cell Systems) to better dissect the correlations?

3.For fitting model M3, as the authors pointed out, there are many local minima. Is the fitting score truly sufficient to eliminate the possibility for partial synchrony especially considering that the authors didn't show how effective the Dex treatment was to synchronize the circadian phase?

4.Regarding model M4, the authors added a cell-specific noise term without specifying the contributing factors. Typically adding degrees of freedom should improve fitting and make it easier for a model to fit, why not in this case? Can the authors provide some explanations/mechanisms.

5.The authors should include the number (range) of cells analyzed in the figure legends.

Significance

Overall, we felt conflicted about the manuscript. On one hand, the authors generated and analyzed a great amount of single-cell RNA FISH data over time on circadian genes. On the other hand, the manuscript was a bit dissatisfying/descriptive. If the authors could provide and analyze some sort of mechanisms on cell-specific burst size (F5), gene-specific dependence on cell size (beta), or the positive/negative gene-pair correlations (rho) it should help improve the manuscript.

Referees cross-commenting

I agree with Reviewer #3 regarding expanding the discussion to include the Shah & Tyagi and Raj et al citations on buffering. However caution should be exercised regarding ref 26 as it is quite controversial and subsequent analyses came to different conclusions (PMID: 30359620 and 30243562). The general consensus is that nuclear buffering of transcript noise (proposed in ref 26) is not a general phenomenon (ref 27 is specific to the calcium response pathway). In fact, the presence and evolution of specific pathways to buffer transcriptional noise, such as protein-protein mechanisms (Shah & Tyagi) or extended half-life proteins (Raj et al. and others), argues that transcript fluctuations are not probably buffered in general.

"human nature"'s definition usually refers to learned cultural values which can be harmful

I feel like these few lines, in a way, frame the whole relationship of Ka and her father, a way that many people can relate to. Although the "natural" way of life is for children to be alive for the passing of their parents, it is an idea that seems so far away to most lucky children, that when they hear of the possibility, they shudder. They think it could never truly happen. What is then more interesting is that it kind of seems like the daughter is in that same denial. She (a few sentences up) admits that her father may even be mentally ill, but has not seen the signs, besides the prison nightmares, but that alone could be a sign enough. This type of denial we have as kids, follows us. It is what keeps us in denial about our biggest fears.

Reviewer #3:

In this manuscript, Sachella et al examine the contributions of the lateral habenula (LHb) to fear conditioning. They use 3 different paradigms: (1) a contextual fear conditioning paradigm, (2) a cued fear conditioning paradigm, (3) a combination paradigm where both context and cues can predict shocks. They also manipulate the LHb in several ways: (1) using muscimol, (2) using inhibitory optogenetics, (3) using excitatory optogenetics. The results are thought-provoking and would represent a novel contribution to the field, but I am left confused about some of the major points. My suggestions for improvement/clarification of the manuscript are as follows:

Major Comments:

1) Some important points need to be brought up in the introduction in order to frame the problem the authors are addressing and motivate the study. First, the introduction needs more background on separate circuits controlling cued vs contextual fear conditioning (hippocampus, amygdala). This only comes up in the discussion. Readers also need more background on connections between known structures for fear conditioning and the LHb. There should also be explicit discussion of the well characterized connections between LHb and dopamine neurons, including how LHb inputs help generate reward prediction errors that may be important for fear conditioning. The idea that prediction errors contribute to the authors' observations could be foreshadowed here.

2) In general, the muscimol experiments are nicely done. However, muscimol is always administered during training. I am left wondering whether LHb activity is required during the initial learning of the association or for consolidation later. It would be ideal to also include a test of muscimol infusion immediately following the FC training, during a memory consolidation period. This is important because the authors at times seem to argue that the LHb is important specifically for memory consolidation, but later in the discussion claim that activity during the training (related to prediction errors) is an explanation for their results.

3) I'm struggling with the interpretation of the experiments in Figures 3 + 4 using the cue + context FC paradigm and talking about "reconsolidation." These are really key to the paper so making sure the experiments are clear is a must. From the cue + context test, it seems that having both cues + contexts available for memory provides a much stronger memory. I am uncertain about why the authors think this is so and whether the effect is independent of the LHb? For the "reconsolidation" experiment, I can't figure out what's new. The no-reconsolidation group should look like Figure 2 muscimol group, and it mostly does. The reconsolidation group should look like the Figure 3 muscimol group, and it mostly does. So this looks to me more like a replication of Figures 2+3 (with no vehicle control) than anything else. What did we learn that could not be learned from the experiments in Figures 1-3? The suggestion is that "FC training under inactivation of the LHb creates a cued memory whose retrieval depends on contextual information." (lines 154-155). I don't disagree with this interpretation necessarily but it seems vague, and there is no circuit-level insight as to the mechanism.

4) The ArchT experiments, as the authors already recognize, are problematic because of potential heating and other artifacts. 25s of continuous 10mW green light is a lot. I am not left with much confidence in interpreting these experiments and therefore I am not sure why they are included in the paper. There are other methods of optogenetic inhibition that would be better suited perhaps, or the results could be replicated with chemogenetics, where the authors could ensure DREADD viruses did not spread into the medial habenula.

5) The oChIEF experiments are interesting, but again very difficult to interpret. There is no data showing what the stimulation does to LHb firing, which is a concern given the very long light stimulation (through the whole experiment). Therefore, it is unclear whether the authors' hypothesis that the light stimulation interferes with normal function is correct. The design here also does not take advantage of the temporal precision of optogenetics.

the language that we use to describe disabilities can influence both how others see people with disabilities, but also impact how people view themselves.

At face value, one may think the Mill Reef Club missing the old Antigua might be a good thing, but it does not help native Antiguans at all. While the natives miss the culture and appreciate the aspects of daily life, the Mill Reef Club misses the amenities and sense of escapism Antigua provided for them. Like tourists, they glorify the dirt roads and other "raw" aspects of Antigua, but they do not appreciate it enough to bring about improvement. They do not see Antigua as a home, but as a place that serves to benefit themselves.

Getting habituated to text production as just another task that machines can do

we like to think we're behind slavery and racial inequality but we're not. while we may not have the same black codes as they did hundred years ago, they are still built into our system one way or another

I still think that we have control over this type of stuff today.

Contextualize

Introducing exotic plants to a natural landscape can bring a different texture level to the site and bring an unexpected habitat to the existing landscape. This habitat may be useful or harmful to the existing condition, human has a plan to it but no power to control. One crucial element to remember when bringing in exotic plant species to the natural landscape is respecting the natural landscape and species. In the article, Wilde, Gandhi, and Colson state that “Recent ecological studies have found that landscaping with exotic plant species can reduce biodiversity on multiple trophic levels. To support biodiversity in urbanized areas, the increased use of native landscaping plants has been advocated by conservation groups and US federal and state agencies. A major challenge to scaling up the use of native species in landscaping is providing ornamental plants that are both ecologically functional and economically viable. Depending on ecological and economic constraints, accelerated breeding approaches could be applied to ornamental trait development in native plants. This review examines the impact of landscaping choices on biodiversity, the current status of breeding and selection of native ornamental plants, and the interdisciplinary research needed to scale up landscaping plants that can support native biodiversity”. There are chances of having negative impacts on the natural landscape when bringing in exotic species. Paying respect to the natural landscape is one of the keys to work on landscape design.

Wilde, H., Gandhi, K., & Colson, G. (2015, January 28). State of the science and challenges of breeding landscape plants with ecological function. Retrieved November 12, 2020, from https://www.nature.com/articles/hortres201469

Relate

Marx believes that humans need to respect nature during landscape design because there are so many uncertainties when bringing in exotic plant species into an environment. That is the right way to consider the relationship between the natural environment and outcoming plants. However, as a landscape architect, they should think about what the role of landscape architecture is? How does it communicate with the general public? What is the value of it? There are a handful of elements that landscape architects need to consider on the design to lead to the question: is it necessary to bring exotic plant species? After researching, studying, and discovering about the area site and alien plant species, whether bring in exotic plant species will be an easy decision to make. Also, evaluated the risk of exotic plant species is necessary. Ferrell It is hard to identify the line Cooper described between human development and nature. Only humans can learn and discover through it to figure out what the line is? How are we balance out the relation with nature? Getting human, educated, and informed is something fundamental to do. Therefore, enough knowledge could help humans to figure out the balance and have respect for nature.

"Pigeonholing" is endemic to the media and human nature, and I think this is definitely something to be aware of today. When a group of people act out with a set of goals or ideas that go against a media outlet's agenda, the media outlet will take advantage on any potentially controversial actions (or actions that they can spin as controversial) done by those people and use it to discredit the goals or ideas of that group. Media outlets aren't the only ones guilty of this; we as individuals and even governments are! That being said, I am glad that the New York Times article included this quote. "Ideas are bulletproof," and creating discomfort has been used throughout history by underrepresented voices to be heard.

1. I completely disagree with this statement as I once read in an article to which I totally agree too. A living thing needs to have certain characteristics to be counted as a living thing. These may include, speech, movement, reproduction, breathing, etc. As for animals, they have all these characteristics. The voice they take out makes us realize weather they're in pain or not. Moreover they're able to move if in danger. As for plants, the only 2 qualities they have are reproduction and breathing in one way or the other. So rather than considering cruelty towards animals, we should think twice before plucking out a plant and eating it.

Similarly good news, but long-term effects persist in some patients, I think. Again, people may see all the good news as reason to ignore social distancing and mask rules.

while the idea of [[diversity of thought]] may have started off a little more innocent (or not...), it's changed over the years to uphold the status quo, while distracting from [[DEI]] efforts that are aimed at improving representation, and lived experience

This sums up the entire point of the article. Wright says that Wallace makes good points on Natural Selection, however wavers when he begins to define things he does not understand as non-scientific or metaphysical. This article seems to not just be an argument for Darwin and Wallace’s natural selection theories, but a rebuke of Wallace’s ideas on will and his assertion of those things he does not understand like consciousness and feeling being placed under the banner of “will”. This may be the greatest contribution of this article, the defense of science in the time where science and religion were still intermingled and becoming frayed. Psychology should always be used in scientific terms, things like feeling and consciousness are difficult to explain as every individual experiences these things differently but they should be looked at through the lens of science and not as some mystical force which has predetermined/preprogrammed how we feel, act, and think.

This seems to be one of the key points Wright is trying to make with this article. It is almost as if he was influenced by those before him which worked with the nervous system. Thinking about the nervous system as a machine (very William James-ian) he basically says here that our nervous systems have evolved to the point which we do not have to consciously think about them for them to do their jobs, sort of in the way which we automatically breathe and have a heartbeat. Giving agency to parts of the body which it seems that humans have evolved to not need to regulate and it moves and operates by physical forces not metaphysical ones. Does this idea still hold true, it would seem correct as electrical impulses sent out from the brain do operate our entire body almost without any “will” from the user.

Wright talking here about materialism over what Wallace hypothesized is being compared to a machine here. After the thoughts on sensation which most materialist say are just atoms discharging against one another, Wright begins to focus on this idea that Wallace theorized was “Will”. Wright is correct in saying that Will is just another name for materialism and Wallace doesn’t really escape what materialism is by citing it as “Will”.

This point that Wright is making, trying to use scientific reasoning to understand and ultimately cut through Wallace’s argument for the more “mystical” explanations in evolutionary science is very interesting. While a bit hard to process, it does seem as if the idea here is to discount any argument of the supernatural using what Wright knows as the order of nature. For example: we know what a rock is made of, we know it is not sentient, and therefore has a purely objective existence. All of these things can be observed and scientifically studied, which is what Wright is trying to hammer on here. Stating that the question of if the rock has sensation is not only foolish but any answer to explain sensation in a rock would be equally if not more foolish. This is important as Wright is seemingly being a scientific purest here, almost saying that there is no room for God in scientific pursuit taking all of the metaphysical out of psychology.

While the business may see the bugs come in, churn, unhappy customers - and think that we may need to solve by adding more engineering people, we should be considering other options.

6

2

(Hypothesis didn't recognize the text so I couldn't add a normal annotation): "Good evening. I'm sorry to -- bother you, but we just thought we'd better let you know that we haven't got anything left. We sent up all we had. There's no more food down here (111)."

In Ben's communication with someone on the upper level, he shows a clear subordination to whoever it is. The pause after saying "sorry" made me think he had a momentary thought of: "I didn't sign up for this, why am I apologizing?" This is a fleeting thought though, if one at all, because he goes on to explain their inability to provide anything more. Without even knowing why, he's taken on the responsibility of giving Gus' things to an unknown "higher power." This bit of dialogue made it very obvious that the play is highlighting a blind adherence to authority, even if it's nonsensical to the viewer. We may even question our own judgement of it -- the hidden authority doesn't give us the space to clearly judge it. It can come off as humorous or frustrating that these orders have made the men panic.

This may be controversial but I think think there should be a perspective citing both her actions and how she was victimized but placing emphasis on the way she was victimized as a result. If she would have gotten out of her seat, there would have been a strong likelihood we would have never heard about this story. However, due to the fact that she did not and the officer used excessive force to remove her, clearly making her a victim in the situation.

I could equate it to driving. If you stop at a stop sign for less than three seconds, that's against the law. Say one stops at a stop sign for less than three seconds but due that action they get involved in a hit-and-run accident that leaves them inquired. Could stopping at that stop sign for the full three seconds changed the outcome? Possibly, but being involved in the accident doesn't make them any less of a victim.

Three Stages of Existence

1. State of Nature

• Man's nature is not shaped by the society.
• Understanding this state sheds light on social experience can shape men.
• Man is unsocial; it has native knowledge and has not acquired other knowledge.
• Man is independent, cannot be influenced by others.
• Man is innocent, is leaning to self-preservation, is lacking interest, his
• Man cannot return to its primeval state.

2. Social Dependence

• As new needs arise, man needs the service of other men.

• Possessions & division of labor = evils of social life.

  > A man with possessions is a man with something to lose, and a man who is dependent on the activities of others is also dependent upon their dispositions.

• Everyone is connected in circumstantial dependence & undesirable comparison

  • unequal circumstances may cause the "state of war"; it is where the government must exist to protect the rich's property and the poor's rights.

• Social existence stay and cannot return to primitive nature.

3. Social Contract/ Community

• Men should overcome conflicts that may dissemble men.
• Men must think that the goal is not to outdo each other but is to establish mutual connection.

• General will must manifest thru democracy, only by abolishing unequal privileges and partial combinations

  > all institutions and practices that mediated the direct relationship of man to community or that divided man's loyalty—were declared illegitimate.

• Better constitution = better influence

• Men as we know them are formed by society, they are malleable, and their social and political participation is potentially inherently re-warding.

Author Response

Summary: This study tackles a difficult problem of understanding the basis for hippocampal theta rhythms through reduction of a highly detailed model, seeking to validate a reduced model that would be more amenable to analysis. The reviewers appreciated the attention to this challenging problem and the substantial work that went into it, but had several fundamental concerns about the methodology, interpretation, and reporting.

We appreciate the detailed feedback provided to us by the reviewers and editors and we are pleased that there was an appreciation for the attention we have given to this challenging problem and the substantial work that went into it. We would like to thank the reviewers for their efforts.

This feedback helped us realize that there was possibly too much presented in this single paper and moving forward, we will split the work into two papers. While we agree with some of the feedback, we think that some aspects were misunderstood, which may be partially due to the extensiveness of the submitted paper. Below we provide general responses to the points raised, leaving specifics for elsewhere.

Reviewer #1:

This study takes two existing models of hippocampal theta rhythm generation, a reduced one with two populations of Izhikevich neurons, and a detailed one with numerous biophysically detailed neuronal models. The authors do some parameter variation on 3 parameters in the reduced model and ask which are sensitive control parameters. They then examine control of theta frequency through a phase response curve and propose an inhibition-based tuning mechanism. They then map between the reduced and detailed model, and find that connectivity but not synaptic weights are consistent. They take a subset of the detailed model and do a 2 parameter exploration of rhythm generation. They compare phenomenological outcomes of the model with results from an optogenetic experiment to support their interpretation of an inhibition-based tuning mechanism for intrinsic generation of theta rhythm in the hippocampus.

This statement summarizes our work to a certain extent but it misses a key aspect – the ‘mapping’ between the minimal (that this reviewer refers to as ‘reduced’) and detailed model is what is used to rationalize and motivate the subsequent extensive 2-parametric exploration in a ‘piece’ of the detailed model (which we termed the segment model). We will aim to write this more clearly in an edited version.

General comments:

1) The paper shows the existence of potential rhythm mechanisms, but the approach is illustrative rather than definitive. For example, in a very lengthy section on parameter exploration in the reduced model, the authors find some domains which do and don't exhibit rhythms. Lacking further exploration or analytic results, it is hard to see if their interpretations are conclusive.

We agree that these are interpretations (not meant to be conclusive), but the goal was to use the minimal model to develop further insight as we did with a hypothesis development presented in the middle of the paper.

2) The authors present too much detail on too few dimensions of parameters. An exhaustive parameter search would normally go systematically through all parameters, and be digested in an automated manner. For reporting this, a condensed summary would be presented. Here the authors look at 3 parameters for the reduced model and 2 parameters in the detailed one - far fewer than the available parameter set. They discuss the properties of these parameter choices at length, but then pick out a couple of illustrative points in the parameter domain for further pursuit. This leaves the reader rather overwhelmed on the one hand, and is not a convincing thorough exploration of all parameters of the system on the other.

See above.

3) I wonder if the 'minimal' model is minimal enough. Clearly it is well- supplied with free parameters. Is there a simpler mapping to rate models or even dynamical systems that might provide more complete insights, albeit at the risk of further abstraction?

We agree that models can be even more minimal, but the goal here was not to further analyse the minimal model through simpler mappings or otherwise. Rather, it was to exploit linkages between the minimal model and detailed models to help understand how theta rhythms could be generated in the biological system (Goutagny et al. 2009 intrinsic theta), using a piece of the detailed model as a ‘biological proxy’.

4) Around line 560 and Fig 12 the authors conclude that only case a) is consistent with experiment. While it is important to match data to experiment, here the match is phenomenological. It misses the opportunity to do a quantitative match which could be done by taking advantage of the biological detail in the model.

5) The paper is far too long and is a difficult read. Many items of discussion are interspersed in the results, for example around line 335 among many others.

We will split the paper into two.

Reviewer #2:

In this work Chatzikalymniou et al. use models of hippocampus of different complexities to understand the emergence and robustness of intra-hippocampal theta rhythms. They use a segment of highly detailed model as a bridge to leverage insights from a minimal model of spiking point neurons to the level of a full hippocampus. This is an interesting approach as the minimal model is more amenable to analysis and probing the parameter space while the detailed model is potentially closer to experiment yet difficult and costly to explore.

We completely agree.

The study of network problems is very demanding, there are no good ways to address robustness of the realistic models and the parameter space makes brute force approaches impractical. The angle of attack proposed here is interesting. While this is surely not the only approach tenable, it is sensible, justified, and actually implemented. The amount of work which entered this project is clear. I essentially accept the proposed reasoning and the hypotheses put forward. The few remarks I have are rather minor, but I think they merit a response.

1) l. 528-530 "This is particularly noticeable in Figure 9D where theta rhythms are present and can be seen to be due to the PYR cell population firing in bursts of theta frequency. Even more, we notice that the pattern of the input current to the PYR cells isn't theta-paced or periodic (see Figure 10Bi)."

This is a loose statement. When you look at the raw LFP theta is also not apparent (e.g. Figure 9.Ei or Fi). What happens once you look at the spectrum of the activity shown in 10.Bi? Do you see theta or not?

We agree – to be done.

2) l. 562 "This implies that the different E-I balances in the segment model that allow LFP theta rhythms to emerge are not all consistent with the experimental data, and by extension, the biological system."

This is speculative. We do not know how generic the results of Amilhon et al. are. They showed what you can find experimentally, not what you cannot find experimentally. I agree with the statement from l.581, though : "Thus, from the perspective of the experiments of Amilhon et al. (2015) theta rhythm generation via a case a type pathway seems more biologically realistic ..."

We agree – to edit accordingly.

3) There are several problems with access to code and data provided in the manuscript.

l. 986, 1113 - osf.io does not give access l. 1027 - bitbucket of bezaire does not allow access l. 1030 - simtracker link is down l. 1129, 1141 - the github link does not exist (private repo?)

Our apologies that all of these were not made public as intended.

4) l. 1017 - Afferent inputs from CA3 and EC are also included in the form of Poisson-distributed spiking units from artificial CA3 and EC cells.

Not obvious if Poisson is adequate here - did you check on the statistics of inputs? Any references? Different input statistics may induce specific correlations which might affect the size of fluctuations of the input current. I do not think this would be a significant effect here unless the departure from Poisson is highly significant. Any comments might be useful.

We were simply using the same input protocol setup done by Bezaire et al. 2016.

5) l. 909 - "Euler integration method is used to integrate the cell equations with a timestep of 0.1 msec."

This seems dangerous. Is the computation so costly that more advanced integration is not viable?

Our apologies as the timestep was erroneously reported. At initial stages of the project, larger stepsizes were attempted to speed up computation. The stepsize/integration used were as in minimal model of Ferguson et al. (2017). That is, Euler integration with a 0.04ms stepsize for the cell simulations and Runge-Kutta for network simulations.

Reviewer #3:

[...] I have a number of methodological issues with the paper. First, both models should be validated against experimental evidence given that the experimental results exist. The validation of a "minimal" model with data from another model is circumstantial and useful to link two models, but in no way is a scientific validation, in my opinion. Second, the model reduction arguments are simply taken as a piece of a large model. This is in now way a systematic reduction, which the authors should provide. In the absence of that, the two models are simply two different models. Third, it is not clear what aspects of the mechanisms cannot be investigated using the larger models that require the reduced models, given that the models do not necessarily match. Fourth, the concept of a minimal model should be clearly explained. They used caricature (toy) models of (2D quadratic models, aka Izhikevich models) combined with biophysically plausible descriptions of synapses. The model parameters in 2D quadratic models are not biophysical as the authors acknowledge, but they can be related to biophysical parameters through the specific equations provided in Rotstein (JCNS, 2015) and Turquist & Rotstein (Encyclopedia of Computational Neuroscience, 2018). In fact, they can represent either h-currents or M-currents. I suggest the authors determine this from these references. In this framework, the dynamics would result from a combination of these currents and persistent sodium or fast (transient) sodium activation. Fifth, from the original paper (Ferguson et al., 2017) their minimal model has 500 PV and 10000 PYR cells (I couldn't find the number of PV cells in this paper, but I assumed they were as in the original paper). This is not what I would call a minimal model. It is minimal only in comparison with the more detailed model. While this is a matter of semantics, it should be clarified since there are other minimal model approaches in the literature (e.g., Kopell group, Erdi group). Related to these models, it is typically assumed that the relationship between PYR to PV is 5/1. This is certainly not holy, but seems to have been validated. Here it is 20/1. Is there any reason for that? Sixth, the networks are so big that it is very difficult to gain some profound insight. What is it about the large networks and their contribution to the generation of theta activity that cannot be learned from "more minimal" networks?

The published minimal model (Ferguson et al. 2017) used experimental data constraints on EPSC and IPSC ratios to come up with the prediction of connectivity. As this connectivity was found in the detailed model (with empirically determined connections), this can be considered a form of validation for the minimal model’s predictions if one considers the detailed as a ‘biological proxy’.

We agree that the segment model is not a systematic reduction of the detailed model. The segment model reasonably represents a ‘piece’ of the CA1 microcircuit that was experimentally shown to be possible to be able to generate oscillations on its own (see Goutagny et al. 2009 Supplementary figure 11). This was the assumption in determining the network size of the previously published minimal model. A large network is needed in order to appropriate capture the very large EPSCs relative to IPSCs that are present in the experiment. This is the essence of why smaller network sizes cannot be justified.

Because of these concerns and the development of the paper, I believe the paper is about the comparison between two existing models that the authors have constructed in the past and the parameter exploration of these models.

We do not fully agree with this statement. The minimal model was constructed by us (Ferguson et al. 2017), but the detailed model was painstakingly constructed in a state-of-the-art fashion by Bezaire et al. 2016. We used a ‘piece’ of this detailed model (see above) so that we could make ‘links’ with the minimal model in understanding the generation of intrinsic theta rhythms. This ‘piece’ also allowed us to do the extensive exploration for the additional results presented. The paper is about taking advantage of the comparison and linkage of minimal and detailed models to show how theta rhythms are generated and their frequencies controlled.

I find the paper extremely difficult to read. It is not about the narrative, but about the organization of the results and the lack (or scarcity) of clear statements. I can't seem to be able to easily extract the principles that emerge from the analysis. There are a big number of cases and data, but what do we get out of that?. Perhaps creating "telling titles" for each section/subsection would help, where the main result is the title of the section/subsection. I also find an issue with the acronyms. One has to keep track of numbers, cases, acronyms (N, B), etc. All that gets in the way of the understanding. I believe figures would help.

Another confusing issue in the paper is the use of the concept of "building blocks". I am not opposed to the use of these words, on the contrary. But building blocks are typically associated with the model structure (e.g., currents in a neuron, neurons in a network). PIR, SFA and Rheo are a different type of building blocks, which I would call "functional building blocks". They are building blocks in a functional world of model behavior, but not in the world of modeling components. For example, PIR can be instantiated by different combinations of ionic currents receiving inhibitory inputs. Also, the definitions of the building blocks and how they are quantified should be clearly stated in a separate section or subsection.

The concept of building blocks was directly taken from Gjorgjieva et al. 2016 as cited in Ferguson et al. 2017 when we first used it, but also cited in the present paper, but for a different point.

I disagree with the authors' statement in lines 214-216, related to Fig. 4. They claim that "From them, we can say that the PYR cell firing does not speci1cally occur because of their IPSCs, as spiking can occur before or just after its IPSCs." Figure 4 (top, left panel) suggests the opposite, but instead of being a PIR mechanism, it is a "building-up" of the "adaptation" current in the PYR cell. (By "adaptation" current I mean the current corresponding to the second variable in the model. If this variable were the gating variable of the h-current, it would be the same type of mechanism suggested in Rotstein et al. (2005) and in the models presented in Stark et al. (2013).) The mechanism operates as follow: the first PV-spike (not shown in the figure) causes a rebound, which is not strong enough to produce a PYR spike before a new PV spike occurs (the first in the figure), this second PV-spike causes a stronger rebound (it is super clear in the figure), which is still not strong enough to produce a PYR-spike before the new PV-spike arrives, this third PV spike produces a still stronger rebound, which now causes a PYR spike. The fact that this PYR spike occurs before the PV spike is not indicative of the authors' conclusions, but quite the opposite.

The authors should check whether the mechanistic hypothesis I just described, which is consistent with Fig. 4 (top, left panel), is also consist with the rest of the panels and, more generally, with their modeling results and the experimental data and whether it is general and, if not, what are the conditions under which it is. If my hypothesis ends up not being proven, then they should come up with an alternative hypothesis. The condition the authors' state about the parameter "b" and PIR is not necessarily general. PIR and other phenomena are typically controlled by the combined effect of more than one parameter. As it stands, their basic assumption behind the PRC is not necessarily valid.

The subsequent hypothesis (about PYR bursting) is called to question in view of the previous comments. The experimental data should be able to provide an answer.

See above.

The authors should provide a more detailed explanation and justification for the presence of an inhibitory "bolus". What would the timescale be? Again, the data should provide evidence of that. In their discussion about the PRC, the authors essentially conclude what they hypothesis, but this conclusion is based on the "bolus" idea. The validity of this should be revised.

The discussion about degeneracy of the theta rhythm generation is interesting. However, because of the size and complexity of the models, this degeneracy is expected. Their minimal modeling approach does not help in shedding any additional light. In addition, the authors' do not discuss the intrinsic sources of degeneracy and how they interact with the intrinsic ones.

The last two sections were difficult to follow and I found them anecdotal. I was expecting a deeper mechanistic analysis. However, I have to acknowledge that because of my difficulty in following the paper, I might have missed important issues.

These last sections are where the ‘piece’ of the detailed model (that we termed the segment model) - a ‘biological proxy’ - essentially shows that the theta rhythm is initiated from the pyramidal cells and that the frequency is controlled by the net input to the pyramidal cells.

The discussion is extensive, exhaustive and interesting. But it is not clear how the paper results are integrated in this big picture, except for a number of generic statements.

The proposal that the hippocampus has the circuitry to produce theta oscillations without the need of medial septum input has been proposed before by Gillies et. (2003) and the models in Rotstein et al. (2005) and Orban et al. (2005). But the idea from this work is not that the hippocampus (CA1) is a pacemaker, but rather what we now call a "resonator". To claim that the MS is simply an amplificatory of an existing oscillator is against the existing evidence.

We agree that many models show theta generation without explicit mention of the medial septum. However, what our modelling work shows is how the intrinsic theta rhythm is generated – it is initiated by the pyramidal cells (large enough network size with some recurrent connections) and the control of the theta frequency (LFP) is due to the net input to the pyramidal cells – this is the main claim of the paper. This is explicitly in reference to an intrinsic theta rhythm experimental context. From there, we suggest that MS and other inputs could amplify an already existing intrinsic rhythm in the CA1 microcircuit.

References:

Bezaire, M. J., Raikov, I., Burk, K., Vyas, D., & Soltesz, I. (2016). Interneuronal mechanisms of hippocampal theta oscillation in a full-scale model of the rodent CA1 circuit. ELife, 5, e18566. https://doi.org/10.7554/eLife.18566

Ferguson, K. A., Chatzikalymniou, A. P., & Skinner, F. K. (2017). Combining Theory, Model, and Experiment to Explain How Intrinsic Theta Rhythms Are Generated in an In Vitro Whole Hippocampus Preparation without Oscillatory Inputs. ENeuro, 4(4). https://doi.org/10.1523/ENEURO.0131-17.2017

Gjorgjieva, J., Drion, G., & Marder, E. (2016). Computational implications of biophysical diversity and multiple timescales in neurons and synapses for circuit performance. Current Opinion in Neurobiology, 37, 44–52. https://doi.org/10.1016/j.conb.2015.12.008

Goutagny, R., Jackson, J., & Williams, S. (2009). Self-generated theta oscillations in the hippocampus. Nature Neuroscience, 12(12), 1491–1493. https://doi.org/10.1038/nn.2440

Reviewer #2:

In this work Chatzikalymniou et al. use models of hippocampus of different complexities to understand the emergence and robustness of intra-hippocampal theta rhythms. They use a segment of highly detailed model as a bridge to leverage insights from a minimal model of spiking point neurons to the level of a full hippocampus. This is an interesting approach as the minimal model is more amenable to analysis and probing the parameter space while the detailed model is potentially closer to experiment yet difficult and costly to explore.

The study of network problems is very demanding, there are no good ways to address robustness of the realistic models and the parameter space makes brute force approaches impractical. The angle of attack proposed here is interesting. While this is surely not the only approach tenable, it is sensible, justified, and actually implemented. The amount of work which entered this project is clear. I essentially accept the proposed reasoning and the hypotheses put forward. The few remarks I have are rather minor, but I think they merit a response.

1) l. 528-530 "This is particularly noticeable in Figure 9D where theta rhythms are present and can be seen to be due to the PYR cell population firing in bursts of theta frequency. Even more, we notice that the pattern of the input current to the PYR cells isn't theta-paced or periodic (see Figure 10Bi)."

This is a loose statement. When you look at the raw LFP theta is also not apparent (e.g. Figure 9.Ei or Fi). What happens once you look at the spectrum of the activity shown in 10.Bi? Do you see theta or not?

2) l. 562 "This implies that the different E-I balances in the segment model that allow LFP theta rhythms to emerge are not all consistent with the experimental data, and by extension, the biological system."

This is speculative. We do not know how generic the results of Amilhon et al. are. They showed what you can find experimentally, not what you cannot find experimentally. I agree with the statement from l.581, though : "Thus, from the perspective of the experiments of Amilhon et al. (2015) theta rhythm generation via a case a type pathway seems more biologically realistic ..."

3) There are several problems with access to code and data provided in the manuscript.

l. 986, 1113 - osf.io does not give access<br> l. 1027 - bitbucket of bezaire does not allow access l. 1030 - simtracker link is down l. 1129, 1141 - the github link does not exist (private repo?)

4) l. 1017 - Afferent inputs from CA3 and EC are also included in the form of Poisson-distributed spiking units from artificial CA3 and EC cells.

Not obvious if Poisson is adequate here - did you check on the statistics of inputs? Any references? Different input statistics may induce specific correlations which might affect the size of fluctuations of the input current. I do not think this would be a significant effect here unless the departure from Poisson is highly significant. Any comments might be useful.

5) l. 909 - "Euler integration method is used to integrate the cell equations with a timestep of 0.1 msec."

This seems dangerous. Is the computation so costly that more advanced integration is not viable?

I think this is super important. There is a large population of people in the United States who are against vaccinations. And we need to keep this in mind when looking at the backlash that this could cause when determining herd immunity. If there are enough people not getting vaccinations, the spread of the virus could be prolonged and outbreaks could be increased. I have even heard rumors and gossip about how once a vaccination is created, our government is going to force its citizens to take it. It will definitely be interesting to see what happens in the coming months to years.

Do a little research on Rembrandt's paintings and Frank Lloyd Wright's designs as described in https://flwright.org/researchandexplore/furnitureanddecorativearts. Do you think Wright would welcome a Rembrandt painting into his interior designs? Why or why not?

I thought this was extremely interesting. To begin, I agree greatly with the line in the beginning that states, "Whenever new approaches or techniques are being advocated, a very understandable ill-humor overcomes those who feel they may have to modify or to reconsider well-established pedagogical habits." I think this is accurate because many times, I've had English teachers complain or explain how new techniques or way of teaching literature are difficult to adapt to and requires them to change their logic on a lot and break old habits. I also thought that noting that their response feeds off of " moral indignation." Truthfully, whether they believe it or not, I find that a lot of teachers do teach the way they do or explain things the way they do based off of their morals and values. They aren't on the Supreme Court, so it is okay. Another thing that stuck out to me in this piece was the line, " Perhaps the most difficult thing for students and teachers to realized is that their appreciation is measured by the analytical rigor of their own discourse about literature, a criterion that is not primarily or exclusively aesthetic." Basically what I get form that after a bit of deciphering is that we appreciate the literature we are able to accurately discuss, and the more interested we are in our discussion about certain literature, the greater appreciation we have for it. It is not always an aesthetic, because it doesn't have to be something that necesarrily draws you in to imply an "aesthetic," yet it is merely a piece of literature that you are able to discuss based off of how much effort you put into analyzing it. I also liked how the author discussed how teaching English is not a "substitution for the teaching of theology, ethics, psychology, or intellectual history." I think it does indeed have to do with close reading. I've personally always thought of those subjects as completely seperate, however, it's interesting to see another viewpoint and understand why and how those possibilities could arise.

Summary: In this well done manuscript, the authors examine the bHLH transcription factor TWIST1 and its interacting proteins in neural crest cell development using an unbiased screen. Given the important role of neural crest cells in craniofacial and cardiac developmental defects, the data are both useful and important.

The major problem is the claim that the regulation reported here is important for neural crest specification / induction. This cannot be the case, as Twist 1 starts to be expressed in mouse only during the delamination step according to published single cell data. The premigratory Zic/Msx positive neural crest shows no expression of Twist1 before EMT markers kick in. The authors need to deal with this. It would be important to show in vivo expression data analysis and bring the conclusions in line with the timing in neural crest development.

Reviewer #1:

This excellent study is focused on the mechanisms of action of Twist1 in the neural crest cells and on the identification of core components of the Twist1 network. The authors performed an in-depth experimental study and sophisticated analysis to identify Chd7/8 as the key partners of Twist 1 during NCC development. This identification and corresponding predictions later appeared consistent with experimental in vivo data including single and combinatorial gene knockout mouse models with phenotypes in the cranial neural crest. Overall, this study is important for the field. However, I disagree with some secondary interpretations the authors give to their results. At the same time, the major conclusions stay solid. Below I discuss the most critical points.

1) Chd7, Chd8 and Whsc1 are ubiquitously expressed. Thus, the specificity of regulation is achieved via interactions with other, more cell type- and stage-specific, factors. This would be good to mention.

2) The authors suggest: "The phenotypic data so far indicate that the combined activity of TWIST1-chromatin regulators might be required for the establishment of NCC identity. To examine whether TWIST1- chromatin regulators are required for NCC specification from the neuroepithelium and to pinpoint its primary molecular function in early neural differentiation, we performed an integrative analysis of ChIP-seq datasets of the candidates".

• This is a strange assumption, given that Twist1 is expressed only starting from the NCC delamination stage in mouse cranial neural crest (Soldatov et al., 2019). It does not seem to correlate with premigratory NCC identity and the situation inside of the neural tube. The authors conclude: "Therefore, combinatorial binding sites for TWIST1, CHD7 and CHD8 may confer specificity for regulation of patterning genes in the NECs." Or, alternatively, they may confer the control of mesenchymal phenotype, downstream migration and fate biasing etc. I do not think the authors have good arguments to bring up induction or patterning of NCCs at the level of the neural tube.
• I have a good suggestion for the authors: I would extract the regulons from Soldatov et al. single cell data and run the binding site proximity check for the individual genes belonging to the gene modules /regulons specific to delamination and early NCC migration stages. I am curious, if the proximity of binding sites of Twist1-related crowd would rather correlate with genes from these specific regulons as compared to randomly selected regulons from the entire published single cell dataset. Randomization/bootstrapping analysis are welcomed. So far, being an excellent study, this paper does not solve a problem of downstream (of Twist1) gene expression program in the neural crest cells. At the same time, this is what the author can try to obtain with their DNA binding data in combination with published single cell data. Repression of Sox2 and upregulation of Pdgfra (reported in Figure 4) might be a part of this downstream program being in line with the published single cell gene expression data (Soldatov et al., 2019).
• The authors conclude the paragraph: "Therefore, combinatorial binding sites for TWIST1, CHD7 and CHD8 may confer specificity for regulation of patterning genes in the NECs". Again, this is not a good or plausible explanation based on specificity of expression of suggested patterning genes (or visualized genes are poorly selected). Additionally, although I believe the obtained results are important and of a good quality, I would not call them "developmentally equivalent to ectomesenchymal NCCs" or other NCCs. This is because the in vitro system will never reflect the embryonic in vivo development with high accuracy (especially when it comes to patterning and positional identity). This might explain that some prominent binding positions and interpretations the authors give do not correspond to the gene expression logic during neural crest development. Besides, Twist1 and Chd7/8 are naturally expressed in many other cell types and might target non-NCC genes (Vegfa?). This does not reduce the value of the data, but it is good to mention for the community.

3) Figure 2: Twist1-/+ Chd8-/+ is repeated two times in panel B (but the embryos look differently), although the authors most likely meant to show Twist1-/+ Chd7-/+ in the second case. If this is indeed the case, the authors should also show a phenotype of Chd7 KO.

4) The authors write: "Impaired motility in Twist1, Chd8 and Whsc1 knockdowns was accompanied by reduced expression of EMT genes (Pdgfrα, Pcolce, Tcf12, Ddr2, Lamb1 and Snai2) (Figure 6D, S3D) and ectomesenchyme markers (Sox9, Spp1, Gli3, Klf4, Snai1), while 375 genes that are enriched in the sensory neurons located in the dorsal root ganglia (Ishii et al., 2012) were upregulated (Sox2, Sox10, Cdh1, Gap43; Figure 6E).

• From the list of genes characterizing EMT, I can agree only on Pdgfra and Snai2, the rest is unspecific for EMT, and appears rather ubiquitous or specific to different cell populations (non-EMT).
• From the list of suggested ectomesenchyme markers, I cannot pick any gene that would be a bit specific for ectomesenchyme (within neural crest lineage) except for Snai1. Sox9 is broadly expressed also in the trunk neural crest, Spp1 and Klf4 are not expressed in early mouse ectomesenchyme, Gli3 is too broad and non-selective. I suggest to select other gene sets (check the expression with online PAGODA app from Soldatov et al): http://pklab.med.harvard.edu/cgi-bin/R/rook/nc.p63-66.85-87.dbc.nc/index.html
• The choice of DRG genes is also non-optimal, as Sox10 is pan-NCC, Sox2 is expressed in early migrating crest and satellite glial cells of DRG and Schwann cell precursors, Gap43 and Cdh1 are not specific enough. These genes clearly suggest the beginning of neuro-glial fates or trunk neural crest bias. To be more precise and for claiming sensory neurons, the authors should come up with pro-neuronal genes such as neurogenins, NeuroD, Isl1, Pou4f1, Ntrk and many others.

Still, overall, I agree with the author's main conclusions.

5) The authors write: "The genomic and embryo phenotypic data collectively suggest a requirement of TWIST1- chromatin regulators in the establishment of NCC identity in heterogeneous neuroepithelial 403 populations". Again, I do not think the authors can claim anything related to the establishment of NCC identity. NCC identity, in broad sense, includes NCC induction within the neural tube, at both trunk and cranial levels. In mice, Twist1 is not expressed in trunk NCCs at all. At a cranial level, Twist1 is expressed too late to be a NCC inducing or patterning gene. As I mentioned earlier, it comes up during delamination.

6) Figure 7G only partly corresponds to the positioning of the NCC markers in a mouse embryo. Id1 and Id2 are broadly expressed throughout all phases of NCC development and in the entire dorsal neural tube beyond the NC region. Mentioning Otx2 as a NCC specifier is strange. At the same time, Msx1, Msx2, Zic1 are excellent genes! Tfap2 is a bit too late, but still ok. Please keep in mind, Msx1/2, Zic1 are expressed before Twist1, and, thus, Twist1 can be downstream of this gene expression program. Also, these genes become downregulated quite soon upon delamination, whereas Twist1/Chd7/8 expression stays (in vivo). Expression pattern of Tfap2a better corresponds to Twist1, although Tfap2a comes a bit before Twist1, and, besides, Tfap2a is expressed independently of Twist1 in trunk NCC. Despite such gene expression divergence, Twist1-based networks might provide positive feedback loops stabilizing the expression of other transcriptional programs that were originally induced by other factors. It might be good mentioning this to the readers. This "stabilizing role" of the Twist1 network can be a really important one. Given the incremental and combinatorial nature of the phenotype in vivo - this is most likely the case. I believe these points are important to reflect in the discussion section.

Reviewer #2:

This manuscript, by Fan et. al, is a comprehensive look into the bHLH protein TWIST1 and its interacting proteins in neural crest cell differentiation. The study employs an unbiased screen where a TWIST1-BirA fusion is used in conjunction with biotin linking to collect Twist protein transcriptional complexes. (BioID-Proximity-labeling, TWIST1-CRMs). The work appears carefully done and the data and impact of this study are high given the nature of NCCs being involved as key players in craniofacial and cardiac developmental defects. The association of TWIST1 with the chromatin helicases CHD7 & 8 is important to understand as numerous TWIST1 loss-of-function studies indicate that its role in NCCs clearly is required for normal NCC function.

The NCC cell line O9-1 is used to collect the data. Genetic interactions between TW1, Chd7, Chd8 and Whsc1 are tested in genome edited ESCs. Overall, this is a well-executed, interesting and important study.

Reviewer #3:

Using BioID, the authors identified more than 140 proteins that potentially interact with transcription factor Twist1 in a neural crest cell line. Most of these 140 Twist1-interactomes do not overlap with the 56 known Twist1 binding partners during neural crest cell development (see below). By focusing on several strong Twist1 binding partner candidates (particularly a novel candidate CHD8), the authors found:

1) Twist1 interacts with these proteins via its N-terminal protein domain as demonstrated by co-IP.

2) Compound heterozygous mutation of Chd8, Chd7 or Whsc and Twist1 displayed more severe phenotype compared to heterozygous mutation of Twist1 alone, for example, more significant reduction of the cranial nerve bundle thickness.

3) ChIPseq analysis of Twist1 and CHD8 and key histone modifications revealed that the binding of Chd8 strongly correlates with those of Twist1, to active enhancers that are also labeled by H3K4me3 and H3K27ac.

4) The binding of CHD8 requires the binding of Twist1, but not vice versa.

5) Twist1-Chd8 regulatory module represses neuronal differentiation, and promotes neural crest cell migration, and potentially their differentiation into the non-neuronal cell types.

The authors use an impressive array of different techniques, both in vitro and in vivo, and yield consistent results. The manuscript is nicely written. The findings are nuanced, but the major conclusions are largely expected.

Critiques:

• As the title states, the three key TWIST interacting factors that most of the study focuses on are chromatin regulators. However, the consequence of mutating these factors at the epigenetic level was not directly addressed, including the level of active histone modification, the accessibility of the Twist1/CDH co-bound promoters/enhancers, and the position of nucleosomes.
• CRISPR-generated ESCs and chimera technology were used effectively to generate mutants. In comparison, the analysis of the phenotypes was rather cursory and can benefit from more in-depth molecular analysis. The altered genes found in mutant NEC and NCC in the last section of the study, especially, should be validated in mutants.
• Across the manuscript, there were jumps from NCC to NEC and back. It will be important to justify why a certain cell type is selected for each analysis, focusing on the biological question at hand.
• Using BioID, the authors detected 140 different proteins that interact with Twist1. However, only 4 of them overlap with the 56 known Twist1 partners (Figure 1A). This result suggests that BioID identified almost a distinct set of Twist1-interacting proteins, compared to the published results. The authors need to discuss the discrepancy, and the underlying reasons.
• The authors show that Twist1 colocalizes with Cdh8, and is required for the binding of Cdh8, thus suggesting that Twist1-Cdh8 form a regulatory module. Given the degenerate nature of bHLH factor binding motifs, it is likely that the binding of Twist1, and subsequently the binding of Cdh8, are dictated by other transcription factors. Therefore, a motif enrichment analysis should be done among the Twist1/Cdh8 co-binding sites, and compare those motifs enriched in Twist1-only and Cdh8-only binding sites.
• The increasing expression of DRG neurons genes in Twist1/Cdh8 mutants suggests a possible transition from cranial NC to trunk NC. Therefore, the authors should examine the expression of marker genes accordingly.

I was surprised that this paragraph is exactly regarding the topic I wrote for my social commentary essay. Writing my essay, I learned so much about what disaster would happen and how the end of the world comes as result of global warming. Intuitionally, we could think the increase of 1 or 2 degree is not a big deal. We could think it is 'just' 2 degrees but is isn't just marginal increase. Our earth is very sensitive to climate change so if the increase of climate really happens, weather anomalies such as heat waves, heavy rains, and fine dust will occur more and more frequently and drought will be everywhere resulting us to lose all the food resources. Unless any food-substitution is invented, we are all put the death because of famine. This is very serious problem. Since I am reading this article after writing my essay, my fury and anxiety penetrate deeply into my heart. Now I once more awakened why we should confront the global warming issue.

Beautiful example of a detailed (and reasonable) correction after the horse has bolted i.e. the report is out there, being used in media etc. I came across via 3 hyperlink trail from the report of an otherwise very admirable foundation where i found the claim "a typical person today is five times more likely to die in an extinction event than a car crash." There link took me to the Atlantic which had added an errata at the top (no doubt some time after their article was out) which took me to here.

I also find the correction somewhat dubious:

We do not know of a robust estimate of the annual probability of global catastrophic risk. Nor do we believe that we are able to create a robust estimate because the uncertainties in key parameters are so large. However, for extinction risks some experts have suggested that a 0.1% annual chance of extinction is within the range of plausible orders of magnitude. A 2008 Oxford survey of expert judgement on the topic implied an average annual extinction risk over the next century of around 0.2%. [1] The UK’s Stern Review on the Economics of Climate Change used 0.1% as an upper bound modeling assumption for annual extinction risk.

The experts they cite are, guess what, Sandberg and Bostrom from the very same organization they are associated with (Future of humanity). Their number seems IMO too high. A 0.2% risk per annum => 20% chance of total extinction in the next 100y (and where do these point estimates come from anyway!).

Furthermore, this is not a constant risk as with say a car crash (where the risk exists every time i drive).

I too used to believe this as a student in high school, and in high school i did not try things i thought i was gonna fail, i loved this passage, its also sad to think that there a lot of students out there that do not try something they could be good at.

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

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Reply to the reviewers

We thank the reviewers for their feedback and constructive comments to our work. We provide here a point-by-point response to the comments of Reviewers #1, #2 and #3 (text in grey and italic).

Responses written in plain text correspond to Reviewer comments that have been addressed in the revised version of the manuscript provided at this stage of the review process (referred-to as “revised version I” below).

Reponses written in bold text correspond to comments that need further experiments. The list of experiments we intend to perform to address these comments is provided in a separate document (Revision plan). The results of these additional experiments will be included in a later revised version of the manuscript referred-to as “revised version II” below.

Reviewer #1

The manuscript addresses an important topic, the posttranscriptional maturation of ribosomes. This topic is inherently interesting because we normally think of ribosome biogenesis as a sequential series of steps that automatically proceeds and cannot be "accelerated" in physiological conditions, but only "delayed" in the presence of genetic mutations. In short, the manuscript proposes that RIOK2 phosphorylation by the action of RSK, below the Ras/MAPK pathway promotes the synthesis of the human small ribosomal subunit.

I honestly admit that I have some difficulties in reviewing this manuscript. The quality of the presented data is, in generally, good. However, overall I find the whole manuscript preliminary and I am not much convinced of the conclusions. Several aspects are superficially analyzed. In short, I think that most of the conclusions are not fully supported by the data because shortcuts are present. A list of all the aspects that I found wrong are listed.

Biological issue

1. _The authors claim that the effects of the inhibition of the maturation of ribosomes by acting on a pathway upstream of RIOk2 are limited to the 40S subunit. This is far from being a trivial point, for the following reason. RIOK2 is known to affect the maturation of 40S ribosomes. Hence, the fact that using an upstream inhibitor of the MAPK pathway such as PD does not inhibit 60S processing in reality would argue against a biologically relevant control in ribosome maturation (of the MAPK patheay). Have the authors considered this? In a way, also, given the fact that the mutants confirm a role in 18S final maturation, it is a bit complex to put all the data in a clear biological context.

We agree that we put more emphasis on the effects on the pre-40S pathway than on the pre-60S pathway in the original manuscript but we did not claim that the effects of PD or LJH inhibitors of the MAPK pathway are restricted to the 40S subunit. We described that the effect of PD or LJH on the 32S was less severe than on the 30S, and we did mention variations of the 12S intermediate. These changes are in the same range of amplitude as the changes in the 21S and 18S-E intermediates in the small subunit pathway. The Northern blot data concerning the pre-60S pathway were placed in the supplementary material of the original manuscript, which may have left the reader with an impression of lesser emphasis. We rephrased this part in the present revised version I of the manuscript (Page 6, Line 26) and we now show the pre-40S and pre-60S intermediates on the same figures (Figures 1A and 1C).

In addition, we will probe more exhaustively the intermediates of the pre-60S pathway in the revised version II of the manuscript as described in the revision plan. These data will be complemented with metabolic labeling experiments to provide a more dynamic analysis of the pre-rRNA processing defects resulting from inactivation of the MAPK pathway. Furthermore, as requested by Reviewer #2 (see below), we will quantify more accurately these data.

A number of specific issues will be concisely described.

Manuscript very well written. Data do not always support the strong conclusions. Low magnitude of the observed effects.

In introduction the authors make a general claim that ribosome biogenesis is one of the most energetically demanding cellular activities. This statement lingers in the literature since 15 years but in reality it has never been formally proved for mammalian cells, and certainly not for HEK293 cells. The original statement, to my knowledge, can be traced by some obscure statement referred to the yeast case and then repeated as a truth. In conclusion, beside being a very banal observation, it should be referenced.

We agree with this comment of Reviewer #1. The original statement has been proposed by Jonathan R. Warner (Warner, 1999, TiBS and references therein) and data from the Bähler group also supported this statement (Marguerat et al., 2012, Cell). However, these data were indeed referring to yeast (S. cerevisiae and S. pombe). In the present revised version I of the manuscript, we introduced the reference of a review providing quantitative data of ribosome biogenesis in human cells (Lewis & Tollervey, 2000, Science) and we modified the problematic sentence as follows:” Growing human cells produce around 7500 ribosomal subunits per minutes (Lewis and Tollervey 2000), which represents a significant expenditure of energy.” (Page 4, Line 1).

Growth factors, energy status are not cues but are proteins or metabolites (introduction).

We agree with this comment of Reviewer #1. We changed the text accordingly in the revised version I of the manuscript (Page 4, Line 8).

Authors write about mTOR without making statements on mTORC1/2. This is very obsolete. Also I am not sure that the choice of Geyer et al., 1982, and subsequent papers makes much sense. At the very minimum TOP mRNA concepts and mTORC1 must be defined.

We provide more details on the mTOR pathway in the revised version I of the manuscript according to Reviewer #1’s suggestions (Page 4, Line 13 and Page 5, Line 3).

The authors claim that their work fills a major gap between known functions of MAPK and cytoplasmic translation. I would not be so sure about it.

Our original sentence stated that “our work fills a major gap between currently known functions of MAPK signaling in Pol I transcription and cytoplasmic translation”. Indeed, although MAPK signaling was known to regulate Pol I transcription and cytoplasmic translation, the impact of the pathway on the post-transcriptional steps of ribosome synthesis, namely pre-ribosome assembly and maturation, has been very little investigated and remains poorly understood. Our data provides the first example of a detailed mechanism of regulation of the maturation of pre-ribosomal particles by the MAPK pathway. Reviewers #2 and #3 seem to agree with this point:

Reviewer #2: “However, there is a lacking mechanistic connection of signaling pathways to pre-rRNA processing and maturation steps of ribosome biogenesis. The authors set out to provide a specific example of a direct target of MAPK signaling, RSK that regulates pre-rRNA maturation through the phosphorylation of a ribosome assembly factor (RIOK2), offering for the first time providing mechanistic insight into MAPK regulation of pre-rRNA maturation.”

Reviewer #3: “With these provisos, the work is technically good and will be of considerable interest to the field. The post-transcriptional regulation of ribosome synthesis is increasingly recognized a significant topic.”

Results. Authors start with a major mistake, i.e. that PMA selectively stimulates the MAPK pathway. Perhaps it stimulates, certainly it does not do it selectively.

We agree with this comment of Reviewer #1. We removed the term “selectively” in the problematic sentence (Page 6, Line 8).

RIOK2 phosphosites are first found by bioinformatics analysis. It should be noted that the predicted phosphosite (S483) is found only in a limited set of datasets from MS databases. The actual importance of this site would not emerge from unbiased studies. Also, there are many other phosphosites that were not analyzed in this study.

We agree with Reviewer #1 that phosphorylation of S483 of RIOK2 has been detected in a limited number of mass spectrometry datasets, but these datasets have been reported in high impact journals (Nature Methods, Mol Cell Proteomics, Science), attesting of the quality of these studies

As mentioned by Reviewer #1, there are several other phosphosites within RIOK2 that were not analyzed in our study. We provided the list of these phosphosites in Supplementary Table S1 of the original manuscript. Besides T481 and S483, none of the other sites belong to consensus motifs recognized by ERK or RSK at medium and high stringency. They are therefore less relevant to our study. We only analyzed phosphorylation at S483 because: (i) our mass spectrometry analysis revealed that S483 is the only phosphosite in RIOK2 whose level increases upon MAPK activation but not in the presence of the MAPK inhibitor PD184352 (Figure 2B); (ii) our in vitro kinase assay showed that the phosphorylation level of RIOK2 by RSK is residual when S483 is replaced by a non-phosphorylatable alanine (Figure 3D); (iii) our data presented in Figure 2C further show that mutation of T481 to an alanine does not prevent RIOK2 phosphorylation on RxRxxS/T motifs upon stimulation of the MAPK pathway.

We clarified this point in the relevant part of the result section of the revised version I of the manuscript (Page 7, Lines 16 and 24, Page 8, Line 17 and Page 9, Line 5).

Throughout the paper the authors use the word strongly, significantly, but the actual effects seem in general quite marginal.

We agree with Reviewer #1 that some of the phenotypes described in the manuscript are modest, in particular the phenotypes resulting from the S483A mutation of RIOK2, which is not aberrant for a point mutation. We rephrased several sentences throughout the manuscript to soften the formulation in the description and interpretation of the data and in the conclusions.

Discussion. The authors claim that they provide solid evidence on MAPK signalling to ribosome maturation. At the very best this is circumstantial evidence for the 40S maturation.

We rephrased the sentence accordingly (Page 16, Line 5): “Our study provides evidence that MAPK signaling applies another level of coordination during ribosome biogenesis, by directly regulating pre-40S particle assembly and maturation.”

Figure 1.

Unclear why LJH should increase P-ERK.

A negative feedback loop has been described in the MAPK pathway whereby RSK activation partially inhibits ERK phosphorylation (Saha et al., 2012, Horm Metab Res; Dufresne et al., 2001, MCB; Schneider et al., 2011, Neurochem; Re Nett et al., 2018, EMBO Rep). Inactivation of RSK with LJH alleviates this inhibition, which results in increased phosphorylation levels of ERK.

We added this information in the revised version of the manuscript along with the corresponding references (Page 6, Line 17).

General lack of quantitation (sd, replicates, bars). Experiment done only on a single cell line in a single experimental setup.

As also requested by Reviewer #2 (Major comment 1.), we applied in the revised version I of the manuscript RAMP quantifications to all Northern blot data. We included error bars corresponding to biological replicates.

Furthermore, in order to validate the impact of the MAPK pathway on pre-ribosome assembly and maturation, we plan to perform the same experiments using PD inhibitors in different cell lines and we will provide a figure with accurate RAMP quantifications, error bars and statistical significance, in the revised version II of the manuscript (see revision plan).

Very different effects on 21S by LJH, PMA and siRNA for RIOK2. Overall the message given by the authors is to me mysterious.

We assume that the reviewer wanted to point out the difference between PMA, PMA+LJH and shRNA for RSK since we did not perform RNAi targeting RIOK2. We agree with this comment. We believe that this difference is likely due to experimental setups that are different between both experiments. In the experiment using inhibitors, we assessed short-term effects of RSK inhibition after acute stimulation of the MAPK pathway (starved cells stimulated with PMA), while in the experiment using shRSK, we monitored long term effects of RSK depletion in serum-growing cells in which other signaling pathways are also active. Prolonged RSK depletion is likely to induce pleiotropic cellular effects, which would interfere with ribosome biogenesis both directly and indirectly. These differences probably explain the variable effects on the 21S intermediate. However, in both experiments we do observe an accumulation of the early 30S intermediate, consistent with the phenotype observed when ERK is inactivated (PD inhibitor), therefore indicating that RSK regulates some post-transcriptional stages of ribosome biogenesis.

To make our results clearer we have withdrawn the experiments using shRSK to avoid the risk of showing indirect effects due to the prolonged absence of RSK. Instead, we included RAMP analyses with error bars from 2 biological replicates using PD and LJH inhibitors (Figure 1B).

Figure 2.

Several red flags. For instance in 2C the loaded levels of RIOK2-HA loaded are clearly less than the ones of the other genotypes, hence the conclusion on P-RIOK2 is not convincing.

Our aim in this experiment was to compare the impact of PMA treatment on the phosphorylation levels of different RIOK2 mutants (T481A, S483A, double mutant). For a given mutant, the levels of RIOK2 loaded in the two conditions (i.e. not stimulated and PMA stimulated) are very similar and we therefore assume that our conclusions are valid.

We nevertheless plan to repeat these experiments and quantify the data for the revised version II of the manuscript.

Staining with anti-P RIOK2 lacks controls, how can be sure that the signal is due to the phosphate? Phosphatase treatment?

We fully agree with Reviewer #1 and we did perform an experiment showing that the phosphorylation signal disappears following treatment of the protein extracts with λ-phosphatase. We did not show these data in the original version of the manuscript because of space limitations. We added these data in the supplementary material of the revised version I of the manuscript (Supplementary Figure S2B) and amended the text accordingly (Page 7, Line 24)

Why FBS does not lead to ERK staining in HEK293? There are plenty of growth factors in FBS that should lead to ERK phosphorylation. I do not understand this experiment.

We agree with this comment. Addition of serum to starved cells does lead to ERK and RSK phosphorylation but with a much lesser efficiency compared to stimulation by EGF and PMA. ERK phosphorylation is barely visible on the exposure shown in Figure 2D but RSK-phosphorylation is clearly observed, although the signal is much weaker compared to EGF and PMA treatments. It is common to observe a stronger response with purified PMA and EGF (see Carrière et al., 2011, JBC ; Ray et al., 2013, Oncogene). There are indeed several growth factors in the serum, but the most abundant (Insulin, IGF1, TGF) are present at ng/ml concentration, while EGF is used at 25 µg/ml in Figure 2D. Moreover, they are not very strong activators of the Ras/MAPK pathway, and it is also possible that after 20 min of FBS treatment the phosphorylation is in the decreasing phase.

In the present revised version I of the manuscript, we included a set of western blots from another experiment showing the same results but of better quality to make the effects more visible (Fig. 2D). We also provided quantifications of phosphorylation of RIOK2 and associated statistical analyses (Fig. 2E).

Figure 3. In vitro phosphorylation, if I understood, it relies on a truncated version of RIOK2. Why? Is the folding of the full length protein not permissive to in vitro phosphorylation?

We did not test phosphorylation of the full length RIOK2 protein in vitro because RIOK2 has been reported to auto-phosphorylate (Zemp I. et al., 2009, JCB) and we were concerned that this auto-phosphorylation activity of RIOK2 in addition to RSK phosphorylation may render this experiment inconclusive.

HA-RSK3 is less?

It was reported that RSK3 is insoluble when over-expressed (Zhao et al., 1996, JBC), which explains the lower levels of protein recovered in our soluble extract. The information was present in the legend of Figure but we transferred it to the main text of the result section in the present revised version I of the manuscript (Page 10, Line 3).

Figure 4. Immunofluorescence is low mag, difficult to understand.

We agree with Reviewer #1. We modified the FISH experiment figure to show cells with a higher magnification and we provided more details in the text (Page 12, Lines 20-25) to facilitate the understanding of the data.

I really like the experiments with RIOK2 mutants, however I wonder what about protein levels after the knock-in? Given the 18S phenotype overlap between the phenotype of the RIOK2 loss of function with the S483A, testing protein level becomes of the utmost importance.

We checked RIOK2 protein levels and observed that the mutations do not decrease the level of RIOK2. On the contrary, the mutations slightly increase RIOK2 levels. Therefore, we are pretty confident that the phenotypes resulting from expression of RIOK2 mutants do not result from defects in the global accumulation of the protein. These data have been added to Figure 4C of the revised version I of the manuscript and we amended the text accordingly (Page 12, Line 5).

Figure 5. Low quality IFL.

Our aim in preparing this figure was to show many cells in the different images to show that the effect of our mutation was homogenous at the level of cell populations. The drawback is that cells are small and look blurred. We improved the quality of the figure in this revised version I of the manuscript with new images from the same experiment, showing less cells with a higher magnification.

Hard to think that histogram quantitation of nuclear versus cytoplasmic staining are reliable in the absence of fractionation, better quantitation, experiment done in other cell lines and so on.

We provide in this revised version I of the manuscript a supplementary figure explaining the procedure we used to quantify the fluorescence data (Supplementary Fig. S7).

Furthermore, to confirm this result using other experimental conditions and cell lines, we will transfect HEK293 and HeLa cells with plasmids expressing GFP-tagged RIOK2 WT or the S483S mutant and we will compare the kinetics of nuclear import of both proteins upon inhibition of pre-40S particle export by leptomycin B using fluorescence microscopy and GFP quantifications. Second, we will transfect HeLa cells with plasmids expressing HA-tagged RIOK2 WT or S483A and perform fractionation assays to monitor their presence in both cytoplasmic and nuclear compartments. We will include these data in the revised version II of the manuscript.

However, very beautiful Fig. 5E perhaps the best of the paper shows also mobility shift driven by S483, thus supporting posttranslational modifications.

We thank Reviewer #1 for this comment. We added the note on the evidence of RIOK2 post-translational modification in the result section (Page 14, Line 9).

Fig. 6. IFL studies are really impossible to interpret.

We improved the quality of the figure with new images from the same experiment, showing less cells with a higher magnification. NOB1 IF data and quantifications have been transferred to the supplemental material (Supplemental Fig. S4A and S4B) to clarify the figure. In addition, we provided more explanations on the principle of this experiment and expected results in the text (Page 15, Line 9).

The effects on RIOK2 release (this figure) and 18S maturation (Fig. 5) are very clear and of great quality.

We thank Reviewer #1 for this comment.

Overall conclusions. The manuscript tends to overinflate the meaning of several experiments. What to me is very clear and interesting is that the the authors provide clear evidence that S483A mutants have a defect in 40S maturation. Whether this is due to MAPK signalling, is only circumstantial. I would suggest to build up on the strong findings and eliminate ambiguous data.

We do not fully agree with this comment of Reviewer #1. If mutation S483A were simply a partial loss of function mutation, this would not be of strong interest for the subject of this manuscript. It would just indicate that S483 is important for RIOK2 function independently of its phosphorylation status. Our data show that the impact of S483 mutation on pre-rRNA processing and other phenotypes is different depending on whether the serine is converted to an alanine (phosphorylation mutant) or to an aspartic acid (phospho-mimetic mutation). These data are a strong indication that what matters is not simply the serine residue by itself but its phosphorylation status.

Reviewer #1 (Significance (Required)):

The paper deals with an important topic, namely whether a regulation of ribosome maturation exists, and how it is mechanistically regulated. In this context, the analysis of the ERK pathway is highly needed considered that most works deal with effects of the PI3K-mTOR pathway, and the parallel, yet important RAS-ERK pathway, is less understood.

As a final note, we should consider that S6K downstream of mTOR, and ribosomal S6K, downstream of ERK have been considered to share some substrates.

We introduced this information in the revised version of the manuscript (Page 19, Line 20). A related comment has been raised by Reviewer #3 (see below, Caveat #2).

The manuscript is interesting, but several statements given by the authors are rather superficial. An example, listed in the previous section, relates to the linguistic usage of mTOR kinase, instead of detailing whether we are dealing with mTORc1 or mTORc2.

We agree with this comment of Reviewer #1. Given that the main focus of this manuscript is the regulation by the MAPK pathway, we had chosen to put less emphasis on mTOR in the introduction. However, we added more precise information on mTOR in the present revised version I of the manuscript to address this comment (Page 4, Line 13 and Page 5, Line 3).

A second gross mistake is the definition of PMA as a stimulator of the ERK pathway. If this is certainly true, this is historically not correct as seminal papers by the group of Parker define this drug as a stimulator of conventional PKC kinases. In short, this paper is a step back in knowledge from the perspective of the literature context.

We are a bit confused by this comment because seminal papers from the Parker group clearly state that PMA activates the MAPK pathway via PKC (Adams and Parker, 1991, FEBS Lett.; Ways et al., 1992, JBC; Whelan et al., 1999, Cell Growth Differ.). We agree, as mentioned earlier by Reviewer #1, that PMA is not specific to MAPK, a comment that has been addressed above.

All people interested to the crosstalk between ribosome maturation and signaling pathways will be certainly read this manuscript.

My expertise is within the ribosome biology and signalling field.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

There have been mechanistic connections of various signaling pathways to regulation ribosome biogenesis steps including rDNA transcription by RNA polymerase I and III, ribosomal protein transcription, and differential mRNA translation efficiency. However, there is a lacking mechanistic connection of signaling pathways to pre-rRNA processing and maturation steps of ribosome biogenesis. The authors set out to provide a specific example of a direct target of MAPK signaling, RSK that regulates pre-rRNA maturation through the phosphorylation of a ribosome assembly factor (RIOK2), offering for the first time providing mechanistic insight into MAPK regulation of pre-rRNA maturation.

The authors observe slight pre-rRNA processing defects upon the use of RSK inhibitors and RSK depletion. They identified several candidate ribosome assembly and modification factors containing the canonical RSK substrate motif, including the RIOK2 kinase. Phosphorylation at this motif was verified to be specifically phosphorylated by RSK1 and 2 isoforms in cells and in an in-vitro kinase assay. The authors produced RIOK2 knock-in eHAP1 cell lines expressing non-phosphorylatable or phosphomimetic versions of RIOK2, observing slowed cellular proliferation, decreases in global translation, slight pre-rRNA processing abnormalities, but not changes in overall mature 18S rRNA levels. More specifically, the authors defined the inability of RIOK2 to be phosphorylated leads to defects in RIOK2 dissociation from the pre-40S ribosomal subunit in an in-vitro assay, and inability for it to be recycled for reuse in pre-ribosome export from the nucleus to the cytoplasm by immunofluorescence.

Overall, the authors provide an interesting mechanism of MAPK regulation of a ribosome assembly factor RIOK2. However, they fail to provide the necessary reproducibility, controls, quantification, and consistent results between experiments to support their hypotheses.

Major Comments:

1. The northern blots reported throughout the manuscript are lacking proper reproducibility and quantification. First, the northern blots are lacking a loading control, which is necessary to report fold changes that are being measured across treatments. Please include a proper loading control (i.e. 7SL or U6 RNAs). Additionally, more rigorous analysis of the pre-rRNA precursor levels through ratio analysis of multiple precursors (RAMP) (Wang et al 2014) can be completed to provide a clearer depiction on which precursor(s) are accumulating. It is unclear for the Figure 1 northern blots if there were replicates completed and what the error bars represent in Figure 1B. Please report replicates, so that statistical analysis can be completed on the differences in precursor relative abundance. This need is emphasized by the small changes observed in pre-rRNA levels (less than 2 fold) between conditions.

As mentioned above (Reviewer #1), we applied in the revised version I of the manuscript RAMP quantifications to all Northern blot data. These quantifications are shown as separate panels in the figures of the revised manuscript.

Furthermore, we are planning to repeat the Northern blot experiments of Figure 1 to obtain biological replicates in other cell lines. We will probe the membranes to detect the 7SL RNA as a loading control in all these experiments. We will perform RAMP analyses on all these Northern blot experiments to provide more accurate quantifications of the pre-rRNA levels in the different conditions. These data will be included in the revised version II of the manuscript.

1. The western blots reported throughout the manuscript are lacking proper reproducibility and quantification. For example, the western blots validating RSK1 and RSK2 depletion in Figure 1C lack a proper loading control. Additionally, it is unclear if there are replicates completed and there is lack of statistical analysis to determine if the changes are significant. Please include loading controls, replicates, and quantification of the western blots throughout the manuscript.

We have included actin levels as loading controls in several figures (Figures 2D, 3A, 3C, 3E, 4C) of the revised version I of the manuscript. We also added phosphorylated Rps6 at Ser235/36 to monitor RSK activity in Figures 1A, 2D, 3A.

We provided quantifications and associated statistical analyses of phosphorylation of RIOK2 presented in Figures 3A and 3C of the revised version I of the manuscript. We also included quantifications of the in vitro phosphorylation assays presented in Figures 3F and 3G.

We are nevertheless planning to repeat and quantify more accurately the western blot experiments presented in Figures 2A, 2C and 3E of the revised version I of the manuscript. These data will be included in the revised version II of the manuscript.

1. Please report the full bioinformatic analysis of the RSK substrate motif search among human AMFs including other AMFs found in this search. A sorted list format would be valuable for the reader to understand other potential RSK substrates involved in ribosome biogenesis.

We understand the request of Reviewer #2. Providing the full list of AMFs identified in our bioinformatic screen would be valuable for the reader, mostly because it would make clearer that RSK seems to be regulating multiple stages of the pre-ribosome maturation pathway, therefore that RSK inhibition induces pleiotropic defects in ribosome synthesis. However, we are currently working on a more global study of the impact of MAPK regulation on the post-transcriptional steps of ribosome synthesis that we would like to publish in a near future.

1. The authors report that RSK inhibition/depletion leads to accumulation of the 30S pre-rRNA, yet mutation of its target site on RIOK2 or RIOK2 depletion leads to an accumulation of the 18S-E pre-rRNA. Additionally, the phosphomimic mutation of RIOK2 leads to an accumulation of 30S, the opposite of the expected result. Please elaborate on this discrepancy in processing defects observed across experiments.

In contrast to RIOK2 which is specifically involved in the late, cytoplasmic stages of the maturation of the pre-40S particles, RSK regulates ribosome biogenesis at multiple levels. Upon activation of the MAPK pathway, RSK activates Pol I transcription in the nucleoli and promotes translation of mRNAs encoding ribosomal proteins and AMFs. In addition, our bioinformatic screen identified several AMFs at different stages of the maturation pathway of both ribosomal subunits as potential targets of RSK. These considerations imply that RSK inhibition is expected to impact ribosome biogenesis at multiple levels (Pol I transcription, availability of RPs and AMFs, export of the pre-ribosomal particles, probably several maturation steps) whereas RIOK2 inactivation more specifically delays 18S-E processing in the cytoplasm. In terms of processing, RSK inhibition induces a significant accumulation of the 30S intermediate. This is another evidence that RSK regulates pre-rRNA processing at several stages. This phenotype might result, as recently described in yeast (Yerlikaya et al., 2016, MCB), from an inhibition of RPS6 phosphorylation which affects its early incorporation into pre-ribosomes, although this has not been demonstrated in human cells. This 30S precursor accumulation affects production of the downstream intermediates and we strongly believe that this precludes accumulation of 18S-E even if the activity of RIOK2 is affected. Given the broad implication of RSK at different stages of ribosome biogenesis, it is biologically relevant to observe that inactivation of RSK does not result in the same processing defects as inactivation of RIOK2.

We nevertheless tried to make this point clearer in the present revised version I of the manuscript. We added in the supplementary material a diagram (Supplementary Fig. S1C) showing all the known and hypothetical targets of ERK and RSK in ribosome synthesis to provide the readers with a global view of the function of RSK in this process and refer to this figure in the introduction and results. In the introduction, we also emphasize more on the multiple aspects of the regulation of ribosome synthesis by ERK and RSK (Page 4, Line 18).

Concerning the phospho-mimetic mutant, it does accumulate slightly the 45S and 30S intermediates contrary to the non-phosphorylatable mutant but this is not totally unexpected. RIOK2 is incorporated into pre-ribosomes in the nucleus, at a stage that remains unclear, and constitutive RIOK2 phosphorylation may interfere with this recruitment and affect processing at an earlier stage. This point has been addressed in the discussion of the revised version I of the manuscript (Page 18, Line 7).

Are there similar results for RSK depletion/inhibition and RIOK2 release from the pre-40S and inability to import into the nucleus? If so, this could provide phenotypic consistency between these two proteins in the proposed pathway to further support the hypothesis.

We performed the same experiments as reported in Figure 6C to try to demonstrate a cytoplasmic retention of RIOK2 after leptomycin B treatment upon ERK inhibition (PD treatment). We also performed IF and cell fractionation experiments upon PD treatment. In all cases, we failed to observe the expected result. We strongly believe that we are facing here the same problem as described above for the previous comment of Reviewer #2. ERK and thus RSK inhibition leads to accumulation of the early, nucleolar 30S intermediate, indicating that the processing pathway is significantly blocked at an early stage preceding formation of the pre-40S particles in which RIOK2 is recruited. This early blockage most likely explains why we do not see the same phenotypes. We discussed this comment in the discussion section of the revised version I of the manuscript (Page 18, Line 19).

1. Mature levels of 18S rRNA are not altered in the RIOK2 mutant cell lines. This could be due to compensation in these mutant cell lines since RIOK2 is essential.

We agree with Reviewer #2 that compensation mechanisms may operate to restore mature 18S rRNA levels despite RIOK2 mutation. On the other hand, although RIOK2 is indeed essential, we may expect that the point mutation of S483 only partially affects RIOK2 function and delays the maturation of pre-40S particles but not to a sufficient extent to impact the mature 18S rRNA levels. This has been observed by others (Montellese et al., 2017, NAR; Srivastava et al., 2010, MCB).

We added this point in the discussion section of the revised version I of the manuscript (Page 19, Line 9).

Please report the mature 18S rRNA levels upon shRNA depletion and RSK inhibitors to provide insight into if this pathway significantly alters mature 18S rRNAs as a mechanism for the altered translation and proliferation observed.

We will probe the levels of the mature 18S and 28S rRNAs in these experiments and the results will be included in Figure 1 of the revised version II of the manuscript.

Minor Comments:

1. Figure 1A lower: The authors use an RSK inhibitor LJH685, that does not inhibit RSK phosphorylation S380. Therefore, another verification of RSK inhibition must be used besides RSK-pS380 abundance as for PD184352 inhibition. Please validate the usage of this RSK inhibitor in the experiments by inclusion of quantification of a direct downstream substrate of RSK, such as YB1-pS102 quantification.

We agree with Reviewer #2. We have probed the membrane with anti-RPS6 and anti-phosho-RPS6 antibodies to show the effect of LJH treatment on RPS6 phosphorylation. These data have been added to Figure 1A in the revised version I of the manuscript and the text has been updated (Page 6, Line 16).

1. Page 7, Lines 8-12: The authors state that RSK knockdown led to increases in the 45S, while the LJH685 treatment led to no changes in 45S levels due to differences in growth conditions. Please elaborate more on how growth conditions would alter 45S pre-rRNA levels. It would be expected that stimulation of the MAPK pathway would increase pre-rRNA transcription compared to steady state growth conditions. However, pre-rRNA processing northern blots are only measuring steady state levels of the precursors. Thus, an rDNA transcription assay would need to be completed to evaluate these differences.

We do observe that PMA treatment of starved cells induces an increase in 45S precursor levels, consistent with an increase in transcription but we agree that northern blot experiments measure the steady-state levels of the intermediates.

To address this comment, we propose to perform short pulse labelings with ortho-phosphate to assess synthesis of the 45S precursor independently of its processing in the different conditions. These data will be included in the revised version II of the manuscript.

1. Figure 2C: Please quantify these results to properly evaluate the role of these two phosphorylation sites in MAPK signaling.

We will repeat these experiments and quantify the results in the new version of Figure 2C.

1. Please include the RIOK2 pS483 antibody generation methodology used in this study.

We added this information in the Materials and Methods section of the revised version I of the manuscript (Page 21, Line 22).

1. In vitro kinase assay methods: Is the recombinant RSK1 the human version of the protein? Please clarify in methods.

Human recombinant RSK1 has been purchased from SignalChem. The information has been added in the revised version I of the manuscript (Page 30, Line 5).

1. Figure 4B: Please include statistical analysis of the puromycin incorporation assay.

We performed a statistical analysis of this assay out of 3 replicates. This analysis has been included in the present revised version I of the manuscript (Figure 4B).

1. Page 13, Line 18: Please explain why RIOK2 co-IP with NOB1 is important.

We added this explanation in the result section of the revised version I of the manuscript (Page 14, Line 3).

1. In vitro dissociation assay: There is no control for pulldown of entire pre-40S particles and not just NOB1 protein. Thus, it is unclear if RIOK2 is dissociating from NOB1 or entire pre-40S particles. Please reference previous literature of the methodology of this experiment if applicable. Additionally, please include controls, such as western blotting of ribosomal proteins or northern blotting of rRNA in the pulldown fraction used.

We agree with Reviewer #2. We have probed the membranes with antibodies detecting LTV1 and ribosomal protein RPS7 to show that the entire pre-40S particle is indeed pulled down. These additional data have been added in Figure 6A of the revised version I of the manuscript and the text has been amended accordingly (Page 14, Line 20).

1. Page 16, Lines 10-12: The authors state "RSK facilitates the release of RIOK2 and other AMFs", however the only other AMF in this study was NOB1. Please reword appropriately that most likely facilitates release of RIOK2 and other AMFs in a RIOK2 dependent or independent manner if it also phosphorylates other AMFs which possess the motif.

We agree with Reviewer #2 and we changed the text accordingly (Page 16, Line 11) but we did not introduce the hypothesis that RIOK2 may target directly other AMFs of late pre-40S particles which possess the motif because our in silico screen did not identify consensus RXRXXS/T motifs in any of these factors.

Reviewer #2 (Significance (Required)):

This manuscript is significant due to the lack of mechanistic connection of cellular signaling pathways to pre-rRNA processing. There have been, for the most part, no mechanistic connection of signaling pathways to pre-rRNA processing regulation and none for direct targets of MAPK signaling (Reviewed in Gaviraghi et al 2019). They provide the groundwork for analysis of MAPK signaling in regulation of an assembly factor and inclusion of their motif analysis could provide RSK signaling targets' regulation of specific steps of ribosome biogenesis that remain to be elucidated.

Although the research delves into a specific mechanism, its audience could be far reaching as it is in the ribosome biogenesis field and MAPK signaling, which have broad implications in cancer and developmental diseases.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

The authors report that inhibition of MAPK signaling via RSK is associated with modest alterations in the relative abundance of human pre-rRNA species, that are most marked for 30S but also visible for 21S - although not clearly shown for 18S-E.

RIOK2 has two closely spaced sites predicted as RSK targets, one of which was confirmed to be MAPK sensitive and shown to be an RSK substrate in vitro. Substitution of Ser483 with Ala was associated with reduced growth and 18S-E accumulation, consistent with impaired NOB1 cleavage activity. RIOK2-S483A also showed greater pre-ribosome association in vivo and consistent with this, more stable association in vitro and increase cytoplasmic residence. These effects are clear, although the data do not directly demonstrate their linkage to loss of RSK phosphorylation.

The mutations were apparently generated directly in the genome of haploid cells, potentially raising concerns that the introduction of a deleterious mutation might have been accompanied by compensatory mutations elsewhere. However, three cells line gave similar results, mitigating this concern.

Specific comments:

1. To help the reader, the authors should directly discuss why they think the data on MAPK inhibition did not reveal a clearer pre-18S cleavage phenotype, as would have been expected for loss of RIOK2 activity.

This comment is similar to major comment #4 of Reviewer #2.

Please refer to the above response.

1. Fig. S3: The degree of RSK depletion with the siRNAs appears very modest, as are the effects on RIOK2-P. Moreover, the double depletion is not clearly better than single depletions. These data should probably be supported by quantitation or withdrawn._

We agree with Reviewer #3 that the effects shown in this figure are modest but we originally chose to show these data because their further supported the role of RSK in RIOK2 phosphorylation at S483 in complement to Figure 3.

We have withdrawn this figure from the present revised version I of the manuscript.

1. Fig. 5D: For 18S-E recovery with RIOK2, is the ratio adjusted for the increase in 18S-E abundance in the mutant - ie is recovery increased when adjusted for the increased pre-rRNA abundance?_

In these experiments, the tagged versions of RIOK2 WT and S483A have been expressed ectopically from plasmids in cells expressing the endogenous wild-type protein. RIOK2 S483A does not behave as a dominant negative mutant in these conditions and does not induce 18S-E accumulation, as shown in the northern blot analysis of the 18S-E levels in the cell lysates (lower panel). This information is indicated in the revised version I of the manuscript (Page 13, Line 26).

Reviewer #3 (Significance (Required)):

Overall, the analyses on the phenotype of RIOK2-S483A, and the demonstration that this site is an RSK target, appear convincing.

Caveats are

1) the phenotype seen on inhibition of RSK, would not have implicated RIOK2 as the obvious candidate for the factor responsible for the observed processing defects;

We agree with this comment, which has also been raised by Reviewer #2 (Major comment 4.). We provide several evidence in the manuscript that RSK phosphorylates RIOK2 on S483 in vivo and in vitro (Figure 3). However, as explained above in response to Reviewer #2, we cannot correlate the in vivo phenotypes resulting from RSK or RIOK2 inactivation for biological reasons. As mentioned in the introduction, RSK regulates multiple substrates at different stages of ribosome biogenesis (Translation of RPs and AMFs, Pol I transcription, pre-ribosome maturation and export), whereas RIOK2 is specifically implicated in the cytoplasmic maturation of pre-40S particles. Inactivation of RSK is therefore expected to induce pleiotropic defects in ribosome biogenesis, and in particular early defects (Reduced Pol I transcription, 30S precursor accumulation) that preclude observation of the expected phenotype linked to RIOK2 inactivation, i.e. 18S-E accumulation.

We nevertheless tried to clarify this point as described in the response to Reviewer #2, major comment 4.

2) the RIOK2-S483A phenotype is not demonstrated to be RSK dependent. This raises the possibility that, although RSK can phosphorylate S483, the effects of the mutation are not due to the loss of this modification.

As mentioned by Reviewer #3, our data show that RSK can phosphorylate RIOK2 S483 in vitro and in vivo (Figure 3). We believe that Figure 4C strongly suggests that the accumulation of the 18S-E in cells expressing RIOK2 S483A mutant is due to the loss of S483 phosphorylation, since mutation of S483 to an aspartic acid (S483D), generally considered as a mutation mimicking a phosphorylated serine, does not affect 18S-E maturation. However, although our manuscript provides many lines of evidence identifying RSK as the kinase responsible for RIOK2 phosphorylation at S483, we cannot formally exclude that other AGC kinases involved in growth and proliferation, such as S6K or Akt, may also be involved redundantly or alternatively. Our data presented in Figure 3A showing that treatment of cells with the RSK inhibitors LJH decrease RIOK2 phosphorylation at S483 support a specific role of RSK.

We developed this point in the discussion section (Page 18, from Line 25).

With these provisos, the work is technically good and will be of considerable interest to the field. The post-transcriptional regulation of ribosome synthesis is increasingly recognized a significant topic.

Author Response

Summary:

This work is of interest because it increases our understanding of the molecular mechanisms that distinguish subtypes of VIP interneurons in the cerebral cortex and because of the multiple ways in which the authors address the role of Prox1 in regulating synaptic function in these cells.

The authors would like to thank the reviewers for their constructive comments. In response, we would like to clarify a number of issues, as well as outline how we plan to resolve major concerns.

Reviewer #1:

Stachiak and colleagues examine the physiological effects of removing the homeobox TF Prox1 from two subtypes of VIP neurons, defined on the basis of their bipolar vs. multipolar morphology.

The results will be of interest to those in the field, since it is known from prior work that VIP interneurons are not a uniform class and that Prox1 is important for their development.

The authors first show that selective removal of a conditional Prox1 allele using a VIP cre driver line results in a change in paired pulse ratio of presumptive excitatory synaptic responses in multipolar but not bipolar VIP interneurons. The authors then use RNA-seq to identify differentially expressed genes that might contribute and highlight a roughly two-fold reduction in the expression of a transcript encoding a trans-synaptic protein Elfn1 known to contribute to reduced glutamate release in Sst+ interneurons. They then test the potential contribution of Elfn1 to the phenotype by examining whether loss of one allele of Elfn1 globally alters facilitation. They find that facilitation is reduced both by this genetic manipulation and by a pharmacological blockade of presynaptic mGluRs known to interact with Elfn1.

Although the results are interesting, and the authors have worked hard to make their case, the results are not definitive for several reasons:

1) The global reduction of Elfn1 may act cell autonomously, or may have other actions in other cell types. The pharmacological manipulation is less subject to this interpretation, but these results are not as convincing as they could be because the multipolar Prox1 KO cells (Fig. 3 J) still show substantial facilitation comparable, for example to the multipolar control cells in the Elfn1 Het experiment (controls in Fig. 3E). This raises a concern about control for multiple comparisons. Instead of comparing the 6 conditions in Fig 3 with individual t-tests, it may be more appropriate to use ANOVA with posthoc tests controlled for multiple comparisons.

The reviewer’s concerns regarding non-cell-autonomous actions of global Elfn1 KO are well founded. Significant phenotypic alterations have previously been reported, both in the physiology of SST neurons as well in the animals’ behavior (Stachniak, Sylwestrak, Scheiffele, Hall, & Ghosh, 2019; Tomioka et al., 2014). The homozygous Elfn1 KO mouse displays a hyperactive phenotype and epileptic activity after 3 months of age, suggesting generalcortical activity differences exist (Dolan & Mitchell, 2013; Tomioka et al., 2014). Nevertheless, we have not observed such changes in P17-21 Elfn1 heterozygous (Het) animals.

Comparing across different experimental animal lines, for example the multipolar Prox1 KO cells (Fig. 3 J) to the multipolar control cells in the Elfn1 Het experiment (controls in Fig. 3E), is in our view not advisable. There is a plethora of examples in the literature on the effect of mouse strain on even the most basic cellular functions and hence it is always expected that researchers use the correct control animals for their experiments, which in the best case scenario are littermate controls. For these reasons, we would argue that statistical comparisons across mouse lines is not ideal for our study. Elfn1 Het and MSOP data are presented side by side to illustrate that Elfn1 Hets (3C,E) phenocopy the effects of Prox1 deletion (3G,H,I,J). (See also point 3) MSOP effect sizes, however, do show significant differences by ANOVA with Bonferroni post-hoc (normalized change in EPSC amplitude; multipolar prox1 control: +12.1 ± 3.8%, KO: -8.4 ± 4.3%, bipolar prox1 control: -5.2 ± 4.3%, KO: -3.4 ± 4.7%, cell type x genotype interaction, p= 0.02, two way ANOVA).

2) The isolation of glutamatergic currents is not described. Were GABA antagonists present to block GABAergic currents? Especially with the Cs-based internal solutions used, chloride reversal potentials can be somewhat depolarized relative to the -65 mV holding potential. If IPSCs were included it would complicate the analysis.

No, in fact GABA antagonists were not present in these experiments. The holding voltage in our evoked synaptic experiments is -70 mV, which combined with low internal [Cl-] makes it highly unlikely that the excitatory synaptic responses we study are contaminated by GABA-mediated ones, even with a Cs MeSO4-based solution. Nevertheless, we have now performed additional experiments where glutamate receptor blockers were applied in bath and we observe a complete blockade of the synaptic events at -70mV proving that they are AMPA/NMDA receptor mediated. When holding the cell at 0mV with these blockers present, outward currents were clearly visible, suggesting intact GABA-mediated events.

3) The assumption that protein levels of Elfn1 are reduced to half in the het is untested. Synaptic proteins can be controlled at the level of translation and trafficking and WT may not have twice the level of this protein.

We thank reviewer for pointing this out. Our rationale for using the Elfn1 heterozygous animals is rather that transcript levels are reduced by half in heterozygous animals, to match the reduction we found in the mRNA levels of VIP Prox1 KO cells (Fig 2). The principle purpose of the Elfn1 KO experiment was to determine whether the change in Elfn1 transcript levels could be sufficient to explain the synaptic deficit observed in VIP Prox1 KO cells. As the reviewer notes, translational regulation and protein trafficking could ultimately result in even larger changes than 0.5x protein levels at the synapse. This may ultimately explain the observed multipolar/bipolar disparity, which cannot be explained by transcriptional regulation alone (Fig 4).

4) The authors are to be commended for checking whether Elfn1 is regulated by Prox1 only in the multipolar neurons, but unfortunately it is not. The authors speculate that the selective effects reflect a selective distribution of MgluR7, but without additional evidence it is hard to know how likely this explanation is.

Additional experiments are underway to better understand this mechanism.

Reviewer #2:

Stachniak et al., provide an interesting manuscript on the postnatal role of the critical transcription factor, Prox1, which has been shown to be important for many developmental aspects of CGE-derived interneurons. Using a combination of genetic mouse lines, electrophysiology, FACS + RNAseq and molecular imaging, the authors provide evidence that Prox1 is genetically upstream of Elfn1. Moreover, they go on to show that loss of Prox1 in VIP+ cells preferentially impacts those that are multipolar but not the bipolar subgroup characterized by the expression of calretinin. This latter finding is very interesting, as the field is still uncovering how these distinct subgroups emerge but are at a loss of good molecular tools to fully uncover these questions. Overall, this is a great combination of data that uses several different approaches to come to the conclusions presented. I have suggestions that I think would strengthen the manuscript:

1) Can the authors add a supplemental table showing the top 20-30 genes up and down regulated in their Prox1 KOS? This would make these, and additional, data more tenable to readers.

We would be happy to provide supplementary tables with candidate genes at both P8 and P12.

2) It is interesting that loss of Prox1 or Elfn1 leads to phenotypes in multipolar but are not present or mild in bipolar VIP+ cells. The authors test different hypotheses, which they are able to refute and discuss some ideas for how multipolar cells may be more affected by loss of Elfn1, even when the transcript is lost in both multipolar and bipolar after Prox1 deletion. If there is any way to expand upon these ideas experimentally, I believe it would greatly strengthen the manuscript. I understand there is no perfect experiment due to a lack of tools and reagents but if there is a way to develop one of the following ideas or something similar, it would be beneficial:

We thank the reviewer for the note.

a) Would it be possible to co-fill VIPCre labeled cells with biocytin and a retroviral tracer? Then, after the retroviral tracer had time to label a presynaptic cell, assess whether these were preferentially different between bipolar and multipolar cell types, the latter morphology determined by the biocytin fill? This would test whether each VIP+ subtype is differentially targeted.

Although this is a very elegant experiment and we would be excited to do it, we do feel that single-cell rabies virus tracing is technically very challenging and will take many months to troubleshoot before being able to acquire good data. Hence, we think it is beyond the scope of this study.

b) Another biocytin possibility would be to trace filled VIP+ cells and assess whether the dendrites of multipolar and bipolar cells differentially targeted distinct cortical lamina and whether these lamina, in the same section or parallel, were enriched for mGluR7+ afferents.

We thank the reviewer for their suggestion and we are planning on doing these kinds of experiments.

Reviewer #3:

In this work Stachiak and colleagues investigate the role of Prox1 on the development of VIP cells. Prox1 is expressed by the majority of GABAergic derived from the caudal ganglionic eminence (CGE), and as mentioned by the authors, Prox1 has been shown to be necessary for the differentiation, circuit integration, and maintenance of CGE-derived GABAergic cells. Here, Stachiak and colleagues show that removal of Prox1 in VIP cells leads to suppression of synaptic release probability onto cortical multipolar VIP cells in a mechanism dependent on Elfn1. This work is of interest for the field because it increases our understanding of differential synaptic maturation of VIP cells. The results are noteworthy, however the relevance of this manuscript would potentially be increased by addressing the following suggestions:

1) Include histology to show when exactly Prox1 is removed from multipolar and bipolar VIP-expressing cells by using the VIP-Cre mouse driver.

We can address this by performing an in-situ hybridization against Prox1 from P3 onwards (when Cre becomes active).

2) Clarify if the statistical analysis is done using n (number of cells) or N (number of animals). The analysis between control and mutants (both Prox1 and Elfn1) need to be done across animals and not cells.

Statistics for physiology were done across n (number of cells) while statistics for ISH are done across number of slices. We will clarify this point in the text and update the methods.

Regarding the statistics for the ISH, these have been done across n (number of slices) for control versus KO tissue (N = 3 and N = 2 animals, respectively). We will add more animals to this analysis to compare by animal instead, although we do not expect any change in the results.

Regarding the physiology, we would provide a two-pronged answer. We first of all feel that averaging synaptic responses for each animal would hide a good deal of the biological variability in PPR present in different cells (response Fig 1), the characterization of which is integral to the central findings of the paper. Secondly, to perform such analysis asked by the reviewer one would need to obtain recordings from ~10 animals or so per condition for each condition, which, to our knowledge, is something that is not standard when utilizing in vitro electrophysiological recordings from single cells. For example, in these very recent studies that have performed in vitro electrophysiological recordings all the statistics are performed using “n” number of cells and not the average of all the cells recorded per animal collapsed into a single data point. (Udakis, Pedrosa, Chamberlain, Clopath, & Mellor, 2020) https://www.nature.com/articles/s41467-020-18074-8

(Horvath, Piazza, Monteggia, & Kavalali, 2020) https://elifesciences.org/articles/52852

(Haas et al., 2018) https://elifesciences.org/articles/31755

Nevertheless, we have now re-run the analysis grouping the cells and averaging the values we get per animal, since we have obtained our data from many animals. The results are more or less indistinguishable from the ones presented in the original submission, except for on p value that rose to 0.07 from 0.03 due to the lack of the required number of animals. We hope that the new plots and statistics presented herein address the concern put forward by the reviewer.

*Response Fig 1: A comparison of cell wise versus animal-wise analysis of synaptic physiology. Some cell to cell variability is hidden, and the reduction in numbers impacts the P values.*

(A) PPR of multipolar Prox1 Control for 14 cells from 9 animals (n/N=14/9) under baseline conditions and with MSOP, cell-wise comparison p = 0.02 , t = 2.74 and (B) animal-wise comparisons (p = 0.04, t stat = 2.45). Statistics: paired t-test.

(C) PPR of multipolar Prox1 KO cells (n/N=9/8) under baseline conditions and with MSOP, cell-wise comparison p = 0.2, t = 1.33 and (D) animal-wise comparisons (p = 0.2, t stat = 1.56). Statistics: paired t-test. Comparisons for PPR of bipolar Prox1 Control (n/N=8/8) and KO cells (n/N=9/9) did not change.

(E) PPR for Prox1 control (n/N=18/11) and KO (n/N=13/11) bipolar VIP cells, cell-wise comparison p = 0.3, t = 1.1 and (F) animal-wise comparisons (p = 0.4, t stat = 0.93). Statistics: t-test.

(G) PPR of Elfn1 Control (n/N=12/4) and Het (n/N=12/4) bipolar VIP cells, cell-wise comparison p = 0.3, t = 1.06 and (H) animal-wise comparisons (p = 0.4, t stat = 0.93)

(I) PPR of Prox1 control (n/N=33/18) and KO (n/N=19/14) multipolar VIP cells, cell-wise comparison p = 0.03, t = 2.17. and (J) animal-wise comparisons (p = 0.07, t stat = 1.99).

(K) PPR of Elfn1 Control (n/N=14/6) and Het (n/N=20/8) multipolar VIP cells, cell-wise comparison p = 0.008, t = 2.84 and (L) animal-wise comparisons (p = 0.007, t stat = 3.23).

3) Clarify what are the parameters used to identify bipolar vs multipolar VIP cells. VIP cells comprise a wide variety of transcriptomic subtypes, and in the absence of using specific genetic markers for the different VIP subtypes, the authors should either include the reconstructions of all recorded cells or clarify if other methods were used.

We thank the reviewer for this comment. The cell parameter criteria will be amended in the methods: “Cell type was classified as bipolar vs. multipolar based on cell body morphology (ovoid vs. round) and number and orientation of dendritic processes emanating from it (2 or 3 dendrites perpendicular to pia (for bipolar) vs. 3 or more processes in diverse orientations (for multipolar). In addition, the laminar localization of the two populations differs, with multipolar cells found primarily in the upper layer 2, while bipolar cells are found throughout layers 2 and 3. Initial determination of cell classification was made prior to patching fluorescent-labelled cells, but whenever possible this initial assessment was confirmed with post-hoc verification of biocytin filled cells.”

Reference:

Dolan, J., & Mitchell, K. J. (2013). Mutation of Elfn1 in Mice Causes Seizures and Hyperactivity. PLOS ONE, 8(11), e80491. Retrieved from https://doi.org/10.1371/journal.pone.0080491

Haas, K. T., Compans, B., Letellier, M., Bartol, T. M., Grillo-Bosch, D., Sejnowski, T. J., … Hosy, E. (2018). Pre-post synaptic alignment through neuroligin-1 tunes synaptic transmission efficiency. ELife, 7, e31755. https://doi.org/10.7554/eLife.31755

Horvath, P. M., Piazza, M. K., Monteggia, L. M., & Kavalali, E. T. (2020). Spontaneous and evoked neurotransmission are partially segregated at inhibitory synapses. ELife, 9, e52852. https://doi.org/10.7554/eLife.52852

Stachniak, T. J., Sylwestrak, E. L., Scheiffele, P., Hall, B. J., & Ghosh, A. (2019). Elfn1-Induced Constitutive Activation of mGluR7 Determines Frequency-Dependent Recruitment of Somatostatin Interneurons. The Journal of Neuroscience, 39(23), 4461 LP – 4474. https://doi.org/10.1523/JNEUROSCI.2276-18.2019

Tomioka, N. H., Yasuda, H., Miyamoto, H., Hatayama, M., Morimura, N., Matsumoto, Y., … Aruga, J. (2014). Elfn1 recruits presynaptic mGluR7 in trans and its loss results in seizures. Nature Communications. https://doi.org/10.1038/ncomms5501

Udakis, M., Pedrosa, V., Chamberlain, S. E. L., Clopath, C., & Mellor, J. R. (2020). Interneuron-specific plasticity at parvalbumin and somatostatin inhibitory synapses onto CA1 pyramidal neurons shapes hippocampal output. Nature Communications, 11(1), 4395. https://doi.org/10.1038/s41467-020-18074-8

Reviewer #3:

This manuscript reports results from an eye tracking study of humans walking in natural terrain. These eye movements together with images simultaneously obtained by a head-fixed camera are used to calculate optic flow fields as seen by the retina and as seen by the head-fixed camera. Next, the structure of these flow fields is described. It is noted that this structure is somewhat stable in the retinal image, due to compensatory gaze stabilisation reflexes, but varies wildly in the head-centric image. Then, the authors estimate the focus of expansion in the head-centric flow and argue that it cannot be used for locomotor control, because it also varies wildly during walking. In a second, more theoretical section of the manuscript, they calculate retinal flow for a movement over an artificial ground plane, given the locomotor and eye movements recorded previously. They describe the structure of the retinal flow and compute the distribution of curl and divergence across the retina as well as in a projection onto the ground plane. They argue that curl around the fovea and the location of the maximum of divergence can be used to estimate the direction of walking relative to the direction of gaze and in relation to the ground plane.

I really like the experimental part of the study. However, I see fundamental issues in the theoretical part, in the general framing of the presentation, and in misrepresentations of previous literature.

The simultaneous measurement of head-centric image and gaze with sufficient temporal resolution to calculate retinal flow during natural walking provides a beautiful demonstration of retinal flow fields, and confirms many known aspects of retinal flow. The calculation of head-centric flow from the head camera images provides a compelling, though not unexpected, demonstration that the FOE in head-centric flow is not useful for locomotor control. It is not unexpected since one of the most well-known issues in optic flow is that the FoE is destroyed when self-motion contains rotational components (Regan and Beverley, 1982, Warren and Hannon, 1990, Lappe et al. 1999). Although this is often presented as an issue of eye movements in retinal flow, it applies to all rotations and combinations of rotations that exist on top of any translational motion of the observer. Thus, the oscillatory bounce and sway motion of the head during walking is expected to render any use of the FOE in a head-centric image futile.

Yet, the first part of the manuscript is very much framed as a critique of the idea of a stable FoE in head-centric flow, presuming that this is what previous researchers commonly believed. This argument contains a logical fallacy. Previous research argued that there is no FoE in retinal flow because of eye rotations (e.g. Warren and Hannon, 1990). This does not predict, inversely, that there is an FoE in head-centric flow. In fact, it does not provide any prediction on head-centric flow. The authors often suggest that a stable FoE in head-centric flow is tacitly implied, commonly believed, etc without providing reference. In fact, the only paper I know that specifically proposed a head-centric representation of heading is by van den Berg and Beintema (1997).

Instead, the fundamental problem of heading perception is to estimate self-motion from retinal flow when the self-motion that generates retinal flow combines all kinds of translations and rotations. The present study shows, consistent with much of the prior literature, that the patterns of retinal flow are sufficiently stable and informative to obtain the direction of one's travel in a retinal frame of reference, and, via projection, with respect to the ground plane. This is due to the stabilising gaze reflexes that keep motion small near the fovea and produce (in case of a ground plane) a spiralling pattern of retinal flow. This is well known from theoretical and lab studies (e.g. Warren and Hannon, 1990, Lappe et al., 1998, Niemann et al., 1999, Lappe et al. 1999) and, to repeat, beautifully shown for the natural situation in the present data. The presentation should link back to this work rather than trying to shoot down purported mechanisms that are obviously invalid.

The second part of the manuscript presents a theoretical analysis of the retinal flow for locomotion across a ground plane under gaze stabilisation. This has two components: (a) the structure of the retinal flow and the utility of gaze stabilisation, and (b) ways to recover information about self-motion from the retinal flow. Both aspects have a long history of research that is neglected in the present manuscript. The essential circular structure of the retinal flow during gaze stabilisation is long known (Warren and Hannon, 1990, van den Berg, 1996, Lappe et al., 1998, Lappe et al. 1999). Detailed analyses of the statistical structure of retinal flow during gaze stabilisation have shown the impact and utility of gaze stabilisation (Calow et al., 2004; Calow and Lappe, 2007; Roth and Black, 2007) and provided links to properties of neurons in the visual system (Calow and Lappe, 2008). These studies included simulated motions of the head during walking, as in the current manuscript, and extended to natural scenes other than a simple ground plane.

Given the structure of the retinal flow during gaze stabilisation the central question is how to recover information about self-motion from it. The authors investigate a proposal originally made by Koenderink and van Doorn (1976; 1984) that relies on estimates of curl and divergence in the visual field. They propose that locomotor heading may be determined directly in retinotopic coordinates (l. 314). This is true, but it fails to mention that other models of heading perception during gaze stabilisation similarly determine heading in retinotopic coordinates (e.g. Lappe and Rauschecker, 1993; Perrone and Stone, 1994; Royden, 1997). In fact, as outlined above, the mathematical problem of self-motion estimation is typically presented in retinal (or camera) coordinates (e.g. Longuet-Higgins and Prazdny, 1980). The problem with the divergence model in comparison to the other models above is threefold. First, it really only works for a plane, not in other environments. Second, it requires a local estimate of divergence at each position in the visual field. The alternative models above combine information across the visual field and are therefore much more robust against noise in the flow. One would need to see whether the estimate of the divergence distribution is sufficient to work with the natural flow fields. Third, being a local measure it requires a dense flow field while heading estimation from retinal flow is known to work with sparse flow fields (Warren and Hannon, 1990). Thus, the theoretical part of the manuscript should either provide proof that the maximum of divergence is superior to these other models or broaden the view to include these models as possibilities to estimate self motion from retinal flow.

The case is similar for the use of curl. It is true that the rotational or spiral pattern around the fovea in retinal flow provides information about the direction of self motion with respect to the direction of gaze, as has been noted many times before. This structure is used by many models of heading estimation. However, curl is, like divergence, a local property and thus not as robust as models that use the entire flow field. It may be interesting to note that neurons in optic flow responsive areas of the monkey brain can pick up this rotational pattern and respond to it in consistency with their preference for self-motion across a plane (Bremmer et al., 2010; Kaminiarz et al. 2014).

I think what the authors may want to draw more attention to is the dynamics of the retinal flow and the associated self-motion in retinal (or plane projection) coordinates. The movies provide compelling illustrations of how the direction of heading (or the divergence maximum, if you want to focus on that) sways back and forth on the retina and on the plane with each step. This requires that the analysis of retinal flow (and the estimation of self-motion) has to be fast and dynamic, or maybe should include some form of temporal prediction or filtering. Work on the dynamics of retinal flow perception has indeed shown that heading estimation can work with very brief flow fields (Bremmer et al. 2017), that the brain focuses on instantaneous flow fields (Paolini et al. 2000) and that short presentations sometime provide better heading estimates than long presentations (Grigo and Lappe, 1999). The temporal dynamics of retinal flow is an underappreciated problem that could be more in the focus of the present study.

Additional specific comments:

Footnote on page 2: It is not only VOR but also OKN (Lappe et al., 1998, Niemann et al., 1999) that stabilises gaze in optic flow fields.

Line 55: Natural translation and acceleration patterns of the head have been considered by (Cutting et al., 1992; Palmisano et al. 2000; Calow and Lappe, 2007, 2008; Bossard et al., 2016)

Line 59: The statement is misleading that the key assumption behind work on the rotation problem is that the removal of the rotational component of flow will return a translational flow field with a stable FoE. Only one class of models, those using differential motion parallax (Rieger and Lawton, 1985, Royden, 1997) explicitly constructs a translational flow field and aims to locate the FoE in that field. Other models (Koenderink and van Doorn, 1976, 1984; Lappe and Rauschecker, 1993; Perrone and Stone, 1994) do not subtract the rotation but estimate heading in retinal coordinates from the combined retinal flow. This also applies to line 109.

Last paragraph on page 5: Measures of eye movement during walking in natural terrain were also taken by Calow and Lappe (2008) and 't Hart and Einhäuser (2012).

Lines 140 to 163: This paragraph is problematic and misleading as pointed out before.

Line 193: The lack of stability is expected, as outlined above. The use of a straight line motion in psychophysical experiments reflects an experimental choice to investigate the rotation problem in retinal flow, not an implicit assumption that bodily motion is usually along a straight line.

Line 200: That gaze stabilization may be an important component in understanding the use of optic flow patterns has also long been assumed (Lappe and Rauschecker, 1993; 1994; 1995; Perrone and Stone, 1994; Glennerster et al. 2001; Angelaki and Hess, 2005; Pauwels et al., 2007).

Line 314: Locomotor heading may be determined directly in retinotopic coordinates. Yes, and this is precisely what the above mentioned models do.

Line 334: What is meant by "robust" here? The videos seem to show simulated flow for a ground plane, not the real flow from any of the terrains. It is not clear whether the features can be extracted from the real terrain retinal flow.

First paragraph on page 15: This is an important discussion about the dynamics of retinal flow in conjunction with the dynamics of the gait cycle. It should be expanded and better balanced with respect to previous work and other models. It is true that any simple inference of an FoE would not work. However, models that estimate heading (not FoE) in the retinal reference frame would be consistent with the discussion. Oscillations of the head during walking affect the location of the divergence maximum and curl as much as the direction of heading in retinal coordinates. In fact, the videos nicely show how these variables oscillate with each step. This applies to all retinal flow analyses, and is a problem for any model. It requires a dynamical analysis. The speed of neural computations is an issue, of course, but it applies to divergence and curl in the same way as to other models. There is some indication, however, that neural computations on optic flow are fast, deal with instantaneous flow fields, and respond consistently to natural (spiral) retinal flow, as described above.

Line 393: This paragraph is misleading in suggesting that naturally occurring flow fields have not been used in psychophysical and electrophysiological experiments.

Line 516: This has been done by Bremmer et al. (2010) and Kaminiarz et al. (2014). Their results are consistent with computing heading directly in a retinal reference frame as predicted by several models of retinal flow analysis (e.g. Lappe et al. 1999).

References:

Angelaki, D. E. and Hess, B. J. M. (2005). Self-motion-induced eye movements: effects an visual acuity and navigation. Nat. Rev. Neurosci., 6:966-976.

Bossard, M., Goulon, C., and Mestre, D. R. (2016). Viewpoint oscillation improves the perception of distance travelled based on optic flow. J Vis, 16(15):4.

Bremmer, F., Kubischik, M., Pekel, M., Hoffmann, K. P., and Lappe, M. (2010). Visual selectivity for heading in monkey area MST. Exp. Brain Res., 200(1):51-60.

Calow, D., Krüger, N., Wörgötter, F., and Lappe, M. (2004). Statistics of optic flow for self-motion through natural scenes. In Ilg, U., Bülthoff, H. H., and Mallot, H. A., editors, Dynamic Perception, Workshop of the GI Section 'Computer Vision', pages 133-138, Berlin. Akademische Verlagsgesellschaft Aka GmbH.

Calow, D. and Lappe, M. (2007). Local statistics of retinal optic flow for self- motion through natural sceneries. Network, 18(4):343-374.

Calow, D. and Lappe, M. (2008). Efficient encoding of natural optic flow. Network Comput. Neural Syst., 19(3):183-212.

Cutting, J. E., Springer, K., Braren, P. A., and Johnson, S. H. (1992). Wayfinding on foot from information in retinal, not optical, flow. J. Exp. Psychol. Gen., 121(1):41-72.

Grigo, A. and Lappe, M. (1999). Dynamical use of different sources of information in heading judgments from retinal flow. JOSA A, 16(9):2079-2091.

't Hart, B. M. and Einhäuser, W. (2012). Mind the step: complementary effects of an implicit task on eye and head movements in real-life gaze allocation. Exp. Brain Res., 223(2):233-249.

Kaminiarz, A., Schlack, A., Hoffmann, K.-P., Lappe, M., and Bremmer, F. (2014). Visual selectivity for heading in the macaque ventral intraparietal area. J. Neurophys. 112(10):2470-80

Lappe, M., Pekel, M., and Hoffmann, K. P. (1998). Optokinetic eye movements elicited by radial optic flow in the macaque monkey. J. Neurophysiol., 79(3):1461-1480.

Lappe, M. and Rauschecker, J. P. (1993). A neural network for the processing of optic flow from ego-motion in man and higher mammals. Neural Comp., 5(3):374-391.

Lappe, M. and Rauschecker, J. P. (1994). Heading detection from optic flow. Nature, 369(6483):712-713.

Lappe, M. and Rauschecker, J. P. (1995). Motion anisotropies and heading detection. Biol. Cybern., 72(3):261-277.

Niemann, T., Lappe, M., Büscher, A., and Hoffmann, K. P. (1999). Ocular responses to radial optic flow and single accelerated targets in humans. Vision Res., 39(7):1359-1371.

Pauwels, K., Lappe, M., and Hulle, M. M. (2007). Fixation as a mechanism for stabilization of short image sequences. Int. J. Comp. Vis., 72(1):67-78.

Perrone, J. A. and Stone, L. S. (1994). A model of self-motion estimation within primate extrastriate visual cortex. Vision Res., 34(21):2917-2938.

Regan, D. and Beverley, K. I. (1982). How do we avoid confounding the direction we are looking and the direction we are moving? Science, 215:194-196.

Rieger, J. H. and Lawton, D. T. (1985). Processing differential image motion. J. Opt. Soc. Am. A, 2(2):354-360.

Roth, S. and Black, M. J. (2007). On the spatial statistics of optical flow. Int. J. Comp. Vis., 74(1):33-50.

Royden, C. S. (1997). Mathematical analysis of motion-opponent mechanisms used in the determination of heading and depth. J. Opt. Soc. Am. A, 14(9):2128-2143.

van den Berg, A. V. (1996). Judgements of heading. Vision Res., 36(15):2337-2350.

van den Berg, A. V. and Beintema, J. A. (1997). Motion templates with eye velocity gain fields for transformation of retinal to head centric flow. NeuroReport, 8(4):835-840.

These all look good - I don't think you need to change anything.

This rhetorical question is a good response to the claims of Bloom's argument. The author suggest that even though a good may be historically relevant, it may not describe the worth of the good entirely. Instead, the author suggests more reasoning than simply history defining something as expensive.

En ese párrafo el autor nos habla sobre el primer tema que abordará. Básicamente dice que intentará demostrar en el ensayo como a lo largo del tiempo muchos grandes individuos han fomentado correcta e incorrectamente la ciencia. Y de que el don de la observación cuanto más ampliamos nuestras consideraciones y cuanto más relacionamos los fenómenos entre sí es ejercitándolo. Teniéndolo y sabiéndolo relacionar con nosotros mismos en nuestras acciones podremos ganar el derecho a ser llamados inteligentes.

Author Response

Summary:

The strengths of the study are the findings that a single oxytocin level measured from saliva or plasma is not meaningful in the way that the field might currently be measuring. The reviewers appreciated this finding, and the careful attention to detail, but felt that the results fell short.

Reviewer #1:

This article describes the investigation of a valuable research question, given the interest in using salivary oxytocin measures as a proxy of oxytocin system activity. A strength of the study is the use of two independent datasets and the comparison between intranasal and intravenous administration. The authors report poor reliability for measuring salivary oxytocin across visits, that intravenous delivery does not increase concentrations, and that salivary and blood plasma concentrations are not correlated.

Line 77-78: While it's true that saliva collection provides logistical advantages, there are also measurement advantages (e.g., relatively clean matrix) that are summarised in the MacLean et al (2019) study, which has already been cited.

Thanks for the suggestion. We added this advantage:

Line 101 “Compared to blood sampling, saliva collection presents several logistical and measurement advantages (i.e. relatively clean matrix)(1).”

Line 86: It is important to note that the 1IU intravenous dose in this study led to equivalent concentrations in blood compared to intranasal administration.

The reviewer is right that 10 IU (over 10min) in our case increased the concentrations of plasmatic oxytocin beyond those observed for the spray or nebuliser (we reported the full time-course of variations in plasmatic oxytocin in another manuscript we published earlier this year)(2). This was an intentional aspect of our study design. We decided to use the highest intravenous dose (at the highest rate of 1IU/min) that we could get permission to administer safely in healthy volunteers as a proof of concept, so as to achieve a robust and prolonged increase in plasmatic oxytocin over the course of our full testing session. In this manner, we demonstrate that even when plasmatic levels of OT are maintained substantially increased throughout the observation interval, we cannot detect increases in salivary oxytocin. In this aspect, we believe that our manuscript goes one step beyond the important findings described in of Quintana et al. 2018(3), showing that this phenomenon is not linked to dosage (or to amount of increase in plasmatic levels of exogenous OT), as far as we can determine given the current safety standards for the administration of OT IV.

Please see also response to Reviewer 2, point 1.

Line 158: When using both ELISA and HPLC-MS, extracted and unextracted samples are correlated when measuring oxytocin concentrations in saliva, at least in dogs. (https://doi.org/10.1016/j.jneumeth.2017.08.033).

Thanks for pointing out this study. Indeed, in this specific study the authors found correlations between extracted and unextracted saliva samples. Such associations in humans have nevertheless been rare. In humans, the body of evidence suggests that the measurements obtained when comparing extracted samples to unextracted samples, or when comparing samples obtained using different methods of quantification (for instance, ELISA versus radioimmunoassay), do not correlate or show very low correlations (4, 5). Furthermore, most ELISA kits and HPLC-MS protocols to measure oxytocin have so far fallen short on sensitivity to detect the typical concentrations observed in humans at baseline (0-10pg/ml)(6). The current gold-standard method for quantifying oxytocin in biological fluids is the radioimmunoassay we used in this study(4). This method has shown superior sensitivity and specificity when compared to other quantification methods, when combined with extracted samples; therefore, it was our primary choice. We now highlight this advantage in the revised version of the manuscript more explicitly.

Line 129 “For all analyses, we followed current gold-standard practices in the field and assayed oxytocin concentrations using radioimmunoassay in extracted samples, which has shown superior sensitivity and specificity when compared to other quantification methods(7).”

Statistical reporting: I ran the article through statcheck R package (a web version is also available) and found a number of inconsistencies with the reported statistics and their p values. For example, on Line 302 the authors reported: t(123) = 1.54, p = 0.41, but this should yield a p value of 0.13. The authors should do the same and fix these errors.

Thanks very much for taking the time to check our statistical reporting thoroughly. We apologize if we were not sufficiently clear in the previous version of the manuscript, but the p-values we reported are corrected for multiple comparisons using Tukey correction. Currently, statcheck can only evaluate inconsistencies when the results are reported in the standard APA style and does not take into consideration corrections for multiple comparisons of any kind. We did check all of our statistical reporting and the p-values and correspondent statistics are correct (we only corrected an inadvertent error in reporting the degrees of freedom for these tests). In any case, we have now clarified in the manuscript when the reported p-values have been adjusted for multiple comparison to avoid any further confusion.

Line 305: The confidence intervals for these correlations should be reported.

We have now added the confidence intervals, estimated using bootstrapping, in our results section.

Line 348: This is an important point, but it's important to note that the vast majority of these studies use plasma or saliva measures. Perhaps CSF measures are more reliable, but the question wasn't assessed in the present study, and I'm not sure if anyone has looked at this question.

We are not aware of any study evaluating the stability of measurements of oxytocin in the CSF. Indeed, there are only a few studies sampling CSF to measure oxytocin in clinical patients and it is unlikely that CSF will become a widely used fluid to measure oxytocin in humans, given the invasiveness of the procedure to obtain CSF samples. Here, we wanted to refer specifically to saliva and plasma, which remain as the most popular options for measuring oxytocin in humans and which we investigated specifically in the current study. We have changed the text accordingly for clarity.

Line 466 “Our data poses questions about the interpretation of previous evidence seeking to associate single measurements of baseline oxytocin in saliva and plasma with individual differences in a range of neuro-behavioural or clinical traits.”

Line 423: I broadly agree with this conclusion, but it should be added that "single measurements of baseline levels of endogenous oxytocin in saliva and plasma are not stable under typical laboratory conditions" Perhaps these measures can be more stable using other means (i.e., better standardising collection conditions). But the fact remains, under typical conditions these measures do not demonstrate reliability.

Thanks for the suggestion. We have revised the text accordingly throughout the manuscript (examples below). Our study is a pharmacological study, which means that it is conducted in a highly controlled setting and adheres to strict protocols (i.e. we tested participants at the same time of the day, we instructed participants to abstain from alcohol and heavy exercise for 24 h and from any beverage or food for 2 h before scanning). These exclusion criteria were stricter than those applied in a large number of studies sampling saliva and plasma for measuring oxytocin for the purposes estimating possible associations with various traits associating. Most of these studies do not control, for instance, for fluid or food ingestion. Therefore, we expected our reliability calculations to represent an optimistic estimate of the reliabilities of the salivary and plasmatic oxytocin concentration used in most studies.

For now, it remains unclear to us what factors might be driving the within-subject variability in salivary and plasmatic concentrations we report in this study. Thanks to Reviewer 3, we are now confident that this is unlikely to represent measurement error (see response to Reviewer 3, point 3).

Line 117 “Here, we aimed to characterize the reliability of both salivary and plasmatic single measures of basal oxytocin in two independent datasets, to gain insight about their stability in typical laboratory conditions and their validity as trait markers for the physiology of the oxytocin system in humans.”

Line 567 “In summary, single measurements of baseline levels of endogenous oxytocin in saliva and plasma as obtained in typical laboratory conditions are not stable and therefore their validity as trait markers of the physiology of the oxytocin system is questionable.”

Reviewer #2:

Summary:

To test questions whether salivary and plasmatic oxytocin at baseline reflect the physiology of the oxytocin system, and whether salivary oxytocin index its plasma levels, the authors quantified baseline plasmatic and/or salivary oxytocin using radioimmunoassay from two independent datasets. Dataset A comprised 17 healthy men sampled on four occasions approximately at weekly intervals. In the dataset A, oxytocin was administered intravenously and intranasally in a triple dummy, within-subject, placebo-controlled design and compared baseline levels and the effects of routes of administration. With dataset A, whether salivary oxytocin can predict plasmatic oxytocin at baseline and after intranasal and intravenous administrations of oxytocin were also tested. Dataset B comprised baseline plasma oxytocin levels collected from 20 healthy men sampled on two separate occasions. In both datasets, single measurements of plasmatic and salivary oxytocin showed insufficient reliability across visits (Intra-class correlation coefficient: 0.23-0.80; mean CV: 31-63%). Salivary oxytocin was increased after intranasal administration of oxytocin (40 IU), but intravenous administration (10 IU) does not significantly change. Saliva and plasma oxytocin did not correlate at baseline or after administration of exogenous oxytocin (p>0.18). The authors suggest that the use of single measurements of baseline oxytocin concentrations in saliva and plasma as valid biomarkers of the physiology of the oxytocin system is questionable in men. Furthermore, they suggest that saliva oxytocin is a weak surrogate for plasma oxytocin and that the increases in saliva oxytocin observed after intranasal oxytocin most likely reflect unabsorbed peptide and should not be used to predict treatment effects.

General comments:

The current study tested research questions relevant for the study field. The analyses in two independent datasets with different routes of oxytocin administrations is the strength of current study. However, the limited novelty of findings and several limitations are noticed in the current report as described below.

Specific and major comments:

1) Previous study with similar results has already revealed that saliva oxytocin is a weak surrogate for plasmatic oxytocin, and increases in salivary oxytocin after the intranasal administration of exogenous oxytocin most likely represent drip-down transport from the nasal to the oral cavity and not systemic absorption (Quintana 2018 in Ref 13). Therefore, the novelty of current findings is limited. The authors should more clearly state the novelty of current results and the replication of previous findings.

We apologize for not describing the novelty and impact of our findings with sufficient clarity, and thanks for the opportunity to do so. Our study had two major goals. The first was to investigate whether single measurements of salivary and plasmatic concentrations of oxytocin can be reliably estimated within the same individual when collected at baseline conditions (i.e. without any experimental manipulation). As the reviewer highlighted, this is an important methodological question given the wide use of these measurements in a large and increasing number of studies to establish associations between the physiology of the oxytocin system and a number of brain and behavioural phenotypes in both clinical and non-clinical samples. However, to our knowledge, no previous study has appropriately conducted a thorough investigation of the reliability of these measurements (see also response to Reviewer 3, point 5). Thanks to our study, we now know that when single measurements are collected at baseline, salivary and plasmatic oxytocin cannot provide a sufficiently stable trait marker of the physiology of the oxytocin system in humans. As we highlight in the manuscript, this finding should deter the field from making strong claims based exclusively on associations of phenotypes with single measurements of peripheral oxytocin concentrations. Furthermore, our study also describes two very concrete implications of our findings which we believe are very important for the field. First, if baseline level of OT is to be used as a trait marker, future studies should, as much as possible, rely on repeated measures within the same participant but collected on different days to maximize reliability. Second, this less than perfect reliability should be taken into consideration when calculating the sizes of the samples needed to detect a certain effect, if it exists, with sufficient statistical power.

The second goal of our study was, as pointed out by the reviewer, to revisit the findings of Quintana et al. 2018(3), but this time with two major design modifications which could strengthen the conclusions from that study. The first modification was the dose of intravenous oxytocin administered, which was considerably higher (see response to Reviewer 1, point 2). The administration of a higher dose that resulted in substantial and sustained increases in plasmatic oxytocin throughout the two hours observation period can only strengthen the previous conclusion that increases in plasmatic oxytocin cannot be detected in salivary measurements, and that this is not a matter of dose (as far as we can ascertain by administering the maximum intravenous dose we could safely administer in healthy volunteers). We believe that this is an important addition to the literature.

The second modification regarded the choice of the method we used to quantify oxytocin. In this study, we used radioimmunoassay, which is superior to ELISA in sensitivity and hence more appropriate to measure the low concentrations of oxytocin in saliva and plasma typically detected in humans at baseline conditions (1-10 pg/ml; for most individuals 1-5 pg/ml)(6). For instance, in Quintana et al. 2018(3) the limitations in the sensitivity of the ELISA kit used led the authors to discard around 50% of the collected saliva samples. Hence, our study replicates and extends the previous findings from Quintana et al. 2018 in important ways, demonstrating that the lack of an association between increases plasmatic oxytocin and salivary measurements is not limited by the dose of intravenous oxytocin administered or limitations of the sensitivity of the method used to quantify oxytocin.

We have now made the novelty and contribution of our work more explicit:

*Line 77 “Currently, we lack robust evidence that single measures of endogenous oxytocin in saliva and plasma at rest are stable enough to provide a valid trait marker of the activity of the oxytocin system in healthy individuals. Indeed, previous studies have claimed within-individual stability of baseline plasmatic and salivary concentrations of oxytocin in both adults and children based on moderate-to-strong correlations between salivary and plasmatic oxytocin concentrations measured repeatedly within the same individual over time using ELISA in unextracted samples(14-16). However, these studies have a number of methodological limitations that raise questions about the validity of their main conclusion that baseline plasmatic and salivary concentrations are stable within individuals. First, measuring oxytocin in unextracted samples has been postulated as potentially erroneous, given the high risk of contamination with immunoreactive products other than oxytocin(4). It is conceivable that these non-oxytocin immunoreactive products might constitute highly stable plasma housekeeping proteins (17) that masked the true variability in oxytocin concentrations. Second, a simple correlation analysis cannot provide information about the absolute agreement of two sets of measurements – which would be a more appropriate approach to study within-subject reliability/stability. Third, it is not clear whether these findings generalize beyond the early parenting(14) or early romantic(15) periods participants were in when the studies were conducted, since these periods engage the activity of the oxytocin system in particular ways(18). Hence, establishing the validity of salivary and plasmatic oxytocin as trait markers of the activity of the oxytocin system in humans remains as an unmet need. Such evidence is urgently required, given reports that plasma and saliva levels of oxytocin are frequently altered during neuropsychiatric illness and that they co-vary with clinical aspects of disease(13).”

Line 509 “Our findings were not consistent with these expectations. We could replicate previous evidence that intravenous oxytocin does not increase salivary oxytocin(3) and extended it by showing that the lack of increase in salivary oxytocin is not limited to the specific low dose of intravenous OT that was previously used (1IU) and that it is not driven by the insufficient sensitivity of the OT measurement method (which had resulted in more than 50% of the saliva samples being discarded in the previous study(3).”*

2) As authors discussed in the limitation section of discussion, the current study has several limitations such as analyses only in male participants and non-optimized timing of collection of saliva and blood due to the other experiments. These limitations are understandable, because the current study was the second analyses on the data of the other studies with the different aims. However, these limitations significantly limit the interpretations of the findings.

Here, we would like to highlight two aspects. First, most studies in the field are indeed conducted in men to avoid potential confounding from fluctuations in oxytocin concentrations across the menstrual cycle in women. Therefore, our study is representative of the typical samples used in most human studies. Second, we did not optimize our study to collect repeated samples of saliva. Indeed, it would have been interesting to describe the full-time course of variations of oxytocin concentrations in saliva after intranasal and intravenous administration. However, this does not detract the importance of our findings in respect to our first aim (which was our main goal).

We agree with the reviewer though that it is at least theoretically possible that we could have missed the window for increases in salivary oxytocin after intravenous oxytocin if it existed, given that we only sampled one post-administration time-point. However, we believe this was unlikely for one reason. Despite the sustained increase (throughout the two-hour observation interval) in plasmatic oxytocin following the intravenous administration of oxytocin, we observed no increase in salivary oxytocin post-dosing (at ~115 min). Unless the half-life of oxytocin is shorter in saliva than in the blood (which we do not know yet), we expected the levels of salivary oxytocin to mirror the changes in plasma – potentially with a slight delay given the time that it might take for oxytocin concentrations to build up in saliva through ultrafiltration from the blood, but this was not the case. Most likely the half-life of oxytocin in the saliva is not shorter than in the blood, since a previous study found increased concentrations of oxytocin in saliva up to 7h after administration of intranasal oxytocin (as the reviewer pointed out below, in our study we no longer could detect significant increases in plasmatic oxytocin after the intranasal administration of 40 IU with two different methods at around 115 mins post-administration). Therefore, while we acknowledge these limitations we also believe they do not detract from the importance of our main findings and the potential they hold to influence the field towards a more rigorous use of these measurements. Please see below for the implemented changes in the text.

Line 554 “It is possible that we may have missed peak increases in saliva oxytocin after the intravenous administration of exogenous oxytocin if they occurred between treatment administration and post-administration sampling. This is unlikely given that the dose we administered intravenously resulted in sustained increases in plasmatic oxytocin over the course of two hours. Unless the half-life of oxytocin in saliva is much shorter than in the plasma, it would be surprising to not find any increases in salivary oxytocin after intravenous oxytocin given that concentrations of oxytocin in the plasma were still elevated at the specific time-point of our second saliva sample. Currently, we have no estimate for the half-life of oxytocin in saliva; however, given that previous studies have found evidence of increased salivary oxytocin after single intranasal administrations of 16IU and 24IU oxytocin up to seven hours post-administration(19), it is unlikely that the half-life of oxytocin is shorter in the saliva than in the plasma.”

3) As reported in page 6, the dataset A comprises administrations approximately 40 IU of intranasal oxytocin and 10 IU on intravenous. The rationale to set these doses should be described. Since the 40IU is different from 24 IU which is employed in most of the previous publications in the research field, potential influence associated with the doses should be tested and discussed.

Thank you for the opportunity to clarify this aspect of our work. With respect of our primary aims (to investigate whether single measurements of salivary and plasmatic oxytocin at baseline can be reliably measured within individuals across different days), the choice of doses is of course not relevant.

With respect to our secondary aim, namely, to investigate whether salivary oxytocin can be used to index concentrations of oxytocin in the plasma, particularly after the administration of synthetic oxytocin using the intranasal and intravenous routes, the administered doses are relevant.

The data reported here were collected as part of a larger project – which determined the choice of both intranasal and IV doses (2). As explained in our response to Reviewer 1, point 2, the selection 10IU (over 10min) was the highest intravenous dose that we could get permission to administer safely in healthy volunteers as a proof of concept, so as to achieve a robust and prolonged increase in plasmatic oxytocin over the course of our full testing session. In this manner, we demonstrate that even when plasmatic levels of OT are maintained substantially increased throughout the observation interval, we cannot detect increases in salivary oxytocin.

Regarding the intranasal OT dose, it is worth noting that the 24 IU is indeed popular in oxytocin studies, but not exclusive, and generally the selection of dose in oxytocin studies has not been informed by detailed dose-response characterizations. Our choice of 40IU was made for the purposes of matching our previous work on the pharmacodynamics of OT in healthy volunteers(20), and is a dose we (21-29) and others (e.g. (30)) have commonly used with patients.

A potentially important implication if dose variations also imply variation in the total volume of liquid administered (as is usually the case with standard nasal sprays – but not with the nebuliser), then it is likely that the potential for drip-down might increase for higher volumes and decrease for lower volumes. As far as we know, no study has ever investigated the impact of administered volume on salivary oxytocin after the intranasal administration of synthetic oxytocin, but we agree this would be an important point to look at. We have now expanded our discussion to accommodate this point.

Line 519 “We expect this phenomenon to be particularly pronounced for higher administered volumes. Further studies should examine the impact of different administered volumes on increases in salivary oxytocin.”

4) It is difficult to understand that no significant elevations in plasma oxytocin levels were observed after intranasal spray or nebuliser of oxytocin. From figure 4A, the differences between levels at baseline and post administration are similar between nebuliser, spray, and placebo. Please discuss the potential interpretation on this result.

The plasmatic concentrations of oxytocin we report in this study refer solely to the samples acquired at around 2h after the administration of intranasal oxytocin. We reported the full-time course of changes in plasmatic oxytocin in a paper published earlier this year(2) – which we now refer the reader to. We did find increases in plasmatic oxytocin after administration of oxytocin with the spray and nebuliser (around 3x the baseline concentrations) that did not differ between intranasal methods of administration. Plasmatic oxytocin reached a peak within 15 mins from the end of the intranasal administrations. Given the short half-life of oxytocin in the plasma, we believe it is not surprising that at 115 mins after the end of our last treatment administration the concentrations of oxytocin in the plasma are no longer different from the placebo condition.

Line 166 “The full time course of changes in plasmatic oxytocin after the administration of intranasal and intravenous oxytocin in this study has been reported elsewhere(2).”

5) In page 12, the reason why not to employ any correction for multiple comparisons in the statistical analyses should be clarified.

We apologize that this was not sufficiently clear, but we did correct for multiple testing using the Tukey procedure in our analyses investigating the effects of treatment on salivary and plasmatic oxytocin (this was described in page 9 – Treatment effects). If the reviewer meant something else, we would be glad to follow any further advice on multiple testing correction he/she might have.

Line 250 “Treatment effects: The effect of treatment on blood/saliva oxytocin concentration were assessed using a 4 x 2 repeated-measures two-way analysis of variance Treatment (four levels: Spray, Nebuliser, Intravenous and Placebo) x Time (two levels: Baseline and post-administration). Post-hoc comparisons to clarify a significant interaction were corrected for multiple comparisons following the Tukey procedure.”

Reviewer #3:

In the current study, baseline samples of salivary and plasma oxytocin were assessed in 13, respectively, 16 participants, to assess intra-individual reliability across four time points (separated by approximately 8 days). The main results indicate that, while as a group, average salivary and plasma samples were not significantly different across time points, within-subject coefficient of variation (CV) and intra-class correlation coefficient (ICC) showed poor absolute and relative reliability of plasma and salivary oxytocin measurements over time. Also no association was established between plasma and salivary levels, either at baseline or after administration of oxytocin (either intranasally, or intravenously). Further, salivary/ plasma oxytocin was only enhanced after intranasal, respectively intravenous administration.

The study addresses an important topic and the paper is clearly written. While the overall multi-session design seems solid, sample collections were performed in the context of larger projects and therefore there appear to be several limitations that reduce the robustness of the presented results and consequently the formulated conclusions.

General comments

1) A main conclusion of the current work is that 'single measures of baseline oxytocin concentrations in saliva and plasma are not stable within the same individual'. It seems however that the study did not adhere to a sufficiently rigorous approach to put forward this conclusion. It lacks a control for several important factors, such as timing of the day at which saliva/ plasma samples were obtained, as well as sample volume. Particularly while it is indicated that all visits were identical in structure, important information is missing with regard to whether or not sampling took place consistently at a particular point of time each day, to minimize the influence of circadian rhythm. Without this information it is not possible to draw any firm conclusions on the nature of the intra-individual variability as demonstrated in the salivary and plasma sampling.

Thanks for pointing this out. Indeed, we were not sufficiently explicit on how strict we were in controlling for some potential sources of variability that could have contributed to the lack of reliability we report here. Our data was acquired in the context of two human pharmacological studies, which by design were strict on a number of aspects to minimize unwarranted noise. All participants were tested in the same period of the day (morning) to avoid the potential contribution of circadian fluctuations of oxytocin. In dataset A, we tried, as much as possible, to match the exact time participants were tested between visits, using the start time of the first visit as a reference. With the exception of one participant, where one session was conduct 1h and 30 mins later than the other three, all the remaining participants from study A were tested within 1h of the exact start time of session 1. Further, we also instructed participants to abstain from alcohol and heavy exercise for 24 h and from any beverage or food for 2 h before scanning. Hence, we believe our sampling protocol was strict enough to discard any potential contribution of major known sources of variability in oxytocin levels.

The reviewer also inquiries about the volume of the samples. For the plasma samples, we used a standardized protocol and collected the same blood volume in all participants, visits and time-points (1 EDTA tube of approximately 4 ml). The saliva samples were collected using Salivettes. Participants were instructed to place the swab from the Salivette kit in their mouth and chew it gently for 1 min to soak as much saliva as possible. After this, the swab was then returned back to the Salivette and centrifuged. In both cases, to avoid degradation of the peptide in the collected sample, we followed a strict protocol where all samples were put immediately in iced water until centrifugation, which happened within 20 mins of sample collection. Samples were then immediately stored at -80C until analysis. Hence, differences in degradation of the peptide related to the processing of the sample are also unlikely to justify the poor reliabilities we report here.

For completeness, we have now added all of these further details to our Methods section.

Line 169 “**All visits were conducted during the morning to avoid the potential confounding of circadian variations in oxytocin levels(31, 32). In addition, we also made sure that each participant was tested at approximately the same time across all four visits (all participants were tested in sessions with less than one hour difference in their onset time, except for one participant where the difference in the onset of one session compared to the other three sessions was 1.5h). “*

Line 192 “Blood was collected in ethylenediaminetetraacetic acid vacutainers (Kabe EDTA tubes 078001), placed in iced water and centrifuged at 1300 × g for 10 minutes at 4°C within 20 minutes of collection and then immediately pipetted into Eppendorf vials. Samples were immediately stored -80C until analysis. Saliva samples were collected using a salivette (Sarstedt 51.1534.500). Participants were instructed to place the swab from the Salivette kit in their mouth and chew it gently for 1 min to soak as much saliva as possible. After this, the swab was then returned back to the Salivette, centrifuged and stored in the same manner as blood samples. For both saliva and plasma, we stored the samples in aliquots of 0.5 ml, following the RIAgnosis standard operating procedures. We followed this strict protocol, putting all samples in iced water until centrifugation with immediate storage at -80C until analysis to minimize the impact putative differences in degradation of the peptide related to differences in the processing of the samples might have on the reliability of the estimated concentrations of oxytocin.” *

Correspondingly, a deeper discussion is needed on the reason why ICC's were considerably variable across pairs of assessment sessions, with some pairs yielding good reliability, whereas others yielded (very) poor reliability.

Currently we have no insightful hypothesis on why this could have been the case. Indeed, we found higher ICCs for only 2 out of 6 pairs of visits for the plasma. However, it is plausible that this might have occurred by chance. In any case, we should note that the 95% confidence intervals for the ICCs of our different pairs of samples overlap; this suggests that there is no evidence that the ICCs we estimated for the specific two pairs where we found higher reliabilities are significantly higher than those observed in the remaining pairs.

Line 431 “If there are specific reasons explaining the higher reliability indices observed for the specific pairs of sessions, these reasons remain to be elucidated. However, it is not implausible that we might have found higher reliabilities for these specific two pairs by chance, since the 95% confidence intervals for the ICCs for all pairs of samples overlapped.”

More detailed descriptions regarding sampling procedures (timing and sampling intervals) are necessary. Also, more information is needed on the volume of saliva collected at each session, to control for possible dilution effects.

This information has been added to the revised version of the manuscript (please see response to your point number 1). As a further clarification, oxytocin concentrations were measured in plasma and saliva aliquots of 0.5 ml, following the standard operating procedures of RIAgnosis. This volume was used for all participants, sessions and time-points. Furthermore, for measuring cortisol, the salivettes were shown to allow for an almost 100% recovery, regardless of cortisol concentration, volume of the sample or method of quantification(33), suggesting that the sampling method is robust.

2) It is indicated that the initial sample would allow to detect intra-class correlation coefficients (ICC) of at least 0.70 (moderate reliability) with 80% of power. Is this still the case after the drop-outs/ outlier removals? Since the main conclusions of the work rely on negative results (conclusions drawn from failures to reject the null hypothesis) it is important to establish the risk for false negatives within a design that is possibly underpowered.

We understand the concern of the reviewer. However, according to the power calculations provided by Bujang and Baharum, 2017(34), the four repeated samples we collected in Dataset A would have allowed us to detect an ICC of 0.5 with 80% of statistical power even with only 13 subjects (which is the lowest sample size we used for the analysis on saliva in dataset A). The two samples we collected in Dataset B would allow us to detect an ICC of 0.6 with 80% of statistical power even with only 19 subjects. Hence, both datasets were powered to detect an ICC of 0.7 with acceptable power, if it existed, even after the exclusion of outliers.

3) Did the authors also assess within-session reliability? For example, by assessing ICC between pre and post-measurements in the placebo session.

Thanks for the suggestion. Indeed, we had not performed this analysis before but we agree it would be informative. We calculated the ICC and CV for the two samples acquired before any treatment administration and the intravenous infusion of saline during the placebo session. These samples where acquired with an approximate 15 min interval in between them. In this analysis, we found that the ICC was excellent 0.92 and the CV 20%. This additional analysis strengthens our findings by supporting the idea that our poor reliabilities across different days reflect true biological variability and cannot be attributed to measurement error. These new findings have now been included in the revised version of the manuscript.

Abstract

Line 44 "Results: Single measurements of plasmatic and salivary oxytocin showed poor reliability across visits in both datasets. The reliability was excellent when samples were collected within 15 minutes from each other in the placebo visit.”

Line 240 “Within-visit reliability analysis: To investigate the reliability of salivary and plasmatic oxytocin concentration within the same visit, we calculated the ICC and CV as described above for two samples acquired before any treatment administration and the intravenous infusion of saline during the placebo session. These samples where acquired with an approximate 15 minutes interval in between them.”

Line 405 “Furthermore, in a further analysis assessing the within-session stability of plasmatic oxytocin using two measurements collected 15 minutes apart from each other in the placebo visit (one sample collected at baseline and the other after the intravenous administration of saline), we found excellent within-session reliability (ICC=0.92, CV=20%). Together, this suggests that the low reliability of endogenous oxytocin measurements across visits in the current study results from true intrinsic individual biological variability and not technical variability/error in the method used for oxytocin quantification.“*

4) It is indicated that the intra-assay variability of the adopted radioimmunoassay constitutes <10%. Were analyses of the current study run on duplicate samples? Was intra-assay variability assessed directly within the current sample?

We reported the intra-assay variability determined by RIAgnosis during the development of this assay(35). This was not specifically assessed for the current study.

Introduction & Discussion

5) The introduction and discussion is missing a thorough overview of previous studies assessing intra-individual variability in oxytocin levels.

Thanks for the suggestion. We have now included in our introduction/discussion an overview of previous studies attempting to tackle this question, which unfortunately do not address this question with sufficient detail or using the appropriate methods and statistical analyses (see response to Reviewer 2, point 1). Hence, from the available evidence, it is not possible to draw robust conclusions about the validity of concentrations of oxytocin in saliva and plasma as valid trait markers of the activity of the oxytocin system. With this manuscript, we hope we can prompt further discussion and guide the field towards a more rigorous use of these measurements. A thorough discussion of this literature has now been added to the Introduction and Discussion.

Line 434 “Our observation of poor reliability questions the use of single measurements of baseline oxytocin concentrations in saliva and plasma as valid trait markers of the physiology of the oxytocin system in humans. Instead, we suggest that, at best, these measurements can provide reliable state markers within short time-intervals (5 mins in our study). Our data does not support previous claims of high stability of plasmatic and salivary oxytocin within individuals over time. For instance, in one study, Feldman et al. (2013) assessed plasmatic oxytocin in recent mothers and fathers at two time-points spaced six months apart during the postpartum period. The authors found strong correlations between the two assessments for both mothers and fathers(14). In another study, Schneiderman et al. (2012) found strong correlations between plasmatic oxytocin concentrations measured at two different instances spaced six months apart in both single and individuals recently involved in a new romantic relationship(15). Two important differences between these studies and ours are i) the method used for oxytocin quantification, and ii) the particular states participants were in when the studies were conducted. Regarding the first difference, these previous studies used ELISA without extraction, reporting concentrations of plasmatic oxytocin well above the typical physiological range of 1-10 pg/ml detected in extracted samples (in their studies, the authors report concentrations above 200 pg/ml). The inclusion of extraction has been postulated as a critical step for obtaining valid measures of oxytocin in biological fluids(4). Unextracted samples were shown to contain immunoreactive products other than oxytocin(4), which contribute largely to the concentrations of oxytocin estimated by this method. It is possible that these non-oxytocin products might represent highly stable plasma housekeeping molecules(17) that masked the true biological variability in oxytocin concentrations between assessments in these previous studies that we could detect in extracted samples in our study. Regarding the second difference, these previous studies on within-individual stability were conducted during the early parenting(14) or early romantic(15) periods, which engage the activity of the oxytocin system in particular ways(18). Instead, we used a normative sample that did not specify these inclusion criteria. Hence, we cannot exclude that during these specific periods the reliability of salivary and plasmatic oxytocin concentrations might be higher. We note though that our sample more closely resembles the samples used the vast majority of studies in the field (which sometimes even exclude participants during early parenthood(36)). Hence, our estimates of reliability are a better starter point for all studies where specific circumstances potentially affecting the activity of the oxytocin system have not been specified a priori.”

6) The paper misses a discussion of previous studies addressing links between salivary/ plasma levels and central oxytocin (e.g. in cerebrospinal fluid). I understand the claim that salivary oxytocin cannot be used to form an estimate of systemic absorption, although technically, a lack of a link between salivary and plasma levels, does not necessarily imply a lack of a relationship to e.g. central levels. The lack of effect is limited to this specific relationship.

In this study, we did not intend to investigate whether salivary and plasmatic oxytocin are valid proxies for the activity of the oxytocin system in the brain. Our data does not address that question and a thorough discussion of these studies falls, in our opinion, out of the scope of the manuscript. Instead, we focused on whether measurements of oxytocin in saliva and plasma (by far the most commonly used biological fluids to measure oxytocin) are sufficiently stable to provide valid indicators of the physiology of the oxytocin system in humans. Additionally, we also investigated whether salivary oxytocin can index plasmatic oxytocin at baseline and after the administration of synthetic oxytocin using different routes of administration.

A previous meta-analysis of studies correlating peripheral and CSF measurements of oxytocin has shown that most likely peripheral and CSF measurements do not correlate at baseline; significant correlations could be found after intranasal administration of oxytocin or specific experimental manipulations, such as stress(37). We believe that currently we still do not have a clear answer about the extent to which these peripheral fluids can actually index oxytocin concentrations in the brain (even if associations with CSF are evident in specific instances). For instance, no study has ever shown that CSF oxytocin actually predicts the concentrations of oxytocin in the extracellular fluid of the brain. Given what we currently know about the synaptic release of oxytocin in the brain(38) (in contrast with former theories of exclusive bulk diffusion in the CSF(39)), we think we have good reasons to suspect this might not be the case.

The only contribution our study can make in that respect is highlighting our current lack of understanding of how oxytocin reaches saliva if not from the blood. Currently there is no evidence of direct secretion of oxytocin to the saliva (not from acinar secretion or nerve terminals release). Hence, as it stands, the most likely mechanism for oxytocin to entry the saliva is from the blood (for instance, by ultrafiltration). If increases in plasmatic oxytocin after intravenous oxytocin cannot produce any significant increases in salivary oxytocin (shown in ours and in a previous study), how does oxytocin reach the saliva and why might it be able to predict concentrations in the CSF, if it does? In this respect, we hope our study highlights the need for further research shedding light on the mechanisms underlying these potential saliva – CSF relationships, if they exist. We would be glad to accommodate any other hypothesis the reviewer might have on this respect.

Line 522 “The lack of increase in salivary oxytocin after the intravenous administration of exogenous oxytocin that was consistently found in our study and in a previous study(3) also raises the question of how oxytocin reaches the saliva if not from the blood. Currently there is no evidence of direct acinar secretion or direct nerve terminals release of oxytocin to the saliva; therefore, transport from the blood remains as the most plausible mechanism of appearance of oxytocin in the saliva. Clarifying these mechanisms of transport is paramount, given the current hypothesis that salivary oxytocin might be superior to plasma in indexing central levels of oxytocin in the CSF(40).”

Methods

7) Related to the general comment, the variability in days between sessions is relatively high (average 8.80 days apart (SD 5.72; range 3-28). However, it appears that no explicit measures were taken to control the conducted analyses for this variability.

Thanks for point this out. Indeed, we were not sufficiently thorough in exploring the impact of this potential variability in the time gap between visits on our estimated ICCs. Thanks to the reviewer we now acknowledged this limitation of our analysis and decided to explore this further. We decided to run the following sensitivity analysis. First, we went back to our dataset A and identified all pairs of consecutive measures that were collected with an exact time interval of 7 days between visits. We could retrieve 15 examples of these pairs from 15 different participants for both saliva and plasma. Then, we recalculated the ICC and CV on this subset of our initial sample. In line with our main analysis, we found poor reliabilities for both salivary and plasmatic oxytocin; in both cases the ICCs were not significantly different from 0 and the CVs were 49% and 40%, respectively. This further analysis has been added to the revised version of the manuscript. We hope the reviewer shares our vision that our main conclusion of poor reliabilities of single measurements of baseline oxytocin in saliva and plasma cannot be simply attributed to the variability in the number of days between visits.

Line 229 “Since there was considerable variability in the time-interval between visits across participants, we conducted a sensitivity analysis where we repeated our reliability analysis focusing on 15 pairs of consecutive measures that were collected with an exact time interval of 7 days between visits in 15 participants. Here, we recalculated the ICC and CV on this subset of our initial sample, using the approach described above.”

Line 399 “These poor reliabilities are unlikely to be explained by variability in the time-interval between visits of the same individual, since we also found poor reliability indexes for both saliva and plasma when we restricted our analysis to a subset of our sample controlling for the exact number of days spacing visits.”*

8) A rationale for the adopted dosing and timing (115 min post administration) of the sample extraction is missing. Additionally, it seems that intravenous administrations were always given second, whereas intranasal administrations were given third, with a small delay of approximately 5 min. Hence, it seems that the timing of 115 min post-administration is only accurate for the intranasal administration.

We collected saliva samples before any treatment administration and after the end of our scanning session (collection of saliva samples in between was just not possible because the participants were inside the MRI machine and could not have moved their heads). For the plasma, we collected samples before any treatment administration, after each treatment administration and at other five time-points during the scanning session. Here, we only report the plasma data that was acquired concomitantly with the saliva samples (the full-time course of plasma changes in plasmatic oxytocin has been reported elsewhere(2)). In the manuscript, we report post-administration times from the end of the full treatment administration protocol. Hence, as the reviewer highlights our post-administration sample was collected at around 115 mins from the last intranasal administration and 120 mins from the end of the intravenous administration. We have now made this aspect explicit in the revised version of the manuscript.

Line 162 “For the purposes of this report, we use the plasmatic and salivary oxytocin measurements that were obtained at baseline and at 115 minutes after the end of our last treatment administration (this means that our post-administration samples were collected 115 mins after the intranasal administrations and 120 mins after the intravenous administration of oxytocin).”

9) Since the ICC of baseline samples showed poor reliability, it seems suboptimal to pool across sessions for assessing the relationship between salivary and blood measurements. It should be possible to perform e.g. partial correlations on the actual scores, thereby correcting for the repeated measure (subject ID). Further, since the sample size is relatively small (13 subjects), it might be recommended to use non-parametric (e.g. Spearmann correlations) instead of Pearson. The additional reporting of the Bayes factor is appreciated; it is very informative.

Thanks for the suggestion. In fact, for the correlation the reviewer mentions we indeed used a multilevel approach where we specified subject as a random effect (please see pages 9-10). This allowed us to deal with the dependence of measurements coming from the same subject in different visits. Furthermore, since we also had concerns about the sample size, we calculated Pearson correlations but used bootstrapping (1000 samples) to obtain the 95% confidence intervals and assess significance. Bootstrapping is a robust statistical technique which allows significance testing independently of any assumptions about the distribution of the data and is robust to outliers. Please see page 12 of the manuscript, section “Association between salivary and plasmatic oxytocin levels”.

10) Now, the authors only compared relationships between salivary and plasma levels, either at baseline or post administration. I'm wondering whether it would be interesting to explore relationships between pre-to-post change scores in salivary versus plasma measures.

Thanks for the suggestion. We have now conducted this further analysis and we could not find any significant correlation between changes from baseline to post-administration in any of our treatment conditions. As for our other correlation analyses, here we also conducted Bayesian inference, which supported the idea that the null hypothesis of no significant correlation between changes in saliva and plasma from baseline to post-administration is at least 4x more likely than the alternative hypothesis. This further analysis strengthens our confidence that changes in salivary oxytocin after administration of oxytocin using the intranasal and intravenous routes should not be used to predict systemic absorption to the plasma.

Line 260 “*As a final sanity check, we also investigated correlations between the changes from baseline to post-administration in saliva and plasma in each of our treatment conditions separately.”

Line 485 “Furthermore, we could not find any significant correlation between changes in salivary or plasmatic oxytocin from baseline to 115 mins after the end of our last treatment administration in any of our four treatment conditions. The lack of significant associations between salivary and plasmatic oxytocin (and respective changes from baseline) was further supported through our Bayesian analyses which demonstrated that given our data the null hypotheses were at least three times more likely than the alternative hypothesis.”*

11) Please provide more information on the outlier detection procedure (outlier labelling rule).

This information has now been added to the revised version of the manuscript.

Line 271 “Outliers were identified using the outlier labelling rule(41); this means that a data point was identified as an outlier if it was more than 1.5 x interquartile range above the third quartile or below the first quartile.”*

12) Please indicate how deviations from a Gaussian distribution were assessed.

We used the combined assessment of i) differences between mean and median; ii) skewness and kurtosis; iii) histogram; iv) Q-Q plots; and v) the Kolmogorov-Smirnov and Shapiro-Wilk normality tests. Deviations from a normal distribution is common in the concentration of several analytes in the saliva (42), including oxytocin (15); hence, following the current recommendations, we used log transformations of the raw concentrations but plot the raw concentrations to facilitate the interpretation of our plots.

Results

13) Please verify the degrees of freedom for the post-hoc tests performed to assess pre-post changes at each treatment level (e.g. baseline vs Post administration: Spray - t(122) = 7.06, p < 0.001) . Why is this 122? Shouldn't this be a simple paired-sample t-test with 13 subjects?

We apologize for this oversight. Indeed, we did a mistake in copying the values of the degrees of freedom from SPSS. We have now corrected these values. All the other p-values and F or T values were reported correctly and hence are not changed in the revised version of the manuscript (please see also response to Reviewer 1, question 4 regarding inconsistencies in the reported p-values).

Note: This rebuttal was posted by the corresponding author to Review Commons. Content has not been altered except for formatting.

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Reply to the reviewers

Please note that the authors have provided a formatted PDF version of this rebuttal, including additional figures and references, via the Open Science Framework: https://osf.io/5acqp/

Reviewer #1

This is an interesting and thorough study characterising human iPSC with hetero or homozygous mutation in pi3k pathway that lead to its hyper-activation. They prove that the increased stemness results from enhanced autocrine responsiveness to TGF signalling pathway. The main conclusions are well supported by the presented data. Cutting edge tools and bioinformatic analysis are adequately applied. I have only one important point:

1) Western blot based validation of TGF pathway activation in wt and mutant iPSCs will be helpful to strengthen the results based on bioinformatic data.

AUTHORS’ RESPONSE__:__ We thank the Reviewer for the positive evaluation of our work.

Functional validation of the signalling hypothesis is indeed important, and we did in fact already present supportive data. Current evidence suggests that SMAD2 is the main transcription factor mediating actions of the TGFb/NODAL pathway in an early developmental context [1,2], and we have shown increased phosphorylation of SMAD2 (S465/S467) in PIK3CAH1047R/H1047R iPSCs using RPPA in the two datasets shown in Fig.2.

We have attempted to demonstrate increased NODAL protein directly in PIK3CAH1047R/H1047R cells, but have been unsuccessful due to poor signal on immunoblotting. We thus opted for functional testing of our hypothesis using the experiment presented in Fig. 5, wherein TGFb (a surrogate for NODAL) is removed from the culture medium. Human iPSCs depend strictly on TGFb/NODAL for maintenance of NANOG expression and thus pluripotency [3,4]. Upon exclusion of TGFb/NODAL from the culture medium of normal human iPSCs, the early responses (prior to overt differentiation) are expected to be: (A) decreased NODAL expression, due to well-established autoregulation [2], then (B) a decrease in NANOG and ultimately POU5F1 (OCT3/4) mRNA levels (see also Introduction, lines 80-90). The evidence in Fig. 5 that PIK3CAH1047R/H1047R fail to exhibit these responses upon exogenous TGFb/NODAL removal supports the notion that these cells autonomously sustain TGFb/NODAL signalling.

For improved clarity, we have also added the following information to the revised manuscript:

lines 202-205: “This is consistent with strong NODAL mRNA upregulation and increased pSMAD2 (S465/S467) in PIK3CAH1047R/H1047R iPSCs in the current study (Dataset S2 and RPPA data in Fig. 2, respectively), and with prior evidence of activation of the NODAL/TGFb pathway in homozygous PIK3CAH1047R iPSCs.”

Reviewer #2

In this manuscript, Madsen et al have investigated the role of heterozygous versus homozygous PIK3CAH1047R gain-of-function mutation at maintaining stemness of induced pluripotent stem cells (iPSCs). The authors have performed high-depth RNAseq, proteomic, and RPPA analyses to show that biallelic PIK3CA alterations induce stronger activation of the PI3K signaling axis, compared to monoallelic mutations. The authors claim that a higher PI3K signaling dose activates the NODAL/TGF-b pathway, which in turn supports stemness in an autocrine fashion. These are important findings, however, the manuscript and its conclusions can be improved.

AUTHORS’ RESPONSE__:__ We thank the Reviewer for acknowledging the importance of the work and for their constructive suggestions for improvements.

The authors have described the role of PIK3CAH-1047R gain-of-function mutation in cancer and overgrowth syndromes. However, cancer associated somatic mutations in PIK3CA are mostly heterozygous. Similarly, PIK3CA related overgrowth syndromes (PROS) are caused by post-zygotic mosaic PIK3CA activating mutation. As such, the relevance of homozygous PIK3CA alterations to these pathological conditions is unclear. The authors should elaborate on the biological implications of their findings.

AUTHORS’ RESPONSE__:__ We disagree with the Reviewer’s comment which implies that homozygous PIK3CA mutations are not relevant to many cancers. In our previous work [5], we provided evidence that many human cancers harbour multiple PIK3CA mutant alleles. Specifically, among cancers with a unique PIK3CA mutation, approximately 50% exhibit multiple copies according to allele copy number analysis. We further demonstrated that a substantial proportion of cancers have multiple different PIK3CA variants or additional oncogenic ‘hits’ within the pathway. These findings have been supported by other recent high-profile papers [6–8]. Such multiple alterations increase activity of the PI3K pathway beyond the level seen with heterozygosity alone [5,6]. This substantial body of literature renders our PIK3CAH1047R iPSC model system highly relevant for studying disease-relevant, dose-dependent oncogenic PIK3CA activation.

The Reviewer is correct, however, that PROS is caused by postzygotic heterozygous PIK3CA mutations almost exclusively. Observations in homozygous cells are therefore not directly relevant to the pathogenesis of PROS. On the other hand, the heterozygous cells are closely relevant, being human, carefully matched with isogenic controls, and unperturbed by further manipulations such as artificial immortalisation. Our prior studies demonstrated no clear phenotypes in heterozygous cells in the iPSC differentiation paradigm, despite the rock solid causal nature of heterozygous mutations in PROS. This negative finding, surprising given the dramatic PROS phenotypes, is very important in understanding how best to create disease-relevant PROS models. One intent of the current study was to increase the sensitivity of our transcriptomic analysis, and to combine this with proteomic studies to determine if heterozygous cells really do not exhibit a phenotype. We now show that there are indeed faint echoes in heterozygous cells of the dramatic changes in homozygous cells. We believe that the human growth phenotype is a summative consequence of such small differences in growth behaviours sustained over months and years, highlighting how subtle difference in signalling can lead to dramatic human growth consequences across the lifecourse. Similar observations were also recently made following systematic analyses of oncogenic RAS mutations [9]. The new information we present about heterozygous PIK3CAH1047R cells, while much less “showy” than the cancer-relevant behavious of homozygous cells, we thus contend is very important for understanding of the PROS phenotype and its experimental modelling. To emphasise this point, we have added the following statements to the abstract and discussion, respectively.

• lines 56-57: “This work illustrates the importance of allele dosage and expression when artificial systems are used to model human genetic disease caused by activating PIK3CA mutations.”
• lines 104-106: “We discuss the implications of our findings for understanding and modelling developmental disorders and cancers driven by genetic PI3K activation.”
• lines 333-340: “Finally, our observations are important for future studies seeking to model human PIK3CA-related diseases. The modest changes observed in heterozygous PIK3CAH1047R cells, in sharp contrast to the radical transcriptional alterations in homozygous cells, emphasise the importance of careful allele dose titration when artificial overexpression systems are used to model disorders caused by genetic PIK3CA activation. Our findings in heterozygous cells are also a reminder that very small effect sizes in cellular systems may summate and result in major human phenotypes over a life course. That such minor changes are found in a cellular study of a rare and severe disorder emphasises the challenges of modelling much more subtle disease susceptibility conferred by GWAS-detected genetic associations, where cellular effect sizes are likely to be smaller still.”

  The role of biallelic PIK3CA mutation is reminiscent of compound mutations in PIK3CA which have also been shown to increase PI3K signaling output. However, double PIK3CA mutations confer enhanced sensitivity to PI3K inhibition (Toska et al. Science 2019). Could the authors kindly speculate on this discrepancy.

AUTHORS’ RESPONSE: We emphasise first that PIK3CAH1047R/H1047R cells do respond to BYL719 at the signalling level, as demonstrated previously [5] and in the manuscript (revised Figure S5; see also additional Western blot below). Our point is that the cells have undergone a switch to self-sustained stemness. That is, while PIK3CA activation was the driver of the initial change in cell state, the induced stemness phenotype is no longer reversed by removal of that trigger, with our data suggesting that this is now driven by self-sustained TGFb/NODAL signalling. This is in line with the role of this pathway in the maintenance of the pluripotent state. We speculate that this may be important in a cancer context where surviving stem cells may permit cancer persistence after toxic therapies, even if short term growth of tumours is reduced by agents such as PI3K inhibitors.

Our data are not directly comparable to prior cellular data, for example in Vasan et al. [6], due to: (a) use of different cell model system and (b) assessment of different functional responses. We would also sound some methodological notes of caution re some of the prior studies alluded to, as potentially confounding differences in growth rate in the cells studied was not corrected for. It is well-established that IC50 and Emax values depend on cell division rates, and failure to correct for this can result in artefactual correlations between genotype and drug sensitivity (see, e.g., Hafner et al. Nature Methods 2016: “Growth rate inhibition metrics correct for confounders in measuring sensitivity to cancer drugs” [10]**).

Similarly, the p110 alpha specific inhibitor, alpelisib, is highly effective against PIK3CA-mutant ER+ breast cancer and PROS. As such, the clinical relevance of the insensitivity of homozygous PIK3CA mutation to PI3K inhibitors is unclear.

AUTHORS’ RESPONSE__:__ Efficacy of Alpelisib in PROS is currently supported only by unregistered observational studies, but is nevertheless striking. It is not relevant to our findings in homozygous cells, as the Reviewer has previously observed, however.

As for cancer, in a randomised phase 3 trial that compared Alpelisib/BYL719 with fulvestrant to fulvestrant alone, the overall response (irrespective of PIK3CA mutant status) was indeed greater with the combination treatment (26.6 % vs 12.8 %), with a hazard ratio of 0.65 (95% CI, 0.5 to 0.85) in patients with PIK3CA-mutant caners versus a hazard ratio of 0.85 (95% CI, 0.58 to 1.25) in those without a PIK3CA mutation [11]. This trial demonstrated the utility of additional PIK3CA mutant-centric stratification, but a substantial proportion of patients with PIK3CA-mutant tumours (>50%) did not benefit from the BYL719 and fulvestrant combination [11]. However, these observations are not directly relevant to this manuscript and are instead included in a separate manuscript focused on PI3K signalling and stemness in human breast cancers (preprint [12]**).

Figure 2: The authors have performed RPPA analysis in the presence of 100 nM BYL719. Alpelisib is commonly used at 1 uM concentration for in-vitro experiments, and has a cMax of ~5 uM. We suggest the authors perform western blot analysis to confirm the results of RPPA.

AUTHORS’ RESPONSE__:__ We carefully chose the optimal concentration of BYL719 to preserve inhibitor selectivity, and to avoid undue toxicity and confounding off-target effects, rather than copying the dose “commonly used”. The Cmax is not relevant to our use of BYL719 in the current study as a precise tool compound. We refer the Reviewer to the known pharmacological characteristics of this compound [13,14]. According to available evidence, it is only a selective PI3Kα inhibitor at concentrations 250 nM (Table below adapted from Ref. **[13]; for formatted version, please see PDF version: https://osf.io/ecmhr/)

Enzyme

In vitro IC50 for NVP-BYL719 (nM)

PI3Kα

4.6 +/- 0.4

PI3Kα-H1047R

4.8 +/- 0.4

PI3K**b

1156 +/- 77

PI3K**d

290 +/- 180

PI3K**g

250 +/- 140

PI4K**b

571 +/- 42

We have previously demonstrated (Fig. 2C in Ref. [5]) that 100 nM BYL719 is sufficient to restore pAKT (S473) levels in both heterozygous and homozygous PIK3CAH1047R to levels observed in WT cells. This is consistent with the RPPA data reported in the current work (Fig. 2B). Of note, while 500 nM BYL719 completely ablates pAKT irrespective of genotype, we previously noted substantial toxicity [5], precluding use of this or higher doses of BYL719 in our model system. This is in line with a recent Nature Cell Biology study by Yilmaz et al. ([15]) which demonstrated the essential growth-promoting role of the PI3K pathway in human pluripotent stem cells; Yilmaz et al. also demonstrate that compared to somatic cells (fibroblasts), human pluripotent stem cells suffer dramatic effects on growth/survival in response to Torin1/rapamycin [15], overall suggesting that this cell type is exquisitely sensitive to inhibition of the PI3K/AKT/mTOR pathway.

In the present study we have also confirmed that 250 nM BYL719, used for Fig. 5 experiments, has worked as expected at the level of pAKT (S473) as shown in the below Western blot (see also revised Fig. S5; please access PDF version to view Western blot: https://osf.io/ecmhr/)

Figures 3 and 4: The authors should expand their RNAseq analysis to demonstrate enrichment of stemness and TGFb signaling in homozygous mutant cells compared to heterozygous cells.

AUTHORS’ RESPONSE__:__ We thank the Reviewer for this suggestion. The unsupervised MDS plot (Fig. 1A) clearly demonstrates the overlap between wild-type and heterozygous cells, strongly suggesting functional concordance and consistent differences to homozygous counterparts. Indeed, the below count table illustrates that the majority of differentially expressed genes in homozygous versus wild-type cells are also differentially expressed in homozygous versus heterozygous cells, including the direction of the change (please access the PDF version for formatted table: https://osf.io/ecmhr/)

Comparison

Differentially expressed gene count

HOMvsWT

5644

HOMvsHET

5764

HOMvsWT AND HOMvsHET

4825 (2300 upregulated; 2525 downregulated; 1 discordant)

We have now performed additional fast gene set enrichment analyses (fgsea; shown below - please access PDF version to view figure: https://osf.io/ecmhr/) using the R package fgsea ([16]) and 14 of the Broad Institute’s 50 Hallmark Gene Set Collection [17], including manual addition of the PLURINET signature [18]. The 14 gene sets were chosen based on their relevance to answering the Reviewer’s question as well as their connection to PI3K signalling. Fold changes for all expressed genes were included in the analyses, without further thresholding in order to minimise bias.

The results for homozygous vs wild-type comparisons are concordant with our upstream regulator analyses using IPA; as expected, TGFb signalling and PI3K signalling are among the top positively enriched (NES > 1) in comparison between homozygous and heterozygous cells. Unsurprisingly, however, the strength of the enrichments are lower when comparing the two PIK3CAH1047R genotypes.

We are not convinced that including these surplus data will add value to the manuscript and its main message, however we will leave this decision to the discretion of the Editor (please also refer to our response to the subsequent question from Reviewer 2). Moreover, these data will remain visible in the publicly available rebuttal document.

The authors should confirm the results of pathway analysis in vitro to show that homozygous PIK3CA mutation confers increased stemness compared to heterozygous mutation.

AUTHORS’ RESPONSE__:__ This was a key finding in our previous publication [5]. The aim of the current study was to interrogate this phenomenon further through high-depth transcriptomic/signalling analyses.

Figure 5: Kindly provide direct evidence demonstrating that increased PIK3CA signaling output induces NODAL expression in this experimental setting.

AUTHORS’ RESPONSE__:__ We have consistently demonstrated increased NODAL mRNA expression (RNAseq data, Fig. S4 and Ref. [5]). Unfortunately, we have been unsuccessful in attempts to obtain good quality immunoblots for NODAL protein in PIK3CAH1047R/H1047R cells (as noted in response to Reviewer 1). We note, in fact, that such documentation of NODAL protein levels, while not unprecedented, is fairly rare.

Also, please normalize gene expression data to WT cells so it is easy to visualize the changes in NODAL and NANOG expression in homozygous and heterozygous mutants compared to WT iPSCs.

AUTHORS’ RESPONSE__:__ It is arithmetically more precise to normalise to the highest expression (i.e. that of PIK3CAH1047R/H1047R cells) – thereby avoiding artificial inflation of fold-changes when normalising to very low levels of expression. Ultimately, the relative levels calculated – and the increased expression of NODAL in PIK3CAH1047R/H1047R cells – are identical visually. Only the entirely arbitrary units change. Thus we do not deem normalisation to WT to be necessary or to add value to the analysis.

Kindly quantify Fig. S5.

AUTHORS’ RESPONSE__:__ These brightfield micrographs were taken as part of routine practice to monitor cell health during maintenance and experimentation, and are suboptimal for direct quantitation due to uneven illumination background and lack of whole-well imaging. Nevertheless, we have now undertaken quantification as the Reviewer suggests, using individual images taken during independent experimental replicates. The results have been added to Fig. S5 and support our assertion that 250 nM BYL719 had a growth inhibitory effect in homozygous PIK3CAH1047R iPSCs. All raw images and associated data have been uploaded to the Open Science Framework (https://osf.io/hbf7x/). The following short method section detailing the image analysis algorithm has also been included in the revised supplementary material:

“Colony size quantitation from light micrographs

Routine cell culture light micrographs were acquired on an EVOS FL digital inverted microscope (AMF4300, Thermo Fisher Scientific) using the 4X or 10X objective (final magnification 40X and 100X, respectively). For quantitation, 4X images were used for colony segmentation with Definiens Developer XD software. Background was detected using a contrast threshold; for this each pixel was compared to those in the surrounding 24 pixels (i.e. a 5x5 pixel box), and pixels with low contrast (between -50 and +50) were classified as background. Remaining pixels were classified as colonies, and any holes (pixels that were not initially classified as being part of the colony due to low contrast) were filled. Edges of the resulting colonies were smoothened by shrinking and then growing the colonies by 2 pixels. Finally, colonies less than 2000 pixels in size were reclassified as background. The area of the resulting colonies could then be measured and averaged over each field of view.”

Reviewer #3

In this manuscript by Madsen et al., a comparison of the transcriptome and proteome in heterozygous and homozygous PIK3CAH1047R human pluripotent stem cells mutants is presented. The authors demonstrate marked alterations in expression at both the protein and RNA level of homozygous mutants compared to wildtype, while heterozygous lines exhibit only minor changes. Multiple analytical approaches are employed to investigate network alterations, leading the authors to suggest a TGFβ-mediated rewiring of key pluripotent genes to induce a state of sustained stemness. Madsen et al. conclude with a set of experiments to functionally implicate NODAL/TGFβ autocrine signalling in PIK3CAH1047R dose-dependent stemness. The key conclusions are not convincing. While the unbiased omics approach sets up this study well, the study suffers from a lack of convincing functional assays (cell biological assays) to test their model and tease apart a phenotype for the het cells. More robust functional experiments are required to support the finding the NODAL/TGFβ signalling mediates the self-sustained stemness, particularly because this is the major novel finding distinguished from the authors previous work.

AUTHORS’ RESPONSE__:__ We thank the Reviewer for their detailed critique. Our perspective on the robustness and novelty of our findings diverges from that of the Reviewer, however, as we elaborate on in more detail below.

While the authors present a comprehensive omics investigation into alterations between wild type, homozygous, and heterozygous mutants, the critical functional experiments are lacking. In Figure 5, the authors seek to support the role of TGFβ in mediated stemness in the homozygous mutants, however, are not able to directly deplete TGFβ due to technical limitations of the culture conditions. Consequentially, the experiments are primarily built on the use of NODAL withdrawal and stimulation. The data presented thus implicate NODAL in the stemness phenotype, but it's not obvious TGFβ is substantially involved, particularly considering the inhibitor subsequently employed also inhibits NODAL type 1 receptors.

AUTHORS’ RESPONSE__:__ NODAL and TGFb activate shared signalling pathways downstream from their respective receptors, and indeed they (as well as Activin) can be used interchangeably in stem cell culture, which is common practice [19–21]. Commercially available Essential 8/TeSR-E8 is supplemented with TGFb not NODAL; therefore the factor we have removed is TGFb, prior to any controlled introduction of NODAL (based on strong upregulation of its mRNA in PIK3CAH1047R/H1047R). Any residual TGFb-like ligands will be contributed by Matrigel as outlined in the text (lines 247-251). It is well-established that “NODAL/TGFb signalling” denotes signalling through SMAD2/3/4 (as opposed to BMP signalling through SMAD1/5/8), and this is how we use the term throughout the manuscript. Accordingly, it is functional activation of the “NODAL/TGFb signalling pathway” that we investigate (see also response to Reviewer 1, p.1).

In summary, we seek not to make a distinct point about TGFb, but rather refer to NODAL/TGFb signalling as a matter of biochemical correctness. For clarity, we now replace mentions of “TGFb signalling” with “NODAL/TGFb signalling” throughout the revised manuscript. We have also revised the legend for Figure 3 to make this clearer.

Furthermore, there is a paucity of readouts for stemness. For example, a more convincing narrative would include additional expression markers of the core pluripotency network (e.g. OCT4, SOX2, etc.) as well as functional readouts (e.g. NODAL withdrawal and assessment of differentiation) after NODAL stimulation/depletion and comparing across genotypes. Overall, the primary conclusions of this work are not well-evidence by the presented data and the authors should consider additional functional experiments or reframing the narrative.

AUTHORS’ RESPONSE__:__ We chose the current strategy because we wanted to capture the earliest changes after depletion of NODAL/TGFb/ signalling, prior to any signalling rewiring triggered by differentiation. In fact, we believe that a strength of this study is our observation of differences in critical stemness markers in spite of the short time course. To aid non-expert readers we offered a primer on stemness genes and rationale for the markers chosen in the existing introduction (lines 80-90).

We have further assessed additional stemness and differentiation marker genes in two independent homozygous PIK3CAH1047R cell lines using a high-throughput pluripotent stem cell scorecard (Fig. S4). This replicates the effect on cell marker genes documented by RT-qPCR in Fig.5, while also showing additional reductions in genes that were upregulated in homozygous PIK3CAH1047R cells (MYC, GDF3, FGF4) and which have previously been shown to be highly expressed in pluripotent stem cells (we have now added this additional clarification to the legend of Fig. S4) [22]. Despite the short term treatment, these data also show that no other treatment but SB431542 is capable of triggering expression of early neuroectoderm markers (CDH9, MAP2 and PAPLN) [23], prior to overt morphological changes in the cultures (Fig. S5; higher resolution images are also available via The Open Science Framework: https://osf.io/hbf7x/). Neuroectodermal gene expression is expected upon inhibition of TGFb signalling in human pluripotent stem cells [24,25].

A key conclusion of this study is there is a dose-dependent stemness phenotype. As this is not explicitly defined, to this reader, it would imply a graded response between wild type, heterozygotes, and homozygotes in the phenotypic and molecular characteristics. However, as is noted particularly in the omics components of the manuscript, there is in fact "near-binary" alteration in the assayed characteristics. Again, this should be qualified more explicitly, but it is more consistent with the data, which suggests the heterozygotes behave very similarly to the wild types, while homozygotes have substantial alterations. I would suggest the authors consider renaming their descriptions, removing "near-binary" and "dose-dependent" to something like "dose-threshold." This suggests after X threshold of oncogenic PI3K signalling, substantial alterations occur; under this threshold (e.g. hets), changes are marginal. In the event however that there may be a more "dose-dependent" effect, I would expect the transcriptomic and proteomic changes observed in the heterozygous cell lines should be seen in the homozygous cell lines (of which they are likely in greater in magnitude in addition to other changes).

AUTHORS’ RESPONSE__:__ This appears to us to be largely a matter of semantics. In talking of “dose dependency” we were certainly not implying a graded affect (as the Reviewer points out, our are findings are far from this, suggesting a sharp threshold of dose which triggers widespread changes), and indeed nothing in these words strictly suggests this interpretation. Nevertheless we are sensitive to the fact of the Reviewer’s interpretation of the term, and mindful that this might be shared by other readers. On the other hand talking of a “near-binary” effect seems to us to be an accurate description of our findings. We have edited the manuscript to minimise ambiguity with the following changes:

• line 49 “dose” replaced with “strength”: “We demonstrate signalling rewiring as a function of oncogenic PI3K signalling strength, and provide experimental evidence that self-sustained stemness is causally related to enhanced autocrine NODAL/TGFb”
• line 102: “This work provides in-depth characterisation of the near-binary PI3K signalling effects seen in hPSCs ….”
• lines 195, 198, 317: inserted “allele dose-dependent” We would also like to take issue with the case that the Reviewer seems to be making that a more graded change in gene expression across heterozygotes and homozygotes is to be expected. As mentioned in the manuscript (lines 206-210), there is evidence for NODAL/TGFb pathway activation in heterozygous cells. Nevertheless given the known temporal, context- and dose-dependent effects of this pathway [1,2,26,27] and, importantly, the widely described biological properties of developmental systems (featuring positive feedback loops, bistability and hysteresis; see Ref. [28,29]), we have no reason to expect that transcriptomic and proteomic changes observed in homozygous cell lines will be reproduced in heterozygous cell lines.

The manuscript would benefit from more direct comparisons between the heterozygotes and homozygotes.

AUTHORS’ RESPONSE__:__ Please refer to the additional data provided in response to a similar question by Reviewer 2.

Further to the above point, as the marginal phenotype observed in heterozygotes is a critical point in this paper, the authors would benefit from including heterozygote lines in the functional experiments presented in Fig 5. Inclusion of the hets in these experiments would instill confidence in this reader that the marginal molecular alterations characterized at the proteomic and transcriptomic level is reflected in the lack of functional stemness-sustaining behaviour.

AUTHORS’ RESPONSE__:__ The lack of stemness-sustaining behaviour in the heterozygous clones was demonstrated across multiple different experiments in our previous work, and further functional studies of early differentiation in these cells seemed a poor use of resource and very unlikely to give useful insights. Given the major disease phenotype associated with the same genetic change (PROS), the relative lack of phenotype in heterozygous cells was surprising and holds obvious implications for disease modelling (see also response to Reviewer 2, pp.2-3), and for how model systems are “calibrated” against human developmental disease. The aim of the current work was to:

1. • Determine whether increasing the depth of signalling and transcriptomic analyses would unmask small but important changes in heterozygous mutants that might have been missed in prior studies (i.e. we actively aimed to increase the power of the study for identification of subtle changes) and *
2. • To characterise in greater depth the signalling and transcriptional changes underpinning the robust threshold effect observed for self-sustained stemness driven by PIK3CAH1047R/H1047R. We would further observe that PROS does not feature obvious qualititative errors in tissue specification, but rather excessive growth of more or less normally differentiated tissues. We conceptualise this as reflecting a small incremental growth advantage in normally differented tissues of certain lineages that summates to create a major disease phenotype over months and years.*

Thus, without the functional and mechanistic experiments alluded to above, the claims/ conclusions are speculative. In particular, the cancer narrative is irrelevant to the study. Considering both the lack of conclusive differentiation experiments or relevant breast cancer experiments, the discussion on differentiation therapy for breast cancer should be removed.

AUTHORS’ RESPONSE__:__ The reference to cancer links to a computational study of human breast cancers where we specifically looked at the relationship between strength of PI3K signalling and ‘stemness’ [12], both measured using established transcriptional indices. We have included the bioRxiv reference in our revised manuscript (see l.337). While there is an element of speculation in this cancer observation, we do feel it is important and grounded in this and the BioRXiv study, and would prefer to maintain it. However, if editors take a different view it can be removed.

Reproducibility is a concern for this study. The authors should perform more replicates on their experiments (focusing on technical replicates of the lines employed to discern technical vs biological variability). A challenge in reading this manuscript is understanding which replicates were used for which experiments, and whether they are technical or biological (i.e. different lines). While some of the figure legends note this information, it would be helpful to provide clarity throughout the text. In addition, it should be noted that some experiments (e.g. the RPPA analysis in Fig 2B and Fig S3B) show substantial variability between replicates, but because it appears only a single technical replicate from two different cell lines was used, it is impossible to distinguish whether the variability is of a biological or technical nature. The authors would do well to focus on collecting more technical replicates of fewer biological replicates, and then expand to include more biological replicates if initial biological variation is observed.

AUTHORS’ RESPONSE__:__ We strenuously disagree with the Reviewer on this point. Throughout this manuscript, we have been transparent and thorough in reporting how experiments were performed, including the number of both biological and technical replicates. Representative examples include:

Legend to Figure 2A (RPPA dataset in growth-replete conditions): “The data are based on 10 wild-type cultures (3 clones), 5 PIK3CAWT/H1047R cultures (3 clones) and 7 PIK3CAH1047R/H1047R cultures (2 clones) as indicated.”

Legend to Figure 5: “The data are from two independent experiments, with each treatment applied to triplicate cultures of three wild-type and two homozygous iPSC clones.”

Specifically to address the RPPA studies, and as is clear from the Figure 2 legend, we initially performed RPPA analyses in growth factor-replete conditions with extensive technical and biological replication, arguing against the Reviewer’s point. To aid interpretation, we opted for summarising this large dataset in Venn diagrams (following extensive limma-based statistical analysis, including correction for multiple comparisons and sample interdependence as advised in Ref. [30]). If the Reviewer deems it valuable, we could include a heatmap overview as shown below:

[To view figure, please access PDF version of this rebuttal on https://osf.io/ecmhr/]

We took the view that the above representation, while comprehensive, is not particularly informative to the reader. All individual data points for both total and phosphoproteins – with and without normalisation – are plotted as part of separate barplots in the accompanying RNotebook (https://osf.io/d9tca/). These clearly demonstrate that the technical and biological variability in canonical PI3K signalling responses at the level of AKT and immediately downstream of AKT is very low. The same applies to the increased phosphorylation of SMAD2 (S465/S467) in PIK3CAH1047R iPSCs. We include two examples below, and would be happy to include the link to the above RNotebook in the respective Figure legend if the Reviewer deems this helpful.

[To view figure, please access PDF version of this rebuttal on https://osf.io/ecmhr/]

The interpretation of the second RPPA experiment (Fig. 2B) in growth factor-depleted conditions is focused entirely on these responses due to their consistency across both datasets (further supported by low-throughput signalling analyses in the previous PNAS publication).

We had made all raw data and guided analysis scripts for the above RPPA dataset publicly available, and the same is true for all original data as highlighted in the Materials & Methods section. Thus we strongly believe that readers have the opportunity to assess our work and reproduce our analyses/conclusions fully should they wish to do so.

• Finally, we noted in the initial PNAS paper describing these models that we derived and worked with up to 10 independent homozygous PIK3CAH1047R clones, as well as with 3 and 4 independent heterozygous and wild-type clones, respectively. This exceeds the common use of 2 clones (if at all mentioned) in many similar studies in the stem cell literature (e.g. Ref. [31–34]). In our view, derivation of more than two independent clones is crucial for reproducibility in gene editing studies given substantial variability arising from genetic drift [35,36]. We have consistently shown the phenotypic robustness of our mutant clones across the two studies; note, for example, the low technical and biological variability in both heterozygous and homozygous mutants in the transcriptomic data in Fig. 1A. As noted in the manuscript, the high-depth RNAseq data analysis was performed in different clones and independently of the RNAseq reported in Ref. [5], yet yields highly similar results and confirms transcriptional rewiring of PIK3CAH1047R/H1047R iPSCs.*

Throughout the text, the authors frequently reference their previous study in PNAS and often the lines of what is novel in this paper vs. reproduction of previous findings is blurred. The authors would benefit from reducing the frequency of referencing their previous study and focusing on emphasizing the novelty of the present findings.

AUTHORS’ RESPONSE__:__ We have carefully reviewed all instances of citation of our previous study in the manuscript and have reduced their numbers to improve focus on the current findings as suggested. As noted above, however, the current study builds closely upon the findings of the previous work, and referring to these to put the current work in context is important. Indeed, this is reflected in some of the reviewers’ collective comments and questions which are answered by the prior study. We have carefully reviewed the places in which we have cited our previous study and note that except for 2 citations in the Introduction and 3 more in the Discussion, all remaining citations are in the context of linking new and old data, which we believe is important for clarity as suggested by the reviewers. However, if editors take a different view we can minimise this and reduce the number of citations.

Without functional assays to complement and test their models, this manuscript is not a significant advance.

AUTHORS’ RESPONSE__:__ While we take the Reviewer’s point that further studies could have strengthened robustness of the evidence supporting a mediating role of NODAL/TGFb signalling in PI3K-driven stemness, we think this assertion is far too sweeping, and neglects numerous facets of the study of use and interest to several fields (as agreed by the other reviewers). To recapitulate some key points of interest/use of this study:

• Using a carefully derived PIK3CAH1047R iPSC model system and pharmacologically relevant doses of a recently approved PI3Ka-selective inhibitor, we demonstrate that the efficacy of the latter can depend on the strength of PI3K pathway activation and phenotype under investigation – despite expected downregulation of PI3K signalling by Alpelisib, the stemness phenotype is not reversed.
• We link this to self-sustained TGFb signalling in cells with strong PI3K activation by homozygous PIK3CAH1047R The link between the two pathways and the underlying rewiring are likely to be relevant in other contexts, as observed recently in a breast epithelial model system [37]. Given similarity between human pluripotent stem cells and cancer cells, our findings are of wider relevance.
• Aberrant PI3K activation has been associated with numerous pathologies, so it is important for the field to have well-characterised model systems with endogenous expression of one of the most common PIK3CA mutations. Our thorough characterisation of PIK3CAH1047R iPSCs validates one such model.
• To our knowledge, this is the first study to provide a comprehensive and integrated characterisation of isoform-specific PI3K signalling and transcriptomic changes in human pluripotent stem cells. This is important because current knowledge of PI3K signalling in human PSCs is largely based on extrapolation of findings from mouse embryonic stem cells, with many previous studies relying on high concentrations of the non-specific pan-PI3K inhibitor LY294002 (the use of which has been discouraged by the PI3K signalling community [38]).

  I believe the narrative was written for pluripotent stem cell biologists but without robust functional and quantitative cell biological assays to test their models, I don't anticipate stem cell biologists will be very interested.

AUTHORS’ RESPONSE__:__ The Reviewer is incorrect in his/her assertion about the target audience. PI3K signalling plays a key role in numerous disease and physiological processes as well as in development, and is of broad interest to cancer biologists, genetecists, rare disease biologists, biochemists, cell signallers, and endocrinologists among many others. Indeed we started with a primary focus on disease modelling (cancer, PROS) rather than stem cell biology, but because our findings are significant for the role of PI3K in stem cell biology as well as for these diseases, we aimed to make findings accessible across many of these readers. We refer the Reviewer to our previous response with regards to the significance of this work.

**Minor Comments:**

Consider adding gridlines to the MDS plots for clarity of read

AUTHORS’ RESPONSE__:__ This is a matter of taste, and as we honestly can not see how it would enhance appreciation of the very clear clustering, we have decided to leave the plot in its current form.

In Fig S2, some of the in-figure labelling is incorrect

AUTHORS’ RESPONSE__:__ We thank the Reviewer for spotting this. We believe the labelling error to be corrected now and we have further tried to streamline the plot headings, but please do let us know if there is something else which we may have missed.

In Fig S1C, the authors note poor correlation in the heterozygotes between this and a previous study. It would be helpful to qualify this discrepancy, as it is potentially concerning.

AUTHORS’ RESPONSE__: The sensitivity to detect differential gene expression is high for large fold changes (as seen in PIK3CAH1047R/H1047R mutants) in transcriptomic studies, but declines rapidly for fold changes in expression lines 126-131: “The magnitudes of gene expression changes in PIK3CAH1047R/H1047R cells correlated strongly with our previous findings (Spearman’s rho = 0.74, p WT/H1047R iPSCs (Fig. S1C), as expected given the smaller number and lower magnitude of observed gene expression changes in heterozygous cells, and the lower depth of previous transcriptomic studies__.”*

Line 208, the authors state that the small p-value for the homozygotes is suggestive of a dose-dependent effect. This is not the case; it simply suggests a greater probability of the effect being non-random.

AUTHORS’ RESPONSE__:__ The Reviewer is formally correct, and we apologise for the imprecision of our language. Nevertheless biological effect size is pertinent to the p value determined, and so our statement, while requiring an inductive leap from the reader, is not wholly invalid. To tidy this up and improve precision we have reworded as follows:

lines 215-217: “This is in keeping with the much lower effect size in heterozygous cells, and consistent with a critical role for the TGFbeta pathway in mediating the allele dose-dependent effect of PIK3CAH1047R in human iPSCs.”

What does the height in Fig 4B correspond to? It would perhaps be of value to scale nodes based on the significance value.

AUTHORS’ RESPONSE__:__ 4B illustrates hierarchical clustering of the module eigengenes - the height corresponds to similarity of gene expression. We clarify this in the revised manuscript.

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This is very interesting!

Great observations

Author Response

We thank the Editor of eLife f or kindly considering our manuscript for publication and for soliciting three peer reviews. We note that the reviews were positive for the most part. We sincerely believe that the key criticisms arise regrettably from a seeming misunderstanding of the motivation and context of our work – one that we hoped was a candid presentation of available data for tarantulas and the methods used. We provide detailed responses to the reviewers’ concerns below. We further note that our manuscript has since been published with minimal changes (Foley et al. 2020 Proceedings of the Royal Society B 287: 20201688, doi:10.1098/rspb.2020.1688).

Tarantulas belong to an enigmatic and charismatic group with a nearly cosmopolitan distribution and intriguingly show vivid coloration despite being mostly nocturnal/ crepuscular. Using a robust phylogeny based on a comprehensive transcriptomic dataset that includes nearly all theraphosid subfamilies (except Selenogyrinae), we performed both discrete and continuous ancestral state reconstructions of blue and green coloration in tarantulas using modern phylogenetic methods. Using phylogenetic correlation tests, we evaluated various possible functions for blue and green coloration, for instance aposematism and crypsis. Our results suggest green coloration is likely used in crypsis, while blue (and green) coloration show no correlation with urtication, stridulation or arboreality. Our findings also support a single ancestral origin of blue in tarantulas with losses being more frequent than gains, while green color has evolved multiple independent times but never lost. We comparatively assessed opsin expression from the transcriptomic data across tarantulas to understand the functional significance of blue and green coloration. Our opsin homolog network shows that tarantulas possess a rather diverse suite of regular arthropod opsins than previously appreciated.

While color vision in (jumping) spiders is relatively well studied, to the best of our knowledge, this is the first study to comparatively consider the identity of opsin expression across tarantulas, and in relation to the evolution of coloration. Our study challenges current belief (e.g., Morehouse et al. 2017 doi: 10.1086/693977 and references therein; Hsiung et al. 2015 doi: 10.1126/sciadv.1500709) that tarantulas are incapable of perceiving colors, at least from a molecular perspective and suggests a role for sexual selection in their evolution. This also adds to the growing body of knowledge on the complexity of arthropod visual systems (e.g., see Futahashi et al. 2015 doi:10.1073/pnas.1424670112, Hill et al. 2002 doi:10.1126/science.1076196).

In short, we believe our results are timely and pertinent broadly to sensory biologists, behavioural ecologists and evolutionary biologists as it is an exhortation for sorely needed behavioural and sensory experiments to understand proximate use of vivid coloration in this enigmatic group.

Summary:

This study offers some interesting data and ideas on colour evolution in tarantulas, building upon previous work on this topic. However, the reviewers judged that the insights are too taxon-specific and that several key conclusions are too speculative. There were also concerns about the methodology for trait scoring from photographs that the authors might consider going forward.

Reviewer #1:

This study investigates the evolution of blue and green setae colouration in tarantulas using phylogenetic analyses and trait values calculated from photographs. It argues that (i) green colouration has evolved in association with arboreality, and thus crypsis, and (ii) blue colouration is an ancestral trait lost and gained several times in tarantula evolution, possibly under sexual selection. It also uses transcriptome data to identify opsin homologs, as indirect evidence that tarantulas may have colour vision.

Otherwise, a few comments:

1) Given that data is limited for the family (only 25% of genera could be included in this study), it seemed a shame not to discuss further the variation in colour and habit within genera. Based on Figure 1 and supplementary tables, the majority of "blue" genera contain a mix of blue and not-blue (and not-photographed) species. Does this mean that blue has been lost many more times in recent evolutionary history? And how often are "losses" on your tree likely to be the result of insufficient sampling for the genus (i.e. you happen not to have sampled the blue species)?

First, the taxa in our robust and well-resolved phylogeny are representative of the major lineages within Theraphosidae, i.e., we have sampled nearly all theraphosid subfamilies (except Selenogyrinae). Our ideal is also to work with a more complete genus-level molecular phylogeny and corresponding color dataset for theraphosidae. However, this group is generally not well represented in museum collections (let alone in digitized collections), while the pet trade is focussed on only a select number of taxa. While we appreciate the reviewer’s concern that adding more taxa and corresponding data could potentially change the results, we believe that with a strong backbone phylogeny recovering the major branches, the results should not change all that much (For instance, cf. Hackett et al. 2008 10.1126/science.1157704 vs. Prum et al. 2016 10.1038/nature19417, where the initial Hackett et al. backbone is robust to increased sampling). Although the way trait losses are concentrated towards the tip suggests that using a genus-level phylogeny would perhaps show a few more recent trait losses, but unlikely to contradict an ancient origin of blue coloration at the base of this group, especially given the way the outgroups are polarized (i.e., outgroups also exhibit blue).

2) A key conclusion of the study is that sexual selection should not be discarded as a possible explanation for spider colour. However, there is very little detail given in the discussion to build this case. Do these spiders have mating displays that might plausibly include visual signals? How common are sexually-selected colours in spiders generally? Where on the body is the blue coloration (in cases where it is not whole body)? I also missed whether the images used are of males or females or both, or how many species show sexual dimorphism in colouration (mentioned briefly in the Discussion, but not summarised for species or genera).

We agree with the reviewer that we should have provided more information regarding sexual dichromatism in tarantulas, and on the images we used in the study (whether male/female). However, the location of blue coloration varies wildly with species – some species have blue chelicerae, blue abdomens, or blue carapaces while others are entirely blue. We also know very little about mating (and selection, if any) strategies in tarantulas, let alone the sensory ecology of this group. However, there is intriguing anecdotal information from one species (Aphonopelma) that they can be active as early as 4pm (Shillington 2002 Canadian J. Zoology, 80: 251-259, doi: 10.1139/z01-227), while some species show an intensification of color upon maturation, often a hallmark of sexual selection. Indeed, we believe that our work will incite broad interest on these intriguing questions.

3) A quick scroll through the amazing images on Rick West's site suggests that oranges and red/pinks are not rare in tarantulas. Perhaps the data is just not available, but it would be good to mention somewhere the rationale behind the blue/green focus, rather than examining all colours.

We agree. However, in the present study, we focused on blue and green colors because the data is readily available and we wanted to build upon the previous work by Hsiung et al 2015. Given that violet/blue and likely also some green coloration are structural in origin (Saranathan et al. 2015 Nano Letters, doi: 10.1021/acs.nanolett.5b0020; Hsiung et al. 2015), these hues are unlikely to fade or vary between individuals unlike diet acquired pigmentary coloration. Hence, these colors perhaps better lend themselves to analyses using digital photographs.

I suggest defining stridulating / urticating setae for non-specialist readers. I had to look these up to understand that they were involved in defence.

We thank the reviewer for this suggestion.

I notice the Rick West website says species IDs should not be made from photos alone. Is there a risk of misidentification for any photos?

We understand the reviewer’s concern. However, Rick West is an experienced arachnologist and quite knowledgeable in tarantula systematics and taxonomy (see https://www.tarantupedia.com/researchers/rick-c-west), which is why we endeavoured to use his website as extensively as possible without resorting to photos from hobbyists. We further validated the IDs with field guides, when in doubt.

The Results section would benefit from some more clear statements of key results. For example, phrases like "AIC values to assess the relationships between greenness and arboreality are reported in Table 3" could be replaced instead with a summary statement indicating what this table shows.

We agree and thank the reviewer for this suggestion.

In the Figure 1 caption I think there is a typo: 'the proportions of species with images that possess blue colouration (grey = no available images)" but should this say "grey = not blue"?

We apologize for the confusion. This is not a typo – this is in relation to Trichopelma, for which no images of described species were available, and so we cannot conclude that none of the taxa are blue/green.

142 - the lengthy discussion here of whether there is one or more mechanisms by which blue is produced in tarantulas, and the detailed criticism of Hsuing SEMs, seems a bit out of place given that the current study does not investigate the proximate mechanism of blue colouration but merely its presence.

We respectfully disagree. The core support for Hsiung et al.’s (2015) argument against sexual selection as a driver of color evolution in tarantulas comes from their structural diagnoses of the nanostructures responsible for the violet/blue structural coloration and their subsequent argument that a diversity of divergent nanostructures rather than convergence argues against sexual selection. While it is true that we did not investigate the proximate mechanism of blue coloration here, one of us (Saranathan et al. 2015) has already done so elsewhere. It appears that in insects and spiders, the bulk of the nanostructural diversity is across families and not within.

Table S6 - It is not clear to me how the values for predicted N orthologs were calculated.

This is mentioned in line 354 of our methods – “Per the ‘moderate’ criteria from the Alliance of Genome Resources (55), hits may be considered orthologous if three or more of the twelve tools in their suite converge upon that result”.

The Table S7 caption states: "A * indicates currently undescribed species with blue or green colour that can be confidently attributed to corresponding genus. However, as the described species exhibit no blue or green colour, we conservatively scored these as 0." Is this a conservative approach though? If they have been confidently assigned to genus, I don't understand why they would not be included.

This refers to the cases where a hitherto undescribed species possesses the blue or green color. However, even though the species has not formally been described, its placement in the genus is not in question. We have not included such undescribed species in our tabulated number of species per genus, as it is difficult to express any such undescribed species as a fraction of the total number of species in that genus.

Reviewer #2:

This paper presents a broad-ranging overview of tarantula visual pigments in relationship with the color of the spiders. The paper is interesting, well-written and presented, and will inspire further study into the visual and spectral characteristics of the genus.

We thank the reviewer for her/his/their kind words.

First a minor remark, Terakita and many others distinguish between opsin, being the protein part of the visual pigment molecule and intact light-sensing, so-called opsin-based pigment, often generalized as a rhodopsin. The statement of line 65, 'convert light photons to electrochemical signals through a signalling cascade' is according to that view strictly not correct. Furthermore, the presence of opsins in transcriptomes may be telling, but it is not at all sure that they are expressed in the eyes, if at all. As the authors well know, in many animal species some of the opsins are expressed elsewhere. It may be informative to mention that.

We thank the reviewer for this clarification. As for the regions of opsin expression, we very much agree – were it not for constraints of sample availability, we would also have preferred to sequence only the eyes and brain of various tarantulas that were all exposed to similar lighting conditions. However, we encouragingly see that our “leg only” transcriptomes have far fewer (often no) opsins as compared to the whole-body data.

The blueness or greenness feature prominently in the paper, but the criteria used for determining to which class a spider belongs are not at all sure. The Color Survey and Supplementary Table S2 refer to Birdspiders.com, but that requires a donation; not very welcoming. The other used sources are also not readily giving the insight or overview which material was sampled. I therefore think that the paper would considerably gain in palatability by adding a few exemplary photographs as well as measured spectra. Of course, I am inclined to trust the authors, but I would not immediately take color photographs from the web as the best material for assessing color data with 4-digit accuracy. Furthermore, the accessible photographs do not always show nice, uniform colors, so it might be sensible to mention which body part was used to score the animals. And finally, using CIE metric might infer to many readers that the spiders are presumably trichromatic, like us. Any further evidence?

We refer to the detailed description of our method for scoring blue or green coloration in tarantulas (l. 277-303). Briefly, we calculated ΔE (CIE 1976) difference values using between the images of each taxa against a suitable reference (average of green leaves, or Haplopelma lividum, the bluest taxa in our survey based on the b value of its images). We use the ΔE Lab values to perform quantitative ancestral state reconstruction, while we use ΔE b (for blue) and ΔE a (for green) to discretize the data for understanding trait gains and losses.

BirdSpiders.com only requires one to enter names of genera as search terms in order to see photos that we used. However, we agree could have provided some photos of exemplars. We do realise that using pictures is not ideal, as opposed to reflectance spectrophotometry (our ideal as well), which is why we limited ourselves to a single reputable source (BirdSpiders.com) for consistent images, whenever possible. However, acquiring sample material and reflectance of tarantulas is challenging. This group is generally not well represented in museum collections (let along in digitized collections), while the pet trade is focussed on only a select number of taxa and doing field work to collect specimens is fraught with moral and ethical issues (e.g., see https://www.nytimes.com/2019/04/01/science/poaching-wildlife-scientists.html). This study nevertheless represents a substantial improvement upon a recent high-profile work that used the OSX “color picker” function (Hsiung et al. 2015).

Indeed, available evidence on tarantula vision (including our opsin sequences) suggests tarantulas are likely trichromats (Dahl and Granda 1989 J. Arachnol., Morehouse et al. 2017) similar to jumping spiders (e.g., Zurek et al. 2015, doi: 10.1016/j.cub.2015.03.033), so we consider CIE as an appropriate color space for a putative tristimulus system in tarantulas (see also our response to Reviewer 3). Again, this underscores the need for future studies on the sensory biology and psychophysics of this enigmatic group.

Reviewer #3:

This neat paper continues the story of structural colour evolution in a group that is rarely appreciated for their ornamentation. The study uses colour & ecological data to model their evolution in a comparative framework, and also synthesises transcriptomic data to estimate the presence and diversity of opsins in the group. The main findings are that the tarantulas are ancestrally 'blue' and that green colouration has arisen repeatedly and seems to follow transitions to arboreality, along with evidence of perhaps underappreciated opsin diversity in the group. It's well-written and engaging, and a useful addition to our understanding of this developing story. I just have a few concerns around methods and the interpretation of results, however, which I feel need some further consideration.

We thank the reviewer for his/her/their kind words.

As the authors discuss in detail, this work in many ways parallels that of Hsiung et al. (2015). The two studies seem to agree in the broad-brush conclusions, which is interesting (and promising, for our understanding of the question), though their results conflict in significant ways too. Differences in methodology are an obvious cause, and they are particularly important in studies such as this in which the starting conditions (e.g. the assumed phylogeny or decisions around mapping of traits) so significantly shape outcomes. The current study uses a more recent and robust phylogeny, which is great, and the authors also emphasise their use of quantitative methods to assign colour traits (blue/green), unlike Hsiung et al.

We thank the reviewer for his/her/their appreciation.

1) This latter point is my main area of methodological concern, and I am not currently convinced that it is as useful or objective as is suggested. One issue is that the photographs are unstandardised in several dimensions, which will render the extracted values quite unreliable. I know the authors have considered this (as discussed in their supplement), but ultimately I don't believe you can reliably compare colour estimates from such diverse sources. Issues include non-standardised lighting conditions, alternate white-balancing algorithms, artefacts introduced through image compression, differences in the spectral sensitivities of camera models, no compensation for non-linear scaling of sensor outputs (which would again differ with camera models and even lenses), and so on (the works of Martin Stevens, Jolyon Troscianko, Jair Garcia, Adrian Dyer offer good discussion of these and related challenges). Some effort is made to minimise adverse effects, such as excluding the L dimension when calculating some colour distances, but even then the consequences are overstated since the outputs of camera sensors scale non-linearly with intensity, and so non-standardised lighting will still affect chromatic channels (a & b values). So with these factors at play, it becomes very difficult to know whether identified colour differences are a consequence of genuine differences in colouration, or simply differences in white balancing or some other feature of the photographs themselves.

We thank the reviewer for his/her/their carefully considered thoughts and for drawing our attention to the work of Martin Stevens, Jolyon Troscianko, Jair Garcia, and Adrian Dyer in this regard (e.g. Stevens et al. 2007 Biol. J. Linn. Soc. Lond., doi: 10.1111/j.1095-8312.2007.00725.x). These are fair points raised by the reviewer. We are indeed aware that there are clear drawbacks in working solely with photographs from online sources as opposed to optical reflectance data (our ideal), but we are sure that the reviewer appreciates how challenging it is to source specimens of tarantulas. It is for this reason that we restricted ourselves to photographs from mostly only 1 reputable source (BirdSpiders.com). Furthermore, this is why we chose a perceptual model that permits device independent color representation, one that lets us separate chromatic variables from brightness, keeping in mind the underlying assumptions. However, some recent research suggests that CIELab space can perform reasonably well as compared to the latest algorithms for illuminant-invariant color spaces (Chong et al. 2008 ACM Transactions on Graphics, doi: 10.1145/1360612.1360660). Please also see our response below (to point #2) and also to Reviewer #2 above.

Given the dearth of tarantula specimens and in the absence of spectrometry, future work will have to try and acquire uncompressed original images (with EXIF data) and could perform image processing such as homomorphic filtering and adaptive histogram equalization (Pizer et al. 1987 Computer Vision, Graphics, and Image Processing; Gonzalez and Woods 2018 Digital Image Processing, Pearson) in order to further mitigate artefacts such as those arising from differences in illumination, especially if using images from a diversity of sources.

2) The justification for some related decisions are also unclear to me. The CIE-76 colour distance is used, and is described as 'conservative'. But it is not so much conservative as it is an inaccurate model of human colour sensation. It fails to account for perceptual non-uniformity and actually overestimates colour differences between highly chromatic colours (like saturated blues). The authors note they preferred this to CIE-2000, which is a much better measure in terms of accuracy, because the latter was too permissive (line 300). I understand the problem, and appreciate their honesty, but this decision seems very arbitrary. If the goal is to quantitatively estimate colour differences according to human viewers, then the metric which best estimates our perceptual abilities would strike me as most appropriate. Also, the fact that all species would be classified as 'blue' using the CIE-2000, when some of them are obviously not blue by simply looking at them, is consistent with the kinds of image-processing issues noted above. I only focus on this general point because it is offered as a key advance on previous work (L 40-41), but I don't think that is clearly the case (though I agree that the scoring methods of Hsiung et al. are quite vague). I'm generally in favour of this sort of quantitative approach, but here I wonder if it wouldn't be simpler and more defensible to just ask some humans to classify images of spiders as either 'blue' or 'green', since that seems to be the end-goal anyway.

We agree that CIE 1976 is an inaccurate model of “human color sensation,” but at the same time the degree of their applicability or lack thereof to non-human tristimulus visual systems is not clear. In any case, the digital photographs do not preserve UV information anyway. We hasten to add CIE 1976 is still widely used in color science and engineering research for its simplicity and perceptual uniformity, as a simple Google Scholar search would attest. We believe that the reviewer is perhaps mistaken as to our motivation for choosing the CIE 1976 and the exact nature of the shortcomings of the CIE 1976 model, which it turns out to be an unintended advantage. Our goal was not, as the reviewer suggests, to just “quantitatively estimate color differences according to human viewers,” but to do so in a device independent fashion given the constraints of working with already available digital images, and for a putative trichromat visual system. Given there are technically no limits for a and b values in the CIE 76 space, color patches with high values of chroma are computed to have too strong a difference than in actual fact (Hill et al. 1997 ACM Transactions on Graphics, 16, 109-154). This is precisely the kind of situation that we do not face here, as we are essentially comparing shades of blue rather than for instance, chromatic contrasts between saturated blue vs. green or blue vs. red. Moreover, we only use the rectilinear rather than the polar coordinate representation of the colors (in other words, we do not compute the psychometric correlates, chroma Cab, or the hue angle hab). Contrary to the reviewer’s assertion that the CIE 1976 “overestimates color differences between highly chromatic colors (like saturated blues),” a quick perusal of Table S3 affirms that a comparison of highly saturated blues such as between our “standard” H. lividum and Poecilotheria metallica reveals they are quite close in terms of chromatic contrasts (i.e., small E values). Moreover, CIE 1994 and subsequent revisions rely on a von Kries-type transformation to account for non-uniformity of the perceptual space, but as the reviewer is well aware, without an accurate idea of the illumination conditions, use of CIE 2000 is not justified.

Lastly, we are sure the reviewer appreciates that asking humans to manually score the colors of images (e.g. Hsiung et al. 2015) is neither reproducible nor enables quantitative analyses of trait evolution.

3) L26-27, 53-56, 171-176: This is a more minor point than the above, but some of the discussion and logic around hypothesised functions could be elaborated upon, given it's presented as a motivating aim of the text (52-56). The challenge with a group like this, as the authors clearly know, is that essentially none of the ecological and behavioural work necessary to identify function(s) hasn't been done yet, so there are serious limitations on what might be inferred from purely comparative analyses at this stage. The (very interesting!) link between green colouration and arboreality is hypothesised and interpreted as evidence for crypsis, for example, but the link is not so straightforward. Light in a dense forest understory is quite often greenish (e.g. see Endler's work on terrestrial light environments) including at night which, when striking a specular, structurally-coloured green could make for a highly conspicuous colour pattern - especially achromatically (which is what nocturnal visual predators would often be relying on). This is particularly true if the substrate is brown rotten leaves or dirt, in which case they could shine like a beacon. Conversely, if the blue is sufficiently saturated and spectrally offset from the substrate it could be quite achromatically cryptic at dusk or night. To really answer these questions demands information on the viewers, viewing conditions, visual environment etc. The point being that it is a bit too simplistic to observe that, to a human, spiders are green and leaves on the forest floor may be green, and so suggest crypsis as the likely function (abstract L 22-23). So inferences around visual function(s) could either be toned down in places given the evidence at hand or shored up with further detail (though I'm not sure how much is available).

We agree. Indeed, we are limited by the absence of rigorous behavioural studies. With this in mind, we have already made every effort to tone down and emphasize that our results might point towards a given function, but we do not claim it outright. It is our fervent hope that these findings will form the basis for future behavioural studies by giving researchers a starting point to test their hypotheses.

We would like to point out that the association we uncovered is actually between arboreal taxa and the presence of green coloration and not as the reviewer says “spiders are green and leaves on forest floor may be green.” These taxa live in natural crevices on trees, shrubs and essentially spend their lives arboreally. Also, green coloration in tarantulas need not be structural in origin (see e.g., Saranathan et al. 2015) and this is why to test for crypsis against foliage, we used (pigmentary) leaves as the representative model for comparison to tarantula green colors. Although, certain lycaenid butterflies (Saranathan et al. 2010 10.1073/pnas.0909616107; Michielsen et al. 2010 10.1098/rsif.2009.0352), for instance, use structural coloration to better aid in crypsis against foliage.

Minor comments:

• I'm not familiar enough with with methods for creating homolog networks to comment in detail, but the use of BLASTing existing opsin sequences against transcriptomes seems straightforward enough. As do the methods for phylogenetic reconstruction.

We agree this is straightforward.

• L48: What constitutes a 'representative' species? And how reasonable is it to assign a value for such a labile trait to an entire genus? I understand we can only do our best of course and simplifications need to be made, but I can imagine many cases among insects (e.g. among butterflies and flies) where genus-level assignments would be meaningless due to the immense diversity of structural colouration among species (including in terms of simple presence/absence).

Please see our response to Reviewer 2 above.

• Line 168: Wouldn't this speak against a sexual function? Only in a tentative way of course, but the presence of conspicuous structural colouration in juveniles, which is absent in adults, would suggest a non-sexual origin to me.

The reviewer’s inference is incorrect. We do not suggest that blue coloration is present in juveniles but absent in adults, but only that such conspicuous colors already appear in the penultimate moult right before the male creates a sperm web and is ready for mating.

Reviewer #3:

This neat paper continues the story of structural colour evolution in a group that is rarely appreciated for their ornamentation. The study uses colour & ecological data to model their evolution in a comparative framework, and also synthesises transcriptomic data to estimate the presence and diversity of opsins in the group. The main findings are that the tarantulas are ancestrally 'blue' and that green colouration has arisen repeatedly and seems to follow transitions to arboreality, along with evidence of perhaps underappreciated opsin diversity in the group. It's well-written and engaging, and a useful addition to our understanding of this developing story. I just have a few concerns around methods and the interpretation of results, however, which I feel need some further consideration.

As the authors discuss in detail, this work in many ways parallels that of Hsiung et al. (2015). The two studies seem to agree in the broad-brush conclusions, which is interesting (and promising, for our understanding of the question), though their results conflict in significant ways too. Differences in methodology are an obvious cause, and they are particularly important in studies such as this in which the starting conditions (e.g. the assumed phylogeny or decisions around mapping of traits) so significantly shape outcomes. The current study uses a more recent and robust phylogeny, which is great, and the authors also emphasise their use of quantitative methods to assign colour traits (blue/green), unlike Hsiung et al.

1) This latter point is my main area of methodological concern, and I am not currently convinced that it is as useful or objective as is suggested. One issue is that the photographs are unstandardised in several dimensions, which will render the extracted values quite unreliable. I know the authors have considered this (as discussed in their supplement), but ultimately I don't believe you can reliably compare colour estimates from such diverse sources. Issues include non-standardised lighting conditions, alternate white-balancing algorithms, artefacts introduced through image compression, differences in the spectral sensitivities of camera models, no compensation for non-linear scaling of sensor outputs (which would again differ with camera models and even lenses), and so on (the works of Martin Stevens, Jolyon Troscianko, Jair Garcia, Adrian Dyer offer good discussion of these and related challenges). Some effort is made to minimise adverse effects, such as excluding the L dimension when calculating some colour distances, but even then the consequences are overstated since the outputs of camera sensors scale non-linearly with intensity, and so non-standardised lighting will still affect chromatic channels (a & b values). So with these factors at play, it becomes very difficult to know whether identified colour differences are a consequence of genuine differences in colouration, or simply differences in white balancing or some other feature of the photographs themselves.

2) The justification for some related decisions are also unclear to me. The CIE-76 colour distance is used, and is described as 'conservative'. But it is not so much conservative as it is an inaccurate model of human colour sensation. It fails to account for perceptual non-uniformity and actually overestimates colour differences between highly chromatic colours (like saturated blues). The authors note they preferred this to CIE-2000, which is a much better measure in terms of accuracy, because the latter was too permissive (line 300). I understand the problem, and appreciate their honesty, but this decision seems very arbitrary. If the goal is to quantitatively estimate colour differences according to human viewers, then the metric which best estimates our perceptual abilities would strike me as most appropriate. Also, the fact that all species would be classified as 'blue' using the CIE-2000, when some of them are obviously not blue by simply looking at them, is consistent with the kinds of image-processing issues noted above. I only focus on this general point because it is offered as a key advance on previous work (L 40-41), but I don't think that is clearly the case (though I agree that the scoring methods of Hsiung et al. are quite vague). I'm generally in favour of this sort of quantitative approach, but here I wonder if it wouldn't be simpler and more defensible to just ask some humans to classify images of spiders as either 'blue' or 'green', since that seems to be the end-goal anyway.

3) L26-27, 53-56, 171-176: This is a more minor point than the above, but some of the discussion and logic around hypothesised functions could be elaborated upon, given it's presented as a motivating aim of the text (52-56). The challenge with a group like this, as the authors clearly know, is that essentially none of the ecological and behavioural work necessary to identify function(s) hasn't been done yet, so there are serious limitations on what might be inferred from purely comparative analyses at this stage. The (very interesting!) link between green colouration and arboreality is hypothesised and interpreted as evidence for crypsis, for example, but the link is not so straightforward. Light in a dense forest understory is quite often greenish (e.g. see Endler's work on terrestrial light environments) including at night which, when striking a specular, structurally-coloured green could make for a highly conspicuous colour pattern - especially achromatically (which is what nocturnal visual predators would often be relying on). This is particularly true if the substrate is brown rotten leaves or dirt, in which case they could shine like a beacon. Conversely, if the blue is sufficiently saturated and spectrally offset from the substrate it could be quite achromatically cryptic at dusk or night. To really answer these questions demands information on the viewers, viewing conditions, visual environment etc. The point being that it is a bit too simplistic to observe that, to a human, spiders are green and leaves on the forest floor may be green, and so suggest crypsis as the likely function (abstract L 22-23). So inferences around visual function(s) could either be toned down in places given the evidence at hand or shored up with further detail (though I'm not sure how much is available).

Minor comments:

-I'm not familiar enough with with methods for creating homolog networks to comment in detail, but the use of BLASTing existing opsin sequences against transcriptomes seems straightforward enough. As do the methods for phylogenetic reconstruction.

-L48: What constitutes a 'representative' species? And how reasonable is it to assign a value for such a labile trait to an entire genus? I understand we can only do our best of course and simplifications need to be made, but I can imagine many cases among insects (e.g. among butterflies and flies) where genus-level assignments would be meaningless due to the immense diversity of structural colouration among species (including in terms of simple presence/absence).

-Line 168: Wouldn't this speak against a sexual function? Only in a tentative way of course, but the presence of conspicuous structural colouration in juveniles, which is absent in adults, would suggest a non-sexual origin to me.

Reviewer #1:

This study investigates the evolution of blue and green setae colouration in tarantulas using phylogenetic analyses and trait values calculated from photographs. It argues that (i) green colouration has evolved in association with arboreality, and thus crypsis, and (ii) blue colouration is an ancestral trait lost and gained several times in tarantula evolution, possibly under sexual selection. It also uses transcriptome data to identify opsin homologs, as indirect evidence that tarantulas may have colour vision.

Otherwise, a few comments:

1) Given that data is limited for the family (only 25% of genera could be included in this study), it seemed a shame not to discuss further the variation in colour and habit within genera. Based on Figure 1 and supplementary tables, the majority of "blue" genera contain a mix of blue and not-blue (and not-photographed) species. Does this mean that blue has been lost many more times in recent evolutionary history? And how often are "losses" on your tree likely to be the result of insufficient sampling for the genus (i.e. you happen not to have sampled the blue species)?

2) A key conclusion of the study is that sexual selection should not be discarded as a possible explanation for spider colour. However, there is very little detail given in the discussion to build this case. Do these spiders have mating displays that might plausibly include visual signals? How common are sexually-selected colours in spiders generally? Where on the body is the blue coloration (in cases where it is not whole body)? I also missed whether the images used are of males or females or both, or how many species show sexual dimorphism in colouration (mentioned briefly in the Discussion, but not summarised for species or genera).

3) A quick scroll through the amazing images on Rick West's site suggests that oranges and red/pinks are not rare in tarantulas. Perhaps the data is just not available, but it would be good to mention somewhere the rationale behind the blue/green focus, rather than examining all colours.

Minor comments:

I suggest defining stridulating / urticating setae for non-specialist readers. I had to look these up to understand that they were involved in defence.

I notice the Rick West website says species IDs should not be made from photos alone. Is there a risk of misidentification for any photos?

The Results section would benefit from some more clear statements of key results. For example, phrases like "AIC values to assess the relationships between greenness and arboreality are reported in Table 3" could be replaced instead with a summary statement indicating what this table shows.

In the Figure 1 caption I think there is a typo: 'the proportions of species with images that possess blue colouration (grey = no available images)" but should this say "grey = not blue"?

142 - the lengthy discussion here of whether there is one or more mechanisms by which blue is produced in tarantulas, and the detailed criticism of Hsuing SEMs, seems a bit out of place given that the current study does not investigate the proximate mechanism of blue colouration but merely its presence.

The Table S7 caption states: "A * indicates currently undescribed species with blue or green colour that can be confidently attributed to corresponding genus. However, as the described species exhibit no blue or green colour, we conservatively scored these as 0." Is this a conservative approach though? If they have been confidently assigned to genus, I don't understand why they would not be included.

Table S6 - It is not clear to me how the values for predicted N orthologs were calculated.

An example of a divide between the social standards for men and women. Helena talks about how women cannot "fight for love" which illustrates them not being able to peruse the ones they truly love, but I also think this comparison works to demonstrate the quite literal fight for "love" that Theseus peruses through taking Hippolyta in the midst of a battle. This quote describes a passive love that women are supposed to partake in, just allowing things to happen, while men are the ones who chose who and how they love. The words "scandal on my sex" demonstrates how not abiding by these terms is in no way acceptable and is a social disgrace.

Lysander's referral to Hermia as an Ethiope is meant to be an insult regarding her darker complexion. We have talked about this sort of thing a lot, but again, we see how darker complexions were seen as negative qualities and could be used as an insult. Like in Othello, we see how these racial systems were already in place where white people thought less of black people. However, I think it may be of importance to note that Lysander, before the magic juice, was in love with Hermia despite this "negative" quality. I do not think this was intended, but the fact that Lysander only says this when he is in this trance makes me read it as a comment about how racial insults/hate/discrimination is the not the result of logical or empathetic thinking, but of animalistic, basic, and disgust driven thought processes. Again though, this is modern view of what I want this play to be saying, I do not think given the time period Shakespeare was arguing that racial biases are fickle and driven only by hate/ignorance.

The best social studies teacher I had was as good as he was, not just because he showed a lot of devotion and energy in his teaching, but also because he understood and used the tools that we used every day

Author Response

Reviewer #1:

Köster and colleagues present a brief report in which they study in 9 month-old babies the electrophysiological responses to expected and unexpected events. The major finding is that in addition to a known ERP response, an NC present between 400-600 ms, they observe a differential effect in theta oscillations. The latter is a novel result and it is linked to the known properties of theta oscillations in learning. This is a nice study, with novel results and well presented. My major reservation however concerns the push the authors make for the novelty of the results and their interpretation as reflecting brain dynamics and rhythms. The reason for that is, that any ERP, passed through the lens of a wavelet/FFT etc, will yield a response at a particular frequency. This is especially the case for families of ERP responses related to unexpected event e.g., MMR, and NC, etc. For which there is plenty of literature linking them to responses to surprising event, and in particular in babies; and which given their timing will be reflected in delta/theta oscillations. The reason why I am pressing on this issue, is because there is an old, but still ongoing debate attempting to dissociate intrinsic brain dynamics from simple event related responses. This is by no means trivial and I certainly do not expect the authors to resolve it, yet I would expect the authors to be careful in their interpretation, to warn the reader that the result could just reflect the known ERP, to avoid introducing confusion in the field.

We would like to thank the author for highlighting the novelty of the results. Critically, there is one fundamental difference in investigating the ERP response and the trial-wise oscillatory power, which we have done in the present analysis: when looking at the evoked oscillatory response (i.e., the TF characteristics of the ERP), the signal is averaged over trials first and then subjected to a wavelet transform. However, when looking at the ongoing (or total) oscillatory response, the wavelet transform is applied at the level of the single trial, before the TF response of the single trials is averaged across the trials of one condition trials (for a classical illustration, see Tallon-Baudry & Bertrand, 1999; TICS, Box 2). We have now made this distinction more salient throughout the manuscript.

In the present study, the results did not suggest a relation between the ERP and the ongoing theta activity, because the topography, temporal evolution, and polarity of the ERP and the theta response were very dissimilar: Looking at Figure 2 (A and B) and Figure 3 (B and C), the Nc peaks at central electrodes, but the theta response is more distributed, and the expected versus unexpected difference was specific for the .4 to .6 s time window, but the theta difference lasted the whole trial. Furthermore, the NC was higher for expected versus unexpected, which should (due to the low frequency) rather lead to a higher theta power for unexpected, in contrast to expected events for the time frequency analysis for the Nc. To verify this intuition, we now ran a wavelet analysis on the evoked response (i.e., the ERP) and, for a direct comparison, also plotted the ongoing oscillatory response for the central electrodes (see Additional Figure 1). These additional analyses nicely illustrate that the trial-wise theta response provides a fundamentally different approach to analyze oscillatory brain dynamics.

Because this is likely of interest to many readers, we also report the results of the wavelet analysis of the ERP versus the analysis of the ongoing theta activity at central electrodes and the corresponding statistics in the result section, and have also included the Additional Figure in the supplementary materials, as Figure S2.

*Additional Figure 1. Comparison of the topography and time course for the 4 – 5 Hz activity for the evoked (A, B) and the ongoing (C, D) oscillatory response at central electrodes (400 – 600 ms; Cz, C3, C4; baseline: -100 – 0 ms). (A) Topography for the difference between unexpected and expected events in the evoked oscillatory response. (B) The corresponding time course at central electrodes, which did not reveal a significant difference between 400 – 600 ms, t(35) = 1.57, p = .126. (C) Topography for the same contrast in the ongoing oscillatory response and (D) the corresponding time course at central electrodes, which did likewise not reveal a significant difference between 400 – 600 ms, t(35) = -1.26, p = .218. The condition effects (unexpected - expected) were not correlated between the evoked and the ongoing response, r = .23, p = .169.*

A second aspect that I would like the authors to comment on is the power of the experimental design to measure surprise. From the methods, I gathered that the same stimulus materials and with the same frequency were presented as expected and unexpected endings. If that is the case, what is the measure of surprise? For once the same materials are shown causing habituation and reducing novelty and second the experiment introduces a long-term expectation of a 50:50 proportion of expected/unexpected events. I might be missing something here, which is likely as the methods are quite sparse in the description of what was actually done.

We have used 4 different stimuli types (variants) in each of the 4 different domains, with either an expected or unexpected outcome. This resulted in 32 distinct stimulus sequences, which we presented twice, resulting in (up to) 64 trials. We have now described this approach and design in more detail and have also included all stimuli as supplementary material (Figure S1). In particular, we have used multiple types in each domain to reduce potential habituation or expectation effects. Still, we agree that one difficulty may be that, over time, infants got used to the fact that expected and unexpected outcomes were to be similarly “expected” (i.e., 50:50). However, if this was the case it would have resulted in a reduction (or disappearance) of the condition effect, and would thus also reduce the condition difference that we found, rather than providing an alternative explanation. We now included this consideration in the method section (p. 7).

Two more comments concerning the analysis choices:

1) The statistics for the ERP and the TF could be reported using a cluster size correction. These are well established statistical methods in the field which would enable to identify the time window/topography that maximally distinguished between the expected and the unexpected condition both for ERP and TF. Along the same lines, the authors could report the spatial correlation of the ERP/TF effects.

For the ERP analysis we used the standard electrodes typically analyzed for the Nc in order to replicate effects found in former research (Langeloh et al., 2020; see also, Kayhan et al., 2019; Reynolds and Richards, 2005; Webb et al., 2005). For the TF analyses we used the most conservative criterion, namely all scalp recorded electrodes and the whole time window from 0 to 2000 ms, such that we did not make any choice regarding time window or the electrodes (i.e., which could be corrected for against other choices). We have now made those choices clearer in the method section, and why we think that, under these condition a multiple comparison correction is not needed/applicable (p. 10). Regarding the spatial correlation of the ERP and TF effects, we explained in response to the first comment the very different nature of the TF decomposition of the ERP and ongoing oscillatory activity and also that these were found to be interdependent (i.e., uncorrelated). We hope that with the additional analysis included in response to this comment that this difference is much clearer now.

2) While I can see the reason why the authors chose to keep the baseline the same between the ERP and the TF analysis, for time frequency analysis it would be advisable to use a baseline amounting to a comparable time to the frequency of interest; and to use a period that does not encroach in the period of interest i.e., with a wavelet = 7 and a baseline -100:0 the authors are well into the period of interested.

The difficulty in choosing the baseline in the present study was two-fold. First, we were interested in the ERP and the change in neural oscillations upon the onset of an outcome picture within a continuous presentation of pictures, forming a sequence. Second, we wanted to use a similar baseline for both analyses, to make them comparable. Because the second picture (the picture before the outcome picture) also elicited both an ERP and an oscillatory response at ~ 4 Hz (see Additional Figure 2), we choose a baseline just before the onset of the outcome stimulus, from -100 to 0 ms. Also we agree that the possibility to take a longer and earlier baseline, in particular for the TF results would have been favorable, but still consider that the -100 to 0 ms is still the best choice for the present analysis. Notably, because we found an increase in theta oscillations and the critical difference relies on a higher theta rhythm in one compared to the other condition, the effects of the increase in theta, if they effected the baseline, this effect would counteract rather than increase the current effect. We now explain this choice in more detail (p.10).

*Additional Figure 1. Display of the grand mean signals prior to the -100 to 0 baseline and outcome stimulus. (A) The time-frequency response across all scalp-recorded electrodes, as well as (B) the ERP at the central electrodes (Cz, C3, C4) across both conditions show a similar response to the 2. picture like the outcome picture. Thus a baseline just prior to the stimulus of interest was chosen, consistent for both analyses.*

Reviewer #2:

The manuscript reports increases in theta power and lower NC amplitude in response to unexpected (vs. expected) events in 9-month-olds. The authors state that the observed increase in theta power is significant because it is in line with an existing theory that the theta rhythm is involved in learning in mammals. The topic is timely, the results are novel, the sample size is solid, the methods are sound as far as I can tell, and the use of event types spanning multiple domains (e.g. action, number, solidity) is a strength. The manuscript is short, well-written, and easy to follow.

1) The current version of the manuscript states that the reported findings demonstrate that the theta rhythm is involved in processing of prediction error and supports the processing of unexpected events in 9-month-old infants. However, what is strictly shown is that watching at least some types of unexpected events enhance theta rhythm in 9-month-old infants, i.e. an increase in the theta rhythm is associated with processing unexpected events in infants, which suggests that an increase in the theta rhythm is a possible neural correlate of prediction error in this age range. While the present novel findings are certainly suggestive, more data and/or analyses would be needed to corroborate/confirm the role of the observed infant theta rhythm in processing prediction error, or document whether and how this increase in the theta rhythm supports the processing of unexpected events in infants. (As an example, since eye-tracking data were collected, are trial-by-trial variations in theta power increases to unexpected outcomes related to how long individual infants looked to the unexpected outcome pictures?) If it is not possible to further confirm/corroborate the role of the theta rhythm with this dataset, then the discussion, abstract, and title should be revised to more closely reflect what the current data shows (as the wording of the conclusion currently does), and clarify how future research may test the hypothesis that the infant theta rhythm directly supports the processing of prediction error in response to unexpected events.

We would like to thank the reviewer for acknowledging the merit of the present research.

On the one hand, we have revised our manuscript and are now somewhat more careful with our conclusion, in particular with regard to the refinement of basic expectations. On the other hand, we consider the concept of “violation to expectation” (VOE), which is one of the most widely used concepts in infancy research, very closely linked to the concept of a prediction error processing, namely a predictive model is violated. In particular, we have made this conceptual link in a recent theoretical paper (Köster et al., 2020), and based on former theoretical considerations about the link between these two concepts (e.g., see Schubotz 2015; Prediction and Expectation). In particular, in the present study we used a set of four different domains of violation of expectation paradigms, which are among the best established domains of infants core knowledge (e.g., action, solidity, cohesion, number; cf. Spelke & Kinzler, 2007). It was our specific goal not to replicate, for another time, that infants possess expectations (i.e., make predictions) in these domains, but to “flip the coin around” and investigate infants’ prediction error more generally, independent of the specific domain. We have now made the conceptual link between VOE and prediction error processing more explicit in the introduction of the manuscript and also emphasize that we choose a variety of domains to obtain a more general neural marker for infant processing of prediction errors.

Having said this, indeed, we planned to assess and compare both infants gaze behavior and EEG response. Unfortunately, this was not very successful and the concurrent recording only worked for a limited number of infants and trials. This led us to the decision to make the eye-tracking study a companion study and to collect more eye-tracking data in an independent sample of infants after the EEG assessment was completed, such that a match between the two measures was not feasible. We now make this choice more explicit in the method section (p. 7). In addition, contrary to our basic assumption we did not find an effect in the looking time measure. Namely, there was no difference between expected and unexpected outcomes. We assume that this is due to the specificities of the current design that was rather optimized for EEG assessments: We used a high number of repetitions (64), with highly variable domains (4), and restricted the time window for potential looking time effects to 5 seconds, which is highly uncommon in the field and therefore not directly comparable with former studies.

Finally, besides the ample evidence from former studies using VOE paradigms, if it were not the unexpected vs. expected (i.e., unpredicted vs. predicted) condition contrast which explains the differences we found in the ERP and the theta response, there would need to be an alternative explanation for the differential responses in the EEG, which produce the hypothesized effects. (Please also note that there are many studies relying their VOE assumption on ERPs alone, here we have two independent measures suggesting that infants discriminated between those conditions.)

2) The current version of the manuscript states "The ERP effect was somewhat consistent across conditions, but the effect was mainly driven by the differences between expected and unexpected events in the action and the number domain (Figure S1). The results were more consistent across domains for the condition difference in the 4 - 5 Hz activity, with a peak in the unexpected-expected difference falling in the 4 - 5 Hz range across all electrodes (Figure S2)". However, the similarity/dissimilarity of NC and theta activity responses across domains was not quantified or tested. Looking at Figures S1 and S2, it is not that obvious to me that theta responses were more consistent across domains than NC responses. I understand that there were too few trials to formally test for any effect of domain (action, number, solidity, cohesion) on NC and theta responses, either alone or in interaction with outcome (expected, unexpected). It may still be possible to test for correlations of the topography and time-course of the individual average unexpected-expected difference in NC and theta responses across domains at the group level, or to test for an effect of outcome (expected, unexpected) in individual domains for subgroups of infants who contributed enough trials. Alternatively, claims of consistency across domains may be altered throughout, in which case the inability to test whether the theta and/or NC signatures of unexpected event processing found are consistent across domains (vs. driven by some domains) should be acknowledged as a limitation of the present study.

We agree that this statement rather reflected our intuition and would not surpass statistical analysis given the low number of trials. So we are happy to refrain from this claim and simply refer to the supplementary material for the interested reader and also mention this as a perspective for future research in the discussion (p. 12; p. 15).

As outlined in our previous response, it was also not our goal to draw conclusions about each single domain, but rather to present a diversity of stimulus types from different core knowledge domains to gain a more generalized neural marker for infants’ processing of unexpected, i.e., unpredicted events.

Reviewer #3:

General assessment:

In this manuscript, the authors bring up a contemporary and relevant topic in the field, i.e. theta rhythm as a potential biomarker for prediction error in infancy. Currently, the literature is rich on discussions about how, and why, theta oscillations in infancy implement the different cognitive processes to which they have been linked. Investigating the research questions presented in this manuscript could therefore contribute to fill these gaps and improve our understanding of infants' neural oscillations and learning mechanisms. While we appreciate the motivation behind the study and the potential in the authors' research aim, we find that the experimental design, analyses and conclusions based on the results that can be drawn thereafter, lack sufficient novelty and are partly problematic in their description and implementation. Below, we list our major concerns in more detail, and make suggestions for improvements of the current analyses and manuscript.

Summary of major concerns:

1) Novelty:

(a) It is unclear how the study differs from Berger et al., 2006 apart from additional conditions. Please describe this study in more detail and how your study extends beyond it.

We would like to thank the reviewers for emphasizing the timeliness and relevance of the study.

The critical difference between the present study and the study by Berger et al. 2006 was that the authors applied, as far as we understand this from Figure 4 and the method section of their study, the wavelet analysis to the ERP signal. In contrast, in the present study, we applied the wavelet analysis at the level of single trials. We now explain the difference between the two signals in more detail in the revised manuscript and also included an additional comparison between the evoked (i.e., ERP) and the ongoing (i.e., total) oscillatory response (for more details, please see the first response to the first comment of reviewer 1).

(b) Seemingly innovative aspects (as listed below), which could make the study stand out among previous literature, but are ultimately not examined. Consequently, it is also not clear why they are included.

-Relation between Nc component and theta.

-Consistency of the effect across different core knowledge domains.

-Consistency of the effect across the social and non-social domains.

-Link between infants looking at time behavior and theta.

We are thankful for these suggestions, which are closely related to the points raised by reviewer 1 and 2. With regard to the relation between the Nc and the theta response, we have now included a direct comparison of these signals (see Additional Figure 1, i.e., novel Figure S2; for details, please see the first response to the first comment of reviewer 1). Regarding the consistency of effects across domains, we have explained in response to point 1 by reviewer 2 that this was not the specific purpose of the present study, but we aimed at using a diversity of VOE stimuli to obtain a more general neural signature for infants’ prediction error processing, and explain this in more detail in the revised manuscript. Having said this, we agree that the question of consistency of effects between conditions is highly interesting, but we would not consider the data robust enough to confidently test these differences given the limited number of trials available per stimulus category. We now discuss this as a direction for future research (p. 15). Finally, we also agree with regard to the link between looking times and the theta rhythm. As also outlined in response to point 1 by reviewer 2 (paragraph 2), we initially had this plan, but did not succeed in obtaining a satisfactory number of trials in the dual recording of EEG and eye-tracking, which made us change these plans. This is now explained in detail in the method section (p. 7).

(c) The reason to expect (or not) a difference at this age, compared to what is known from adult neural processing, is not adequately explained.

-Potentially because of neural generators in mid/pre-frontal cortex? See Lines 144-146.

The overall aim of the present study was to identify the neural signature for prediction error processing in the infant brain, which has, to the best of our knowledge, not been done this explicitly and with a focus on the ongoing theta activity and across a variety of violations in infants’ core knowledge domains. Because we did not expect a specific topography of this effect, in particular across multiple domains, we included all electrodes in the analyses. We have now clarified this in the method section (p. 10).

(d) The study is not sufficiently embedded in previous developmental literature on the functionality of theta. That is, consider theta's role in error processing, but also the increase of theta over time of an experiment and it's link to cognitive development. See, for example: Braithwaite et al., 2020; Conejero et al., 2018; Adam et al., 2020.

We are thankful that the reviewer indicated these works and have now included them in the introduction and discussion. Closest to the present study is the study by Conejero et al., 2018. However, this study is also based on theta analyses of the ERP, not of the ongoing oscillatory response and it includes considerably older infants (i.e., 16-month-olds instead of 9-month-olds as in the present study).

2) Methodology:

(a) Design: It is unclear what exactly a testing session entails.

-Was the outcome picture always presented for 5secs? The methods section suggests that, but the introduction of the design and Figure 1 do not. This might be misleading. Please change in Figure 1 to 5sec if applicable.

Yes, the final images were shown for 5s in order to simultaneously assess infants’ looking times. However, we included trials in the EEG analysis if infants looked for 2s, so this is the more relevant info for the analysis. We now clarified this in the method section (p. 7) and have also added this info in the figure caption.

-Were infants' eye-movements tracked simultaneously to the EEG recording? If so, please present findings on their looking time and (if possible) pupil size. Also examine the relation to theta power. This would enhance the novelty and tie these findings to the larger looking time literature that the authors refer to in their introduction.

Yes, in response to the second reviewer (comment 1) we explained in more detail why the joint analysis of the EEG and looking time data was not possible: We planned to assess both, infants gaze behavior and EEG response. Unfortunately, this was not very successful and the dual recording only worked for a few infants and trials. This led us to collect more eye-tracking data after the EEG assessment was completed, such that a match between the two measures was not feasible. We now clarified this in the method section (p. 7).

(b) Analysis:

-In terms of extracting theta power information: The baseline of 100ms is extremely short for a comparison in the frequency domain, since it does not even contain half a cycle of the frequency of interest, i.e. 4Hz. We appreciate the thought to keep the baseline the same as in the ERP analysis (which currently is hardly focused on in the manuscript), but it appears problematic for the theta analysis. Also, if we understand the spectral analysis correctly, the window the authors are using to estimate their spectral estimates is largely overlapping between baseline and experimental window. The question arises whether a baseline is even needed here, or if a direct contrast between conditions might be better suited.

Please see our explanation about the choice of the baseline in our response to reviewer 1, comment 2. Because our stimulus sequences were highly variable, likely leading to highly variable overall theta activity, and our specific interest was in the change in theta activity upon the onset of the unexpected versus unpredicted outcome, we still consider it useful to take a baseline here. Also because this makes the study more closely comparable to the existing literature. We now clarified this in the method section (p. 9)

-In terms of statistical testing

-It appears that the authors choose the frequency band that will be entered in the statistical analysis from visual inspection of the differences between conditions. They write: "we found the strongest difference between 4 - 5 Hz (see lower panel of Figure 3). Therefore, and because this is the first study of this kind, we analyzed this frequency range." ll. 277-279). This approach seems extremely problematic since it poses a high risk for 'double-dipping'. This is crucial and needs to be addressed. For instance, the authors could run non-parametric permutation tests on the time-frequency domain using FDR correction or cluster-based permutation tests on the topography.

-Lack of examining time- / topographic specificity.

Please also note the sentence before this citation, which states our initial hypothesis: “While our initial proposal was to look at the difference in the 4 Hz theta rhythm between conditions (Köster et al., 2019), we found the strongest difference between 4 – 5 Hz (see lower panel of Figure 3).” Note that the hypothesis of 4 Hz can be clearly derived from our 2019 study. We would maintain that the center frequency we took for the analysis 4.5Hz (i.e., 4 – 5Hz) is very close to this original hypothesis and, considering that we applied a novel design and analyses in very young infants, could indeed hardly have fallen more closely to this initial proposal. The frequency choice is also underlined, as the reviewer remarks, by the consistency of this peak across domains, peaking at 4Hz (cohesion), 4.5Hz (action), and 5Hz (solidity, number). Importantly, please note that we have chosen the electrodes and time window very conservatively, namely by including the whole time period and all electrodes, which we now explain in more detail on p. 10. Please also see our response to reviewer 1, comment “1)”.

3) Interpretation of results:

(a) The authors interpret the descriptive findings of Figure S1 as illustration of the consistency of the results across the four knowledge domains. While we would partly agree with this interpretation based on column A of that figure (even though also there the peak shifts between domains), columns B and C do not picture a consistent pattern of data. That is, the topography appears very different between domains and so does the temporal course of the 4-5Hz power, with only showing higher power in the action and number domain, not in the other two. Since none of these data were compared statistically, any interpretation remains descriptive. Yet, we would like to invite the authors to critically reconsider their interpretation. You also might want to consider adding domain (action, number etc.) as a covariate to your statistical model.

We agree with the reviewers (reviewer 2 and reviewer 3) that our initial interpretation of the data regarding the consistency of effects across domains may have been too strong. Thus, in the revised version of the manuscript, we do not state that the TF analysis revealed more consistent results. Given that the analysis was based on a different subsample and highly variable in trial numbers, we did not enter them as a covariate in the statistical model.

This abstract is a great place to find topics that you may be interested in as you look for your 3 letters from the main website. Think about what topics were of interest to students. Also, how did this assignment give students, "choice and voice"? How does this type of assignment contrast to a typical assignment the could've been given on this topic but without student voice? Take note and find correlations that may be relevant and/or helpful to you as you write your final paper for this week.

Very insightful

This is a very interesting account of how you related to ideas in the chapter.

Author Response

1) There were concerns about the normality tests and reanalysis to avoid pseudo-replication that must be addressed.

We have now checked the data by two tests for normal distribution (Shapiro-Wilk and Kolmogorov_Smirnoff) and found that flight data do not follow a normal distribution. Therefore statistical analysis of flight data have now been performed using non-parametric tests. We have used the Kruskal-Wallace test followed by Dunn’s multiple comparison test for multiple comparisons and Mann-Whitney U-Test for pair wise comparisons. This information has been included in the statistical tests section in methods. Regarding pseudo-replication, as suggested imaging data have been replotted and calculated now to include just one cell, or one lobe per brain. In addition we have included individual brain traces for every experiment as supplemental data (Figure 5 - supplement F2, Figure 6 – supplement F1, F3 and F4).

2) Discussion should be made clearer and expanded to encompass more of the literature. Specifically, the authors should expand upon the final section of the discussion to discuss more about 1) the potential context for cholinergic modulation of the PPL1-y2alpha'1 DANs (For example, consider where the acetylcholine signal onto DANs might come from. DANs may not be entirely presynaptic to Kenyon cells but might also receive input from Kenyon cells.), 2) the proposed role of these DANs (which have been studied in several contexts) and 3) modulation of innate behavior in general. The paper begins with the importance of modulating innate behavior, but the discussion on this topic is spare and focused almost entirely on research on the mushroom bodies of Drosophila. The discussion section leans heavily on summarizing the results, rather than making connections to work in other systems or networks.

As suggested we have now addressed each of these points in greater detail in the last section of the discussion which has been expanded to two paragraphs. The possibility of cholinergic inputs from KC cells to DANs stimulating the IP3R have been included in the discussion and in the final model in Figure 7. Several other references that mention the role of PPL1-y2alpha'1 DANs in modulation of behaviour are now included – see last para of the discussion. We have expanded the last section of the discussion to include possible roles for other regions of the brain in modulating flight and references to other insect brains, where relevant.

3) One common point raised by all reviewers was the need for expression of the itprDN during pupation which could have been due to either the perdurance of endogenous itpr vs. a developmental effect caused by the itprDN (the authors fully acknowledge the issue). This section raised many questions that aren't within the scope of this study, nor are easily resolved. Nevertheless, the authors must expand upon the implications of these results and suggest future studies will needed to resolve the issue.

We are indeed unable to state equivocally if adult behavioural phenotypes, arising from expression of the IP3R^DN, are only pupal or both pupal and adult. We have expanded on the implications of these results both in the results (Page 9-10) and in the discussion (page 11). One way of addressing this is to express a tagged IP3R^DN specifically in late pupae and then follow it’s perdurance in adults. This experiment has now been suggested as a way to resolve this issue in the second paragraph of the discussion.

Reviewer #1:

The authors report experiments on Drosophila to show that the proper function of an IP3 receptor in a small subset of dopaminergic neurons is required for flight behavior. Most interesting is the fact that the requirement is restricted to a time point during pupal development. Technically, the authors report a novel dominant-negative mutant for of the IP3 receptor to interfere with its function. Physiologically, the IP3 receptor-dependent impairment in the function of the dopaminergic neurons affects both synaptic vesicle release and excitability, Also, muscarinic acetylcholine receptors are required for proper development of the flight-modulating circuit during development.

The role of dopamine in the brain of Drosophila (as a model for general dopamine and brain function) is in the center of current research, and is studied by a large number of laboratories. More and more types of behavior are discovered that are modulated by dopaminergic neurons, and in particular those innervating the mushroom body. Therefore, the study is of very high interest for researchers working on Drosophila, but also to a broader readership.

The experiments are well designed. with appropriate controls at place. The conclusions drawn are highly interesting and novel (dopaminergic modulation of flight behavior, perhaps in the context of food seeking behavior, molecular mechanisms of circuit maturation).

Minor comments:

1) A test for normal distribution of data is required to determine whether parametric statistical tests are actually appropriate.

Done – please see response above.

2) It is not clear to me why the authors conclude an acute requirement of IP3R during the adult state although the phenotype can arise through a genetic intervention during earlier time points in development (Page 9, lines 297ff). This has to be outlined much clearer. My interpretation of the data is: During a certain time window after pupal formation IP3 signaling is required for a proper formation of the neuronal circuit. This is likely to be not only a cell-intrinsic (i.e., cell autonomous) effect because the mAchR is also required during this time window. This provides an excellent example (there are actually only very few!) of circuit development that requires synaptic interactions between neurons. If one keeps in mind that dopaminergic neurons have reciprocal synapses with Kenyon cells (e.g. Cervantes-Sandova, elife 2017; should be included in schematic illustration!)), and these release acetylcholine onto dopaminergic neurons, a potential circuit maturation based on the concerted activity is most interesting. I suggest that the authors point out more precisely how they think the actual phenotype comes about, of course, with all due caution.

The primary reason that we suggest an adult requirement for the IP3R in the DANs is that we see a Ca2+ response to carbachol in adult PPL1-y2alpha'1 DANs (Figure 5 – supplement 1). We put together this finding with the observation that carbachol stimulates dopamine release from PPL1-y2alpha'1 DANs (Figure 5) and that blocking vesicle release acutely in adults reduce durations of flight bouts (Figure 4) to suggest that there is likely to be an adult requirement. However, we agree that this is not conclusive and certainly does not negate a pupal requirement. As mentioned above we have addressed the pupal vs pupal+adult issue in greater detail in the results (page 9, 10) and discussion (page 11). We agree that there may be acetylcholine release from Kenyon cells at the MB synapse. This possibility has been included in the discussion and in Figure 7.

3) Statistical tests should be done across independent brains, not across different cells in the same brains.

We have done this. Thank you for pointing this out.

Additional data files and statistical comments:

A test for normal distribution of data is required to determine whether parametric statistical tests are actually appropriate.

Done.

Figure legend 5 C should be 5B. The scaling of the y-axis is not optimal.

Done.

Statistical tests should be done across independent brains, not across different cells in the same brains. This would cause a mixture of dependent and independent data. This is of importance!

Done.

Reviewer #2:

The results of the individual experiments reported by the authors are convincing. The approach is rigorous and they take full advantage of the many powerful molecular genetic tools available in Drosophila. The identification of a mechanism by which a small subset of dopaminergic cells may control behavior is significant. My concerns about the manuscript are relatively minor.

Minor comments:

I have reviewed "Modulation of flight and feeding behaviours requires presynaptic IP3Rs in dopaminergic Neurons" by Sharma and Hasan. The authors first translated to Drosophila a dominant negative (DN) strategy first tested in mammalian cells to block the function of the fly IP3 receptor. Controls using westerns to test the expression in vivo and calcium imaging to assess inhibitory activity in an ex vivo prep were generally convincing. They then show that the DNA, RNAi and a wt transgene disrupts flight as they have shown previously using both genetic mutants and RNAi. They use genetic rescue to further show that alterations in the function of itpr in dopaminergic cells are likely to mediate at least some aspects of the flight deficit. The restricted distribution of the THD' driver was used to narrow down the identity of DA cell clusters responsible for this effect to PPL1 and/or PPL3. Additional split GAL4 lines identified a deficit when the DN was expressed in the PPL1-γ2α′1 subset of DA cells that project to the mushroom bodies. This is a key finding of the paper since it localizes the requirement of the IP3R to cells that have been implicated in other behaviors. Developmental tests using TARGET/GAL80 indicate a requirement for itpr during late development. Disruption of itpr only in the adult did not have a significant effect. This seems likely to be due to perdurance of itpr as suggested by the authors. However, these data make it difficult to determine which aspects of the phenotype are due to broad developmental deficits versus disruption of IP3R in the adult (see below). The authors next test the effects of mAhR with the idea that mAChR is likely to signal through IP3R. While it was known that developmental expression of mAcHR expression is required for adult flight, the current data more specifically that the PPL1-γ2α′1 DANs are required, enhancing the impact of the paper.

To tie these results to vesicle recycling and release the authors use the shibere[ts] transgene in PPL1-γ2α′1. Flight bouts were disrupted via exposure to the non-permissive temperature both during late pupal development and the adult. The adult phenotype has been demonstrated previously but the developmental defect is novel. The demonstration of an effect in adults is important since it suggests loss of itpr during adulthood might also have an effect in adults even though this can't be tested due to perdurance. Expression of shibire[ts] in PPL1-γ2α′1 also disrupts feeding, and the authors next phenotype these effects with the itpr DN, indicating that IP3R expression in PPL1-γ2α′1 is required for both feeding and flight. However, here as with the flight experiments, it is not possible to directly demonstrate an effect in adults due to perdurance. They show that knockdown of mAChR also reduces feeding similar to its effects on flight and suggest that the deficits are due to disruption of the mAchR ->(Gq) ->IPR3 pathway. The suggestion of connections between mAchR and IPR3 within PPL1-γ2α′1 and the idea that PPL1-γ2α′1 controls two distinct behaviors are a significant finding and one of main contributions of the paper.

To help link the shibire[ts] data set with and the results of perturbing mAchR and IPR3, the authors show that carbochol induced DA release is reduced, making excellent use of the relatively new GRAB-DA lines. As a control, they show that synapse density of PPL1-γ2α′1 in the γ2α′1 MB lobes are not altered. The demonstration that DA release is altered elevates the technical strength of the paper. Moreover, although further experiments might be needed to prove their model, these data support the argument that mAchR ->(Gq) ->IPR3 pathway is disrupted in the adult. The final set of experiments in Fig 6 indicate that excitability of the PPL1-γ2α′1 DANs is also disrupted by knock down or IP3R. Is it possible that this deficit contributes to the decrease in DA release by the mAchR ->(Gq) ->IPR3 and the authors nicely explain a possible mechanism and cite relevant references in the Discussion.

The results of the individual experiments reported by the authors are convincing. The approach is rigorous and they take full advantage of the many powerful molecular genetic tools available in Drosophila. The generation of the DN transgene is a nice idea and in combination with other tools helped them to identify specific subsets of DA neurons important for the behaviors they test. However, they have previously demonstrated similar effects with mutants and RNAi, and again use them to help map the relevant cells. Since the use of the DN construct did not really go beyond the experiments using RNAi or genetic rescue, the emphasis on the importance of this reagent might be reduced in the abstract and introduction.

Flight deficits have also been seen in other experiments on these the DANs identified by the authors. Thus, the major novel finding of this section is the demonstration that itpr is required in these cells for regulating flight. While it was previously shown that feeding behavior is also required by DAN projections to the MB, the idea that overlapping cells might control both flight and feeding is interesting. Although the idea that these two phenotypes are specifically related to each other seems somewhat speculative, one major strength of the paper lies in tying together prior observations on itpr and the DANs with their current experiments. They do this again at the cellular level using GRAB to show that carbachol induced release of DA (but not synapse density) is reduced by itpr knock-down, thus tying together data on shibere, AcHR and itpr.

These connections make for an exciting story, and they have been cleverly woven together by the authors. On the other hand, they also represent a possible concern about the manuscript as a whole, since causal relationships between the deficits between the effects of blocking the effects of IP3R, mAcHR, neuronal excitability and vesicle release are not yet proven. It is therefore possible that all of these are relatively non-specific effects of disrupting the function of PPL1-γ2α′1 neurons. This modestly reduces the strength of the paper but is also a relatively minor concern. A second potential concern is that despite the interesting connections made by the authors as well as some exciting new data, some of the findings replicate previous data.

It is indeed likely that loss of the IP3R in PPL1-y2alpha'1 DANs leads to both specific (acetylcholine signaling followed by neurotransmitter release) and non-specific changes (such as loss of excitability). Both are likely to have an effect on the behavioural phenotypes modulated by PPL1-y2alpha'1 DANs. We have previously shown a role for both mAchR and the IP3R in flight. However, in this work we have addressed cell specificity and mechanism, neither of which was known earlier.

A third concern is the relationship between the effects of disrupting PPL1-γ2α′1 during development versus the adult. As the authors suggest, perdurance (of protein expression) and/or "perdurance" of previously formed tetramers could easily account for the failure of itpr and mAChR knock down in the adult to cause behavioral deficits. By the same token, it is difficult to parse out the contribution of developmental defects in the DA cells versus problems with signaling in the adult and the following issues should be addressed: the observation that synaptic bouton density is not disrupted is a good way to eliminate gross disruption of connectivity during development but does not rule out other more subtle developmental defects in neuronal function. The fact that shibire[ts] can cause effects in the adult is appreciated but does not really help us to understand what IP3R and perhaps mAcHR are doing during development.

We agree and have tried to further address this issue in the text (see above).

Additional Minor Concerns.

To validate the decrease in the overall response to carbachol in Fig 1D and E, the authors show a statistically significant difference for area under the curve. A parallel metric and statistical test might be used to support the statement that the response is delayed in 1D but not 1E.

Thank you for this suggestion. We performed the test and in fact found that both cellular and mitochondrial responses are delayed. In presence of IP3RDN. This part of the text has been modified (page 4).

"Interestingly, the mitochondrial response did not exhibit a delay in reaching peak values." Why is that? A brief explanation might be useful.

This is no longer the case. The sentence has been removed.

The second explanation of how shibire[ts] works might be shortened.

Done.

Reviewer #3:

General Assessment:

This study demonstrates that IP3R signaling (triggered by muscarinic receptor activation) affects excitability and quantal content of a subset of dopaminergic neurons to modulate flight duration and food search. I had no technical concerns and am generally supportive. My only major concern was that the narrative was fragmented. I believe this is because the perspective shifted between the IP3Rs and the dopamine neurons themselves, and was too focused. I think that streamlining the narrative and providing a broader perspective for the results will remedy this issue.

Major Comments:

-I would like the authors to expand upon their final section of the discussion to discuss more about 1) the potential context for cholinergic modulation of the PPL1-y2alpha'1 DANs, 2) the proposed role of these DANs (which have been studied in several contexts) and 3) modulation of innate behavior in general. The paper begins with the importance of modulating innate behavior, but the discussion on this topic is spare and focused almost entirely on research on the mushroom bodies of Drosophila. The discussion section leans heavily on summarizing the results, rather than making connections to work in other systems or networks.

We have expanded the last section of the discussion to include these suggestions (see above under consolidated review points).

-The developmental section seemed somewhat tangential as the authors cannot distinguish between a developmental role for the IP3R from a need to express the ItprDN transgene prior to adulthood to overcome a potential slow turnover of endogenous IP3R. In essence, it was unclear how these results contributed to the overall narrative of state modulation of behavior. Is this section informative to the development of the mushroom bodies or rigorous validation of the novel transgene?

The manuscript addresses how IP3R function impacts behaviour. In that context pupal (developmental) and adult contributions are both relevant.

Reviewer #1:

In this manuscript, Bosco et al. propose that DHX30 coordinates cytoplasmic translation and mitochondrial function to impact on cancer cell survival. They deplete DHX30 and report that this causes an enhancement of translation including those of mRNAs encoding for cytoplasmic ribosomal proteins, while paradoxically reducing the translation of mitoribosome protein mRNAs. There are cytoplasmic and mitochondrial isoforms of DHX30 and the authors assess the long-term consequences of knockdown of the cytoplasmic versus mitochondrial + cytoplasmic proteins. Some of the novelty of this paper has been preempted by a previous publication by Antonicka and Shoubridge showing that loss of DHX30 results in impaired mitochondrial ribosome assembly, impaired mitochondria OXPHOS assembly, impaired mitochondrial mRNA precursor processing, and a very severe decrease in mitochondrial translation. I think the work, while interesting, is preliminary and should aim to provide mechanistic insight for the phenotype associated with DHX30 knockdown.

As far as I can see, none of the targets obtained from the polysome profiling are validated in this study. This is concerning since polysome profiling was previously reported in a Cell Report 2020 publication by the authors (GSE 95024; available at the GEO database), but the origin of the RNA-seq data in the current paper is not clear (GSE 154065; not available at the GEO database). We do not know if the RNA-seq data was generated from the same samples as the polysome profiling samples previously reported or completely independent of these (this information is lacking). Regardless, validation of any putative translation responsive genes predicted from polysome profiling data would appear to be a reasonable expectation these days.

The authors claim that depletion of DHX30 leads to increased global translation (Figs 1f, g). They also provide evidence that translation of mRNAs encoding cytoplasmic ribosomal proteins is increased, while the translation of mRNAs encoding mitoribosome ribosomal proteins is decreased (Fig 1b). DHX30 is associated with ribosomal subunits, 80S monosone and low-molecular weight polysomes, and it also interacts with a CG-rich motif for p53-dependent death (CGPD) in 3' UTRs of mRNAs. What is lacking is a mechanism to explain these observations (if the data validates)? To this reviewer the lack of mechanistic insight is a serious shortcoming of the current submission. What is responsible for the general translational increase (including cytoplasmic rps encoding mRNAs), yet mitochondrial rp mRNA translation decrease, upon DHX30 knockdown? Many rp mRNAs have TOP motifs at their 5' ends, is this pathway affected?

The authors previously identified DHX30 as a CGPD-motif interactor. They published this as a specific DHX30 binding motif, yet this motif is not enriched in the new data set established by the authors. I don't understand the statement put forth by the authors on line 286 that " While we cannot exclude that the CGPD motif can be implicated, only a subset of RP transcripts harbors instances of it". Either it is significantly enriched or it is not. In any event, there appears to be an inconsistency with previously published data.

The ENCODE eCLIP data suggests that DHX30 can bind to 67 cytoplasmic ribosomal and 23 mitochondrial protein transcripts. Yet in their eCLIP validation experiments using RIP, the authors probe for the potential of DHX30 to bind to only MRPL11 and MRPS22 (Fig 2a). They write "These findings suggest that DHX30 directly promotes the stability and/or translation of mitoribosome transcripts." What about the cytoplasmic ribosome protein mRNAs, which according to the ENCODE data can also bind DHX30, yet their response to DHX30 depletion is the opposite of that of the mitoribosome protein mRNAs. I think it may be premature to correlate DHX30 with mitoribosome protein regulation.

The comparison of the efficiency of knockdown using siRNAs targeting the cytoplasmic form versus the mitochondrial + cytoplasmic forms versus shRNA knockdown efficiency is confusing and, in my humble opinion doesn't add insight into mechanism of action. "Transient silencing of DHX30" (ie, using siRNAs) achieves ~50% mRNA reduction in HCT and U2OS cells 48-96s following transfection. On the other hand, silencing of DHX30 mRNA using shRNA achieved better levels of reduction (60-75% decrease) in U2OS and MCF7 cells (Fig S2e). The authors use these differences in knockdown efficiencies to correlate differences in expression response of several mitochondrial encoded genes. The authors need to show the extent to which DHX30 protein levels are reduced in the siRNA treated cells (only changes in mRNA levels are presented). As well, there should be a genetic rescue experiment to show that siRNA or shRNA resistant DHX30 cDNA can overcome this effect. Lane 3 of Fig 2h appears underloaded as assessed by the actin intensity. MRPL11 protein levels appear greater in lane 2 (siDHX30-C) compared to lane 1, why is that?

Please provide details on the siRNA and shRNAs used. It appears that only one shDHX30 was used to target cytoplasmic DHX30 and one shRNA to target cytoplasmic + mito DHX30. I couldn't find information on this.

If mutations in DHX30 are known to trigger stress granules formation, does knockdown of DHX30 do the same. Is eIF2 alpha phosphorylated upon HDX30 knockdown?

There appears to be several DHX30 mRNAs made through alternative splicing (see https://www.ncbi.nlm.nih.gov/gene/22907). In this study, when the authors refer to cytoplasmic DHX30, is the equivalent function being attributed to these different potential isoforms?

The pictures in Figs 1e, 2d, and S3g are quite difficult to appreciate and should be provided at higher magnification.

Fig 2f. Why is there so much tubulin in the mitochondrial protein extract lane?

Suppression of DHX30 mRNA leads to lowered proliferation rates in HCT116 cells. This however was not due to significant alterations in the cell cycle (Fig 4e). Apoptotic rates do not appear to be affected (compare HCT_shNT to HCT_shDHX30 in the DMSO samples of Fig 4g). Can the authors please provide an understanding into what is leading to the lowered proliferation rates if cell cycle progression and cell death are unaffected. Confusingly, "transient" silencing of DHX30 mRNA (protein levels were not assessed) in U2OS cells did not impact proliferation while in MCF7 cells it did. Although the authors attribute this difference in response to better depletion of DHX30 mRNA in MCF7 cells, they do not actually measure DHX30 protein levels and the use of different cell lines complicates the interpretation.

Line 267 "none of the DHX30 closer homologs showed strong evidence of such localized translation". What homologs are being referred to here?

Line 269. "Although our experiments did not enable us to confirm this in HCT116, a previous report also showed evidence for DHX30 interaction with mitochondrial transcripts in human fibroblasts by RIP-seq (Antonicka and Shoubridge, 2015). Our data instead point to a direct interaction with mitoribosome transcripts and their positive modulation as another means by which DHX30 can indirectly affect mitochondrial translation." DHX30 thus interacts with many different mRNAs and in my view it becomes difficult to ascribe a particular biological response to DHX30 to a particular set of transcripts based on interaction data.

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Reply to the reviewers

Response to the reviewers’ comments:

We thank both the reviewer for their critical evaluation and excellent suggestion to improve the manuscript. We are making all the changes suggested by both the reviewers and performing the experiments to address all the concerns specifically from the reviewer #1. Please find below our response to the reviewers’ comments:

Reviewer #1:

This is an interesting study from the Rahaman group that identifies cardiolipin (CL) as a potential binding target for Drp6 recruitment to the nuclear membrane in Tetrahymena (that has a unique nuclear remodeling program). In addition, they identify a residue, I553 in the DTD region, which they claim is a key residue involved in specific CL interactions. While the experiments themselves are technically sound, and are well performed and controlled, I don't find the major conclusion that I553 is involved in direct CL interactions justified or well rationalized. By their own admission (in the discussion), the conservative mutation I553M may perturb local folding and may indirectly affect CL interactions. There is no test of DTD folding with and without the I553M mutation, nor are there other mutations (e.g. I553A and in the vicinity) tested. CD experiments in the absence and presence of CL-containing membranes will likely yield information on the impact of the I553 mutations, while DLS experiments would inform on the hydrodynamic properties (overall 3D fold) of the DTD and the impact of these mutations. CL interactions generally involve a combination of electrostatic and hydrophobic forces. Where do the electrostatic interactions come from? Why would an Isoleucine to Methionine mutation affect the hydrophobic component, even if I553 is the key hydrophobic residue?

Response:

We thank the reviewer for the comments that the experiments are sound, well performed with appropriate controls. While we agree that the exact mechanism of how I553 provides specificity to cardiolipin binding is not addressed in the present manuscript, our study clearly demonstrates that the isoleucine at 553 plays important role in determining cardiolipin specificity and nuclear recruitment. As pointed out by the reviewer, it is possible that changing isoleucine to methionine may affect the local conformation. However, there is no major conformational change in the DTD due to this mutation. This conclusion is based on clear loss of nuclear localization and cardiolipin interaction for the mutant without affecting other properties. The in vitro floatation assay clearly stablish that the effect is directly by inhibiting interaction specifically with cardiolipin containing membrane. It should be further noted that the same domain DTD interacts with other two lipids (PS and PA) and mutant retains interaction with them arguing that conformation of this domain is not significantly changed due to I to M mutation. Consistent with these results I553M mutant could be targeted to the nuclear membrane as a complex with wildtype Drp6 further confirming that I553 could form correct self-assembled structure with wildtype protein required for association with nuclear membrane. This is further substantiated by comparing all the known biochemical properties including GTPase activity, membrane binding via other two lipids, formation of helical spirals and ring structures. Hence it is clear that I553 provides specificity to bind cardiolipin and recruitment to the nuclear membrane. We will further confirm if there is any local conformation change due to the mutation I to M by fluorescence quenching experiments and will be incorporated in the revised manuscript.

Regarding overall folding of the mutant, this is an excellent suggestion by the reviewer. We are planning to perform CD experiments of the I553M mutant and wildtype proteins to compare if there is any change in overall folding due to mutation. This result would be incorporated in the revised manuscript.

Reviewer is right to point out that both electrostatic and hydrophobic interactions are important for interaction with cardiolipin. Electrostatic interaction is important for all the phospholipids while interacting with protein and is expected to come from other amino acid residues which are positively charged. Electrostatic interaction may contribute to the affinity of the interaction by providing additional binding energy. But considering its universal nature of interaction with all the phospholipids, it cannot give specificity for a specific lipid and hence would not discriminate among different phospholipids.

Regarding affecting hydrophobic component, the reviewer is correct that both are strong hydrophobic amino acids and loss of I553M interaction with cardiolipin may not be due to change in hydrophobicity

To address that the loss of cardiolipin interaction is not specific to methionine and is due to absence of isoleucine, the suggestion from the reviewer to replace I553 with A (alanine) is an excellent one. We are doing the experiments and we anticipate to incorporate these results in our revised manuscript.

Reviewer #1 (Significance (Required)):

The addressed phenomenon is restricted to Tetrahymena and may not have far reaching implications. Regardless, the identification of CL as a binding target for Drp6 at the nuclear membrane of this organism is in itself significant. The conclusion that I553 is the key CL binding residue is however not warranted. Additional experiments are needed to dissect how this residue impacts CL interactions and examine whether the observed effect is direct or indirect.

Response:

We thank the reviewer for appreciating the significance of this work. We agree that our data is Tetrahymena specific. However, we believe that the study is relevant for all the proteins whose association with target membranes depend on cardiolipin including many cardiolipin interacting DRPs (such as DRPs involved in biogenesis and maintenance of mitochondria).

We really appreciate the reviewer for the excellent suggestions. Based on this we are performing the following experiments.

1. CD experiments to assess overall folding of I553M and Wildtype protein
2. Fluorescence quenching of Tryptophan (at amino acid position 548) residue in the vicinity of I553 to compare conformation of the mutant with that of wildtype protein.
3. Evaluation of I553A in nuclear localization and cardiolipin binding. We anticipate these results to further confirm if I553 is the key CL binding residue and if the effect is direct.

The writing is not clear in some parts and may require a round of language editing. There are no issues with reproducibility.

Response

We thank the reviewer for pointing out the language editing. We will edit the language wherever we find it appropriate. We would highly appreciate if reviewer can indicate the portions that need special attention.

Reviewr #2:

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

Dynamin is a GTPase superfamily protein involved in membrane fusion and division. This paper focused on Drp6, one of the eight dynamin superfamily proteins of Tetrahymena, and analyzed its nuclear envelope localization mechanism by a combination of in vivo cytogenetical analysis and in vitro biochemical analysis for the various mutant Drp6 proteins. Results showed that a specific amino acid residue (isoleucine at the 553rd) in the membrane binding domain of Drp6 was required for its nuclear membrane localization, but this residue is not required for ER/endosome localization and GTPase activity. Furthermore, in vitro floating analysis using centrifugation indicated that Drp6 specifically bound to the cardiolipin at the 553rd isoleucine residue and this binding was required for Drp6's nuclear membrane localization. Finally, removal of cardiolipin from the conjugating cells using inhibitor treatment showed that cardiolipin was required for the new macronucleus formation (including the expansion of macronuclear envelope) through the function of Drp6. Based on these results, authors concluded that cardiolipin targets Drp6 to the nuclear membrane in Tetrahymena.

\*Major comments:***

The experimental data presented in this paper are reasonable and the results are solid, and therefore I think the deduced conclusions are convincing. However, to improve this paper, I have several minor comments to be revised before publication.

\*Minor comments:***

1. In the previous paper, it has been shown that GFP-Drp6 is localized in the inner nuclear membrane of both macronucleus and micronucleus. In this paper, however, this point is not clearly stated and is not shown in the figures --- I could not understand such localization pattern of GFP-Drp6 in Fig. 1C and Fig. 3b and the statements in the text. I suggest adding such statements somewhere in Introduction or Result section. Also, add adequate references to the corresponding statements in the text.
2. • Related to the comment 1, I suggest replacing Fig. 1C (images of fixed cells) with Fig. S1B (images of live cells) because nuclear localization of GFP-Drp6 are much clearer in Fig. S1B (live cell) than Fig. 1C (fixed cell), and because fixation may cause artificial redistribution of the proteins. Please add arrows in those figures to point out the position of micronucleus in those figures if necessary.*
3. • Similarly, I suggest replacing images of Fig. 5B (fixed cells) with those of Fig. S3 (live cells).*
4. • page 7, line 224: GFP-Nup3 is used as a marker protein of the nuclear pore complex (NPC). However, there is no description of how GFP-Nup3 is obtained or made. Add description how this DNA plasmid was obtained or generated.*
5. • Related to the comment 4, "Nup3" is first discovered in Malone et al., Eukaryotic Cells, 2009, but also soon after discovered as the name of "MicNup98B" in Iwamoto et al., Curr Biol, 2009 and used in several papers including Iwamoto et al., Genes Cells, 2010; JCS, 2015; JCS 2017; and more. Because Nup3 is the Tetrahymena paralogs of human Nup98 and the name of "Nup98" is well established to call these homologs in various eukaryotes, I suggest adding the name of "MacNup98B" after the word of "Nup3" for reader's better understanding. I also suggest adding appropriate references to refer to this protein as follows: Add Malone et al. 2009 for "Nup3" and Iwamoto et al., 2009 for "MacNup98B."*
6. • page 9, line 295: I wonder if "Fig. 3b" may be a mistake of "Fig. 5C." If so, please correct this.*
7. • page 10, the second paragraph (lines 311-322): This paragraph discussed the possible involvement of Drp6 in the nuclear envelope expansion of the post-zygotic nucleus. It may be interesting to point out that large-scale nuclear envelope reorganization including the formation of the redundant nuclear envelope and the type-switching of the NPC (from the MIC-type NPC to the MAC-type one) has been reported at this developmental stage (Iwamoto et al., JCS 2015). For example, the peculiar shaped nuclear envelope with the redundant/overlapping nuclear envelope structure can be seen and the MAC-type NPCs rapidly assembles to the expanding nuclear envelope. It may be interesting to point out that cardiolipin and Drp6 may be involved in these phenomena. But it is too speculative and therefore consider adding such a discussion as an option.*
8. • page 13, line 412: Is the word "GFP-drp6-I553M" written in italics intended for the gene for the GFP-drp6-I553M protein? If so, protein may be acceptable here. Make sure there are no problems with italicized characters. Also, check if the lowercase letter "d" in "drp6" is OK because large letters are used in other cases.*
9. • page 20, figure 1: I recommend switching the positions of HDyn1 and Drp6 in Figure 1a to keep the order in Figure 1b.*
10. • page 21, line 671: Add the word "Tetrahymena" before "Drp 6" to pair with the word "human dynamin 1".*
11. • page 23, line 729: Remove "and."*
12. • page 23, lines 729 and 731: Unify the expression of "cardiolipin" and "Cardiolipin"*
13. • page 23, line 732: Add "or" before "10% Phosphatidylserin."*
14. • page 24, Figure 3a: Please mark the position of I553M in the figure if possible. Alternatively, indicate the range of amino acid residues after the words "red" and "green" in the figure legend.* Response:

We thank the reviewer for the excellent comments that “the experimental data presented in this paper are reasonable and the results are solid, and therefore I think the deduced conclusions are convincing.” We also thank the reviewer for the minor comments which are thorough and very insightful. it will improve the manuscript substantially. We would incorporate all the changes in the revised manuscript.

Reviewer #2 (Significance (Required)):

The corresponding author and his colleagues have reported that Tetrahymena Drp6 is localized to the outer nuclear membrane of both macronucleus and micronucleus of Tetrahymena (Elde et al., 2005) and that Drp6 is required for the formation of new macronuclei during nuclear differentiation (Rahaman et al., 2008). Therefore, these parts are not novel.

The novelty of this study is as follows:

(1) The discovery of a specific amino acid residue (isoleucine at the 553rd) of Drp6 that is required for its nuclear membrane localization.

(2) the discovery of a lipid molecule, cardiolipin, as a critical partner for Drp6's nuclear membrane targeting.

(3) Discovery of involvement of cardiolipin in the new macronucleus formation (the expansion of macronuclear envelope) through the function of Drp6.

*

I think their findings are highly novel and will provide new insight into a field of cell biology. Especially, their findings will contribute to understanding how specific proteins targeted to the specific intracellular membranes. In addition, their methods (such as floatation assay) for analyzing the interaction between the protein of interest and lipid/liposomes will become an important tool.*

Response:

We are very happy to note that the reviewer has pointed out the significance of the present study. We fully agree with reviewer and appreciate thorough analysis and excellent conclusion from the reviewer.

FOX NEWS SUCKS

SO TRUE-- "just because someone consistently believes something doesn't mean that it's likely to be true"... "even if a large number of people consistently believe something, its credibility may be negligible" 1.

1) Theodore Schick Jr., Lewis Vaughn, How to Think About Weird Things: Critical Thinking for a New Age, (New York: McGraw-Hill Education, 2019), 84, e-book.

Reviewer #2:

The authors describe the dependence of the p-value on sample size (which is true by definition) and offer a solution, using simulated data and an applied example.

I'm not sure that the introduction successfully motivates the paper. It is unclear whether this is due to misunderstandings by the authors of some key points, or rather is a matter of awkward communication, such that the authors' intentions are accurately conveyed.

The authors note the link between the p-value and sample size. In particular, the authors suggest that statistical significance can be achieved by using a sufficiently large sample size, and they call this 'p-hacking'. I certainly don't recognise use of a large sample size as an example of p-hacking. Instead, this term refers to analytical behaviours which cause the p-value to lose its advertised properties (advertised type 1 error rate). Examples would include taking repeated looks at data without making any appropriate adjustment, trying tests on different groupings of data (and selecting results on the basis of significance), or trying different definitions of an outcome measure. The key point is that, when these actions are performed, reported p-values are no longer valid p-values - they do not behave as they are supposed to. So straight away the authors' argument becomes confusing. Are they criticising the behaviour of the valid p-value? Or are they trying to criticise behaviours that cause the p-value to lose its stated properties? This point remains very unclear. I believe the authors are attempting the former, but wrongly describe this as an example of p-hacking.

But other statements in the introduction invite further confusion. The authors say " even when comparing the mean value of two groups with identical distribution, statistically significant differences among the groups can always be found as long as a sufficiently large number of observations is available using any of the conventional statistical tests (i.e., Mann Whitney U-test (Mann and Whitney, 1947), Rank Sum test (Wilcoxon, 1945), Student's ttest (Student, 1908)) (Bruns and Ioannidis, 2016)." Again, it is unclear what the authors are trying to say here, and the statement is clearly false under the most obvious interpretation. If the authors are saying that significance will always be found when the null is true and model assumptions are correct provided that the sample size is large, then this is clearly false. In this case, the test will reject the null 5% of the time, using a significance threshold of 5%. The authors can easily confirm this for themselves with a simple simulation. Are the authors trying to make the point that the error rate is conditional not only on the null, but also on the test assumptions (and so when they are violated the test may reject erroneously?) They certainly do not state this, and the fact that they refer to 'identical distribution' suggests otherwise. Another way the test assumptions could be violated is if actual p-hacking (see examples above) were present, such that the reported p-values were no longer valid. Again, the authors do not tell us that this is what they mean, if they in fact do, and this would be a criticism of p-hacking behaviours rather than of the p-value.

When they write "big data can make insignificance seemingly significant by means of the classical p-value" they might be thinking of confusion between statistical and practical significance, which is a common misinterpretation made in the presence of large data size, but again, if this is what the authors are thinking of they should say it. The discussion by Greenland (Valid P-Values Behave Exactly as They Should: Some Misleading Criticisms of P-Values and Their Resolution With S-Values, especially section 4.3) seems to address the concerns raised by the authors fairly decisively. For a given parameter size, increasing sample size should produce stronger evidence against the null. The p-value does not tell you about the size of the parameter directly - it measures the discrepancy between the data and the null - interpreted correctly, there is no problem.

So, with apologies to the authors, I don't think they are successful in convincing the reader that there is a problem to be solved, and the manner of presentation (which may just be an issue of communicating the authors' intentions) is such that it causes doubt about the authors' handling of the relevant concepts. Throughout the text, there are other confusing presentations around fundamental concepts. E.g. the authors write things like "Hence, we claim that whenever there exist real statistically significant differences between two samples..." I know what a real difference is, but what is a real statistically significant difference? There are no statistically significant differences in nature. Are the authors trying to refer to instances where the null is false and is rejected? Or, are they trying to say that a 'real significant difference' is where the difference exceeds some magnitude?

For example - the authors write things such as "When 𝑁(0,1) is compared with 𝑁(0,1), 𝑁(0.01,1) and 𝑁(0.1,1), 𝜃 is null; so those distributions are assumed to be equal. In the remaining comparisons though, 𝜃 = 1, thus there exist differences between 𝑁(0,1) and 𝑁(𝜇,1) for 𝜇 ∈ [0.25,3]", highlighting the fact that perhaps the authors really want to address the practical significance vs statistical significance issue (although again, this is not explicitly stated). If the authors are interested in size of effect/ difference, then it is not clear that this proposal offers any advantage in that regard over the p-value (which, as noted, does not tell us about the size of a parameter). If interest is in size, then it is unclear why the authors do not direct the reader to consider the estimate and confidence interval, so that they may consider this explicitly in terms of magnitude and precision.

With apologies to the authors, who have clearly spent a large amount of time on this - I would think that the best way forward here would be to post this as a preprint and to try to invite as much feedback as possible. The authors have lofty ambitions with this work. Maybe there is a good underlying idea here, obscured by the presentation? Unfortunately, it is difficult to assess this at present.

Reviewer #1:

The paper sets out to confront p-hacking and addressing the dependence of the p-value on the sample size. The paper sets out the motivation behind the problem and then proposes a solution using three examples.

I have a major problem with this work in that I do not understand the motivation and hence cannot judge the value of the proposed solution.

The authors need to set out some definitions which might help them framing the context. I outline below what I understand as the context and hence why I do not understand how their proposal will address the problem.

Firstly 'p-hacking' is the term usually reserved for when researchers do not follow a pre-specified protocol on how a research question will be answered through the statistical analysis of a resource, single study or experiment, but instead analyse the data in many ways. Maybe they use slightly different assumptions, adjust the definition of an outlier or who is eligible for inclusion or adjust to a different outcome variable. In this manner they select to report the analysis that gives the smallest p-value. (Ioannidis referred to some of this as vibration effects) This is a major problem in science but it is not only the problem of the size of the data available. Although the bigger the dataset, the more subgroups that can be analysed. The main problem here is that we do not know how many ways the data have been analysed, we only know what researchers have selected to report. The manuscript does not address this problem at all.

The p-value is defined as the probability of observing a result as or more extreme when the null hypothesis is true. In most settings the 'null' is that there are no differences between two or more groups, for example that all the means are the same or equal. Often this translates into the statement that we expect the distribution of p-values under the null to be uniformly distributed [0,1]. This can be demonstrated or checked by simulation. In the hypothesis testing framework we usually power our studies so we will be able to detect a (true) difference between two groups with some high probability. The specific difference we are interested in would be called the alternative hypothesis. Hence the p-value is used to reject the null, but under the alternative hypothesis the p-value will not be uniform [0,1]. It is well known that the larger your sample size the more precise estimates you will obtain and the smaller differences you will be able to detect. Sample size calculations require a specific alternative to be stated (e.g. a difference in means of 0.5 of a standard deviation) then a sample size that guarantees as specific power for the specific type 1 error can be calculated.

This manuscript is confusing properties of the p-value when there are no differences and minimal differences between the two groups. I think the authors are trying to make the point that a statistically significant result is not necessarily a clinically or biologically meaningful result. They have done some simulations to show the distribution of the p-value when the true difference between the two means is 0.01. This is an example of an 'unimportant' difference, but it is not the null. This problem is best addressed by reporting effect sizes and 95% confidence intervals for quantities of interest rather than trying to adjust p-values in some way. Obviously when we have access to large datasets we may have a much larger sample than we needed to detect a meaningful effect though we may find small p-values. Adjusting the p-values will not really help as it is the effect sizes that are of interest.

I feel the manuscript needs to be redrafted to be more clear about the problem they are trying to fix.

This is the only useful idea in the text. Whatever we read has the context in which it was written and the context in whcih it is being read. Is this a hermeneutic circle as described earlier? Don't think so.

Author Response

We thank the editors and reviewers for taking the time to assess our paper. We note that the reviewers seemed generally supportive of the paper, including noting that the paper addressed important questions. For context, we reiterate here our main findings:

• a prefrontal cortex population encodes the past and the present in its joint activity, but solves the interference problem by encoding all features on independent axes for their past and their present.
• This encoding would in principle allow upstream regions to independently access representations of the past and present in mPfC populations. We go on to show this happens: we show that only the encoding of the present, and not the past, is reactivated in sleep after training.

In this context, the main editorial objection that we “did not control for potential confounding of behavioral variables” is not explained in the reviews; we also note that there were no “concerns about the analytical methods used” that were pertinent to our main findings. We are thus unclear about the basis for rejection.

We respond below to the main points of each reviewer; their suggestions on terminology and of separating literature citations on rodent and primate PfC are being given due consideration.

Reviewer #1:

Maggi and Humphries examined how the coding of the present and past choices in the medial prefrontal cortex (mPFC) of the rats during a Y-maze task overlaps and whether they can be reliably distinguished. They found that the neural signals related to the animal's choice in the present and past are distinct and as a result they can be recalled separately, for example, during post-training sleep. Although these are very important questions and an interesting set of analyses have been applied, the results in this report are not entirely convincing, because the analyses did not successfully exclude some alternative hypotheses.

1) The authors analyzed the signals related to the choice, light cue, and outcome separately, and this is possible because the relationship between the animal's choices and cues were decoupled by testing the animals under at least two different rules. There were a total of 4 alternative rules and different sessions included different subsets of these rules. It is possible that at least some results reported in this paper might vary depending on which of these results were tested. For example, rules might affect how the animals learned the task. Therefore, the authors should provide more detailed information about how often different rules were used to collect the neural data reported in this paper, and whether any of the results change according to the rules used in a given session.

In the paper we did examine mPfC encoding in the trials under the two qualitatively distinct types of rule (direction-based i.e. egocentric, and cue-based i.e. allocentric), and showed that encoding of the direction, light, and outcome occurred in both rule types (figure 1e). We gave the number of sessions for those rules in the legend for Figure 1e. (We could equally decode all 3 features in direction-based and cue-based rule sessions in the inter-trial interval as well, see Maggi et al 2018, Figure 9). Thus we compared the decoding vectors across all rule-types.

Only 8 sessions contained more than 1 rule, in the sessions in which the rule was switched. In the full analysis underlying this paper, we had also separately examined the decoding in these 8 rule-switch sessions, and found equally good decoding of direction, choice, and cue. As the paper was already dense - see e.g. Reviewer 3’s comments - we elected to not show this null result in the current version of the manuscript - it is available in version 1 of this preprint - but it can be restored if desired.

2) The authors claim that the neural coding identified in this study does not depend on the signals in individual neurons by showing comparable results after removing the neurons with significant modulations. This logic is flawed, because the neurons without "significant" modulations might still include meaningful signals due to type II errors. Furthermore, if individual neurons carry absolutely no signals, how can a population of neurons still encode any signals? This might suggest some kind of joint coding, and the authors should not merely implicate such a possibility without more thorough tests.

The joint coding of information by a population of neurons is the basis for the whole paper, and is tested extensively: for example, Figure 1 is about establishing that joint coding exists in mPfC. Our point on lines 91-95 was simply to show that the decoding could not be trivially explained by one or two neurons that reliably and strongly differed in the firing rates between different labels (e.g. between left or right choice of direction). To do so, we found sessions in which there were neurons with significantly detectable tuning to the task feature, omitted those sessions, and then looked at the performance of the feature decoding in the remaining sessions - and found it was just as good. Indeed, our point is precisely that it is possible for individual neurons to carry no signals detectable by classic significance testing (potentially due to Type II errors), yet for the population to be able to perfectly encode the information.

The explanation is simply that most, and sometimes all, individual neurons do not consistently covary their firing with the changes in a feature (e.g. choose left and choose right trials) across every trial of a session. In other words, no neuron need consistently participate in encoding information. But so long as when a neuron does change its firing it does consistently vary with the feature, then across a population there are enough intermittently participating neurons on a given trial to always decode the information.

3) The authors analyzed the activity divided into 5 different epochs, where the position #3 corresponds to a choice point and #5 corresponds to the reward site. Therefore, it is surprising that the reliable outcome signals begin to emerge from the position #3 (i.e., choice point). Is this a false positive?

No, this replicated a common finding of outcome-predictive signals in prefrontal cortex; e.g. Daw, N. D., O’Doherty, J. P., Dayan, P., Seymour, B. & Dolan, R. J. Cortical substrates for exploratory decisions in humans. Nature 441, 876–879 (2006).

Fellows, L. K. Advances in understanding ventromedial prefrontal function: the accountant joins the executive. Neurology 68, 991–995 (2007).

Sul, J. H., Kim, H., Huh, N., Lee, D. & Jung, M. W. Distinct roles of rodent orbitofrontal and medial prefrontal cortex in decision making. Neuron 66, 449–460 (2010).

Kaplan, R. et al. The neural representation of prospective choice during spatial planning and decisions. PLoS Biol. 15, e1002588 (2017).

We will add these references to the next version of the manuscript.

4) The authors report that there is retrospective coding, i.e., no coding of the choice in the previous. By contrast, during the intertrial interval (while the animal's returning to the start position), the signals related to the "past" choice were still present but different from how this information was coding earlier during the trial. This is not surprising since during the intertrial interval, the animal's movement direction is opposite compared to that during the trial, so this coding change could reflect the animal's sensory environment. Whether the brain encodes the past and previous events using different coding schemes or not cannot be tested with such confounding.

We note that the reviewer’s objection here only relates to the choice of arm direction, whereas we showed independent encoding of all three features: direction, outcome, and cue position. We can thus test how the past and present are differently encoded because we showed they are both encoded in the same set of neurons. We showed at length both here (Figure 2a&c, Supplementary Figure 5a) and in Maggi et al 2018 (Figs 5-6 and accompanying supplementary figures) that we could decode the past events from the population activity during the inter-trial interval. The information of the trial and the inter-trial interval can be decoded from the same neurons, so the question is: how can the same neurons encode both the present and the past?

One interpretation of the reviewer’s comments is that they are concerned about the possible confounding of movement direction between the trial and the following inter-trial interval. Namely, that the turn directions are guaranteed to be opposite: e.g a left turn into the left-hand arm on the trial would mean a right-hand turn on the return journey of the inter-trial interval. However, that would mean the feature labels would be exactly complementary e.g. trial =[L L R L R] and ITI = [R R L R L]. So if the population was encoding the direction choice the same way in both the trial and ITI, then using the trial’s decoder of direction to decode direction choice in the ITI should result in a performance of 1-[proportion of correctly classified trials], meaning the classifier would be significantly below chance (and vice-versa for using the inter-trial interval’s decoder for the trials). However, we find the cross-decoding performs at chance (Fig 2).

5) The authors tested whether the coding of present and past events is consistent using a transfer (cross-decoding) analysis. However, this is based on simply correlation, and does not exclude the possibility that neurons changing their activity similarly according to (for example) the animal's choice might also change their baseline activity between the two periods (as revealed by the analysis of "population activity" in Figure 3) or might additionally encode different variables. In this case, decoding based on simple correlation might not reveal consistent coding that might be present.

It is unclear what the referee means by the cross-decoding analysis being “based on simple correlation”. The decoder is trained on vectors of firing rates (cf Figure 1b). The decoder assigns high weights to neurons whose activity differs most strongly between the two labels (e.g. left and right choice of direction). So a change in “baseline”, presumably meaning the average firing rate of a neuron across all trials or all ITIs, would not alter the decoder outcome. In addition to the two cross-decoding tests, we also showed the independent encoding by: (a) The angles formed by the decoding vectors trained solely on the trials and solely on the ITIs (Fig 2d-f) (b) The independence of the population rate vectors between trials and ITIs (Fig 3). Indeed, the change in population rates between trials and ITIs shown in Figure 3 is exactly those predicted by the cross-decoding results, as explained on pg 7.

Reviewer #2:

The study by Maggi and Humphries re-examines data by Peyrache et al. (2009), which the authors have themselves analysed previously (Maggi et al., 2018), recorded , in rat prelimbic/infralimbic cortex (see comment below on terminology). In particular, they look at the relationship between decoding of task events during performance of a trial, and during the subsequent intertrial interval. (n.b. in this study, unlike in many studies, the ITI is considerably longer than the trial period). They find that although task-relevant information can be decoded during these two periods, the information is encoded in orthogonal subspaces during trials ('the present') and ITIs ('the past'). They build on this to examine how information is encoded during sleep following training (vs a pre-training control period). They find that only the trial subspaces are reactivated during sleep, not the ITI subspaces, and more so if the rat received a higher rate of average reward.

On the whole, I found this an interesting paper with a clear set of findings, and well-analysed data. Although the advance in some ways an incremental one on previous studies of sleep/replay, and on the authors' previous analyses of this dataset, the study will undoubtedly be of interest to researchers who are interested in consolidation of past experience during sleep. In particular, the study benefits from being able to look for two different types of information ('past' and 'present' decoders) in the same sleep recording sessions. There were a few things that I felt the authors could address:

1) For the cross-decoding analysis in figure 2 b, it is not entirely clear from the main text which part of the trial and ITI coding is being used here. It seems to me like a more useful way of showing the cross-decoding analysis would be to show the 10x10 matrix of cross decoding accuracy for each of the 5 maze positions in both trials and ITIs. This is, I think, different from what the analysis in figure 3g is trying to show (which plots the classification error after dimensionality reduction to a 2D space).

As we strived to explain in the text, for the cross-decoding analysis we used the decoder trained on the firing rates across the entire trial and separately across the entire ITI, in order to arrive at the most stable decoding vectors. We did not show the cross-decoding for the full 5x5 matrix of positions, as the results would be quite noisy. Nevertheless, this is a constructive suggestion, and we will add this analysis. (And indeed the analysis in Figure 3 already shows that the population activity is separable in 1 or 2 dimensions between the trials and ITIs at each maze position, so we would expect the decoder weight vectors to also be independent).

2) It was surprising to me that the authors do not mention the finding in figure 4e anywhere in the abstract or introduction. It makes the reactivation story far more compelling if it can be linked to a change in behaviour during the preceding trials. I think this finding would benefit from not being buried deep in the results section.

We are happy to make this result clearer. Our main finding is of the independent coding, and this result in Fig 4e does not speak directly to the independent coding results, but rather is a lovely little result to support the hypothesis that there really is reactivation of the population vectors in sleep. Because it did not speak to the main thrust of the paper, it was omitted from the abstract given the constraints on the number of words (150).

3) The finding in figure 5 seems slightly extra-ordinary. It suggests that reactivation decoding during sleep is reliable even if very long bins of activity are used to calculate the firing rate (e.g. up to 10s). Does this relationship ever break down? Presumably with the sleep data, it would be possible to extend bins up to 1 minute, 5 minutes, etc. If there is still more reactivation at these extremely long time-bin lengths, does this mean that these neurons are essentially more persistently active? One possible way to test for this might be to project the data recorded during sleep through the classifier weights, and then calculate the autocorrelation function of this projected data (e.g. Murray et al., Nat Neuro 2014) - if this activity becomes more persistent, the shape of the ACF may change post-training.

An excellent question. Rather than persistent activity, we interpreted the consistency of reactivation across orders of magnitude time-scales as showing that the correlations between the neurons were roughly consistent; and thus when active tended to be active in roughly the same relative order. Support for this comes from the findings in Appendix Fig A4e - the correlation matrix between neurons in the trial was more consistently found in post than pre-session sleep.

Reviewer #3:

This article asks the question if within trial (present) and ITI (past) task parameters are encoded in mPFC, and how encoding during these two trial epochs are encoded. They claim that firing in mPFC reflects past and present, but population encoding of past and present are independent. Further they show that the present is reactivated during sleep, not the past.

On the face of it, this seems like an interesting paper. It is novel in that ITI encoding would be highly related to what was going on in the trial. The sleep finding is also interesting but I don't quite get the distinction between present and past for sleep. That could use some clarification.

1) I'm not an expert in regards to this type of analysis, but throughout I was left with the feeling that I would prefer at least some single neuron data and firing rate analysis to complement the highly computational analysis, which frankly, was difficult to understand or critique by somebody who is not an expert.

The goal of the paper is to assess the population coding in PfC of the same events in the past and the present. Indeed, as reported in the paper, we found 25-39 sessions which had no single neuron tuning at all to a given event in a trial (such as the choice of maze arm).

2) I would have liked to see more analysis of firing correlations with behavior. It seems to me if animals were doing different things during the trial and the ITI, then it might not be a surprise that there is independent encoding.

3) I also wonder if the finding is solely dependent on the task (which is poorly described). It seems like there should be independent coding of past and present in this circumstance because they do not feed into each other, and behavior during one is independent of behavior in the other.

4) Relatedly, the authors suggest that independent encoding can explain how the brain resolves interference between past and present, but in this task there was no interference between past and present, and the authors do not show that when there is more or less dependent encoding that there is more or less interference. Without it is unclear how to know how important this finding is as it relates to performance and general mPFC function.

We deal with these points together, as they are all on the behaviour in the trial and inter-trial interval in the task. Yes, the behaviour in the trial is independent of that in the inter-trial interval, so there is no “interference” of behaviour. But that is not of relevance to what is encoded in the PfC. The Introduction and Discussion both point out that the problem is interference of the encoding itself: the encoding of the past and present exists, as we show at length, so the question is: how can it co-exist in the same neurons? We indeed ask if there is no “interference” in the encoding simply because activity in the inter-trial interval is just a memory trace of activity in the trial, and rule that out.

We cannot address when there is “more or less dependent” encoding, because the results are what they are: there is independent encoding of the same events (Figure 2).

The task is described in detail in the Methods (pgs 20-21).

5) Could activity reflect what the animal predicts will happen on the next trial, or what they are planning to do? It wasn't clear if that was examined.

Whether activity in the inter-trial interval predicted what will happen in the next trial was examined in detail in Maggi et al 2018 (Fig 6), and shown here in Figure 2g. We found no encoding of the following trial’s choices, except for a very niche occurrence: an above chance decoding of the next trial’s direction choice when the rat had returned to the start position, during a learning session, and for a direction rule. In other words, as it turned to start the next trial, so there was decoding of the upcoming choice of arm.