Author Response

Reviewer #3 (Public Review):

Main results:

1) TCR convergence is different from publicity: The authors look at CDR3 sequence features of convergent TCRs in the large Emerson CMV cohort. Amino usage does not perfectly correlate with codon degeneracy, for example, arginine (which has 6 codons) is less common in convergent TCRs, whereas leucine and serine are elevated. It's argued that there's more to convergence than just recombination biases, which makes sense. (I wonder if the trends for charged amino acids could be explained by the enrichment of convergent TCRs in CD8 T cells, which tend to have more acidic CDR3 loops). There's also a claim that the overlap between convergent and public TCRs is lower in tumors with a high mutational burden (TMB), but this part is sketchy: the definition of public TCRs is murky and hard to interpret, and the correlation between TMB and convergence-publicity overlap is modest (two cohorts with low TMB have higher overlap, and the other three have lower, but there is no association over those three, if anything the trend is in the other direction). It's also not clear why the overlap between COVID19 cohort convergent TCRs and public TCRs defined by the pre-2019 Emerson cohort should be high. A confounder here is the potential association between convergence and clonal expansion since expanded clonotypes can spawn apparently convergent TCRs due to sequencing errors. The paper "TCR Convergence in Individuals Treated With Immune Checkpoint Inhibition for Cancer" (Ref#5 here) gives evidence that sequencing errors may be inflating convergence in this specific dataset.

We really appreciate the reviewer’s feedback. We respond to each of the reviewer’s points below:

(1) Amino acid preference of convergent TCRs might be caused by CD8+ T cell enrichment. To test this hypothesis, we performed the same analysis using only CD8+ T cells (using the Cader 2019 lymphoma cohort). The results are shown below. We do not observe significant changes after excluding CD4+ T cells, indicating that this enrichment might be caused by factors other than CD4/CD8 differences.

(2) Definition of public TCRs. We have changed the definition of public TCRs. Instead of mixing the Emerson cohort into each group and using the mixed cohort to define the public TCRs, we just used the 666 samples of the Emerson cohort to define the same set of public TCRs and applied them to each cohort. Both the dataset and the approach used in this manuscript is consistent with a previous study on the same topic (Madi et al., 2014, elife).

(3) Convergence-publicity overlap: We agree with the reviewer that some high TMB tumors did not show further decrease of convergence-publicity overlap. One potential explanation is that the correlation between the two is not linear. By adding additional cohorts in this revision (healthy and recovered COVID-19 patients), we confirmed the previously observed overall trend between TMB and the overlap, which supported our conclusions (see figure below). On the other hand, we believe that the high overlap of convergent TCRs among healthy cohorts might result from exposure to common antigens. In the cancer patients, while still exposed, private antigens derived from tumor cells are expected to compete for resources, thus reducing the proportion of these public TCRs in the blood repertoire. The above discussion has been added to the revised manuscript:

“Healthy individuals are expected to be exposed to common pathogens, which might induce public T cell responses. On the other hand, cancer patients have more neoantigens due to the accumulative mutation, which drives their antigen-specific T cells to recognize these 'private' antigens. This reduces the proportion of public TCRs in antigen-specific TCRs. Furthermore, a higher tumor mutation burden (TMB) would indicate a higher abundance of neoantigens, resulting in a lower ratio of public TCRs.”

2) Convergent TCRs are more likely to be antigen-specific: This is nicely shown on two datasets: the large dextramer dataset from 10x genomics, and the COVID19 datasets from Adaptive biotech. But given previous work on TCR convergence, for example, the Pogorelyy ALICE paper, and many others, this is also not super-surprising.

We thank the reviewer for bringing up this related work. In the Pogorelyy ALICE paper, the authors defined TCR neighbors based on one nucleotide difference of a given CDR3, which included both synonymous and non-synonymous changes. In other words, ALICE combines both convergence and mismatched (with hamming distance 1) sequences as neighbors. Although highly relevant, our approach is different by focusing only on the convergence, as mismatch has been extensively investigated by previous studies. We have now added this paper as Ref 27, and discussed the difference between ALICE and our method in the revised manuscript.

3) Convergent T cells exhibit a CD8+ cytotoxic gene signature: This is based on a nice analysis of mouse and human single-cell datasets. One striking finding is that convergent TCRs are WAY more common in CD8+ T cells than in CD4+ T cells. It would be interesting to know how much of this could be explained by greater clonal expansion of CD8+ T cells, together with sequencing errors. A subtle point here is that some of the P values are probably inflated by the presence of expanded clonotypes: a group of cells belonging to the same expanded clonotype will tend to have similar gene expression (and therefore similar cluster membership), and will necessarily all be either convergent or not convergent collectively since they share the same TCR. So it's probably not quite right to treat them as independent for the purposes of assessing associations between gene expression clusters and convergence (or any other TCR-defined feature). You can see evidence for clonal expansion in Figure 3C, where TRAV genes are among the most enriched, suggesting that Cluster 04 may contain expanded clones.

(1) We agree with the reviewer that a possible explanation of the CD8/CD4 difference is the larger cell expansion of CD8+ T cells. We tested this hypothesis by counting the number of T cell clones instead of cell number to remove the effect that would have been caused by CD8 T cell expansion. We first investigated the bulk TCR repertoire sequencing samples as Figure 3 - figure supplement 2C-2D (see figure below). We observed higher convergence levels for the CD8+ T cell clones compared to CD4+ T cells. The additional description of this topic was added at the last paragraph of the result section of “Convergent T cells exhibit a CD8+ cytotoxic gene signature” as follows:

“The results may be explained by larger cell expansions of CD8+ T cells than CD4+ T cells. Therefore, we calculated the number of convergent clones within CD8+ T cells and CD4+ T cells from the above datasets to exclude the effects of cell expansion. As a result, in the scRNA-seq mouse data, while only 1.54% of the CD4+ clones were convergent, 3.76% of the CD8+ clones showed convergence. Likewise, 0.17% of convergent CD4+ T cell clones and 1.03% of convergent CD8+ T cell clones were found in human scRNA-seq data. In the bulk TCR-seq lymphoma data, similar results were also observed, where the gap between the convergent levels of CD4+ and CD8+ T cells narrowed but remained significant (Figure 3—figure supplement 2C-2D). In conclusion, these results suggest that CD8+ T cells show higher levels of convergence than CD4+ T cells, which substantiated our hypothesis that convergent T cells are more likely antigen-experienced. This observation has been tested using multiple datasets with diverse sequencing platforms and sequencing depth to minimize the impact of batch or other technical artifacts.”

(2) We next investigated the effect of cell expansion in the single cell analysis. We agree with the reviewer that some highly-expanded convergent clones could inflate the p-value. Therefore, we revised the calculation of TCR convergence by using the T cell clone instead of individual cells. We observed that the clusters of interest mentioned in the paper (for both mouse and human data) remain at the top convergent level among all clusters (see table below), with p values estimated using Binomial exact test. These results supported our hypothesis that TCR convergence is enriched for T cell clusters that are more likely antigen-experienced.

4) TCR convergence is associated with the clinical outcome of ICB treatment: The associations for the first analysis are described as significant in the text, and they are, but just barely (0.045 and 0.047, but you have to check the figure to see that).

As suggested by the reviewer, we have added the p-value to the test so that it is easier to see. In this revision, we adopted another definition of convergent level, changing from the ratio of convergent TCR to the actual number of convergent T cell clones within each sample. The p-values were more significant using this new indicator (0.02 and 0.00038). To avoid the effect of other variables that might be correlative with convergent levels, especially the sequencing depth, the multivariate Cox model was used for both datasets tested in the paper, correcting for TCR clonality, TCR diversity and sequencing depth (and different treatment methods for melanomas data). As a result, convergence remains significantly prognostic after adjusting for the additional variables.

5) Introduction/Discussion: Overall, the authors could do a better job citing previous work on convergence, for example, papers from Venturi on convergent recombination and the work from Mora and Walczak (ALICE, another recombination modeling). They also present the use of convergence as an ICB biomarker as a novel finding, but Ref 5 introduces this concept and validates it in another cohort. Ref 5 also has a careful analysis of the link between sequencing errors and convergence, which could have been more carefully considered here.

We thank the reviewer for this excellent suggestion. We have added the citation of Venturi on convergent recombination as Ref 43 and we cited it at the last paragraph of the result selection:

“Convergent recombination was claimed to be the mechanistic basis for public TCR response in many previous studies(Quigley et al., 2010; Venturi et al., 2006).”

We also included work from Mora and Walczak in the fourth paragraph of the introduction and the third paragraph of the discussion as Ref 27 to introduce this TCR similarity-based clustering method as well as its application in predicting ICB response:

“This idea has led several TCR similarity-based clustering algorithms, such as ALICE (Pogorelyy et al., 2019), TCRdist (Dash et al., 2017), GLIPH2 (Huang et al., 2020), iSMART (Zhang et al., 2020), and GIANA (Zhang et al., 2021), to be developed for studying antigen-driven T cell expansion during viral infection or tumorigenesis.”

“In addition, the potential prognostic value of TCR convergence and TCR similarity-based clustering was testified in other studies(Looney et al., 2019; Pogorelyy et al., 2019).”

Ref 5 was recited while discussing the effect of sequencing error on TCR convergence in the fourth paragraph of discussion:

“Improper handling of sequencing errors may result in the overestimation of TCR convergence (Looney et al., 2019).”

Author Response

Reviewer #1 (Public Review):

Kazrin appears to be implicated in many diverse cellular functions, and accordingly, localizes to many subcellular sites. Exactly what it does is unclear. The authors perform a fairly detailed analysis of Kazrin in-cell function, and find that it is important for the perinuclear localization of TfN, and that it binds to members of the AP-1 complex (e.g., gamma-adaptin). The authors note that the C-terminus of Kazrin (which is predicted to be intrinsically disordered) forms punctate structures in the cytoplasm that colocalize with components of the endosomal machinery. Finally, the authors employ co-immunoprecipitation assays to show that both N and C-termini of Kazrin interacts with dynactin, and the dynein light-intermediate chain.

Much of the data presented in the manuscript are of fairly high quality and describe a potentially novel function for Kazrin C. However, I had a few issues with some of the language used throughout, the manner of data presentation, and some of their interpretations. Most notably, I think in its current form, the manuscript does not strongly support the authors' main conclusion: that Kazrin is a dynein-dynactin adaptor, as stated in their title. Without more direct support for this function, the authors need to soften their language. Specific points are listed below.

Major comments:

1) I agree with the authors that the data provided in the manuscript suggest that Kazrin may indeed be an endosomal adaptor for dynein-dynactin. However, without more direct evidence to support this notion, the authors need to soften their language stating as much. For example, the title as stated would need to be changed, as would much of the language in the first paragraph of the discussion. Alternatively, the manuscript could be significantly strengthened if the authors performed a more direct assay to test this idea. For example, the authors could use methods employed previously (e.g., McKenney et al., Science 2014) to this end. In brief, the authors can simply use their recombinant Kazrin C (with a GFP) to pull out dynein-dynactin from cell extracts and perform single molecule assays as previously described.

While this is certainly an excellent suggestion, the in vitro dynein/dynactin motility assays are really not straight forward experiments for laboratories that do not use them as a routine protocol. That is why we asked Dr. Thomas Surrey (Centre for Genomic Regulation, Barcelona), an expert in the biochemistry and biophysics of microtubule dynamics, to help us with this kind of analysis. In their setting, TIRF microscopy is used to follow EGFPdynein/dynactin motility along microtubules immobilized on cover slides (Jha et al., 2017). As shown in figure R1, more binding of EGFP-dynein to the microtubules is observed when purified kazrin is added to the assay (from 20 to 400 nM), but there is no increase in the number or processivity of the EGFP-dynein motility events. These results are hard to interpret at this point. Kazrin might still be an activating adaptor but a component is missing in the assay (i. e. an activating posttranslational modification or a particular subunit of the dynein or dynactin complexes), or it could increase the processivity of dyneindynactin in complex with another bona fide activating adaptor, as it has been demonstrated for LIS1 (Baumbach et al., 2017; Gutierrez et al., 2017). Alternatively, kazrin could transport dynactin and/or dynein to the microtubule plus ends in a kinesin 1-dependent manner, in order to load the peripheral endosomes with the minus end directed motor (Yamada et al., 2008).

Figure R1. Kazrin C purified from E. coli increases binding of dynein to microtubules but does not increase the number or processivity of EGFP-dynein motility events. A. TIRF (Total Internal Reflexion Fluorescence) micrographs of microtubule-coated cover slides incubated in the presence of 10 nM EGFP-dynein and 20 nM dynactin in the presence or absence of 20 nM kazrin C, expressed and purified from E. coli. B. Kymographs of TIRF movies of microtubule-coated cover slides incubated in the presence of purified 10 nM EGFP-dynein, 20 nM dynactin and either 400 nM of the activating adaptor BICD2 (1:2:40 ratio) (left panel) or kazrin C (right panel). Red squares indicate processive dynein motility events induced by BICD2”.

Investigating the molecular activity of kazrin on the dynein/dynactin motility is a whole project in itself that we feel it is out of the scope of the present manuscript. Therefore, as suggested by the BRE, we have chosen to soften the conclusions and classify kazrin as a putative “candidate” dynein/dynactin adaptor based on its interactome, domain organization and subcellular localization, as well as on the defects installed in vivo on the endosome motility upon its depletion. We also discuss other possibilities as those outlined above.

2) I'm not sure I agree with the use of the term 'condensates' used throughout the manuscript to describe the cytoplasmic Kazrin foci. 'Condensates' is a very specific term that is used to describe membraneless organelles. Given the presumed association of Kazrin with membrane-bound compartments, I think it's more reasonable to assume these foci are quite distinct from condensates.

We actually used condensates to avoid implying that the kazrin IDR generates membraneless compartments or induces liquid-liquid-phase separation, which is certainly not a conclusion from the manuscript. However, since all reviewers agreed that the word was misleading, we have substituted the term condensates for foci throughout the manuscript.

3) The authors note the localization of Tfn as perinuclear. Although I agree the localization pattern in the kazKO cells is indeed distinct, it does not appear perinuclear to me. It might be useful to stain for a centrosomal marker (such as pericentrin, used in Figure 5B) to assess Tfn/EEA1 with respect to MT minus ends.

We have now changed the term perinuclear, which implies that endosomes surround the nucleus, by the term juxtanuclear, which more accurately define what we wanted to indicate (close to). We thank the reviewer for pointing out this lack of accuracy. We also more clearly describe in the text that in fibroblast, the Golgi apparatus and the Recycling Endosomes (REs) gather around the pericentriolar region ((Granger et al., 2014) and reference therein), which is usually close to the nucleus ((Tang and Marshall, 2012) and references therein). Nevertheless, as suggested by the reviewer, we have included pictures of the TxR-Tfn and EEA1-labelled endosomes accumulating around pericentrin in wild type mouse embryonic fibroblast (MEF) (Figure 1–supplement figure 3) to illustrate these points.

4) "Treatment with the microtubule depolymerizing drug nocodazole disrupted the perinuclear localization of GFP-kazrin C, as well as the concomitant perinuclear accumulation of EE (Fig. 5C & D), indicating that EEs and GFP-kazrin C localization at the pericentrosomal region required minus end-directed microtubule-dependent transport, mostly affected by the dynactin/dynein complex (Flores-Rodriguez et al., 2011)."

• I don't agree that the nocodazole experiment indicates that minus end-directed motility is required for this perinuclear localization. In the absence of other experiments, it simply indicates that microtubules are required. It might, however, "suggest" the involvement of dynein. The same is true for the subsequent sentence ("Our observations indicated that kazrin C can be transported in and out of the pericentriolar region along microtubule tracks...").

We agree with the reviewer. To reinforce the point that GFP-kazrin C localization and the pericentriolar accumularion of EEA1 rely on dynein-dependent transport, we have now added an experiment in figure 5E and F, where we use ciliobrevin to inhibit dynein in cells expressing GFP-kazrin C. In the treated cells, we see that the GFP-kazrin C staining in the pericentrin foci is lost and that EEs have a more dispersed distribution, similar to kazKO MEF. We have also completed and rearranged the in vivo fluorescence microscopy data to more clearly show that small GFP-kazrin C foci can be observed moving towards the cell centre (Figure 5-S1 and movies 6 and 7). Taken all this data together, I think we can now suggest that kazrin might travel into the pericentriolar region, possibly along microtubules and powered by dynein.

5) Although I see a few examples of directed motion of Tfn foci in the supplemental movies, it would be more useful to see the kymographs used for quantitation (and noted by the authors on line 272). Also related to this analysis, by "centripetal trajectories", I assume the authors are referring to those moving in a retrograde manner. If so, it would be more consistent with common vernacular (and thus more clear to readers) to use 'retrograde' transport.

We have now included some more examples of the time projections used in the analysis in figure 6-S1 and 2, where we have coloured in blue the fairly straight, longer trajectories, as opposed to the more confined movements that appeared as round dots in the time projections (coloured in red). We have also added more videos illustrating the differences observed in cells expressing endogenous or GFP-kazrin C versus kazKO cells or kazKO cells expressing GFP or GFP-kazrin C-Nt. Movies 8 and 11 show the endosome motility in representative WT and kazKO cells (movie 8) and kazKO cells expressing GFP, GFPkazrin C or GFP-kazrin C Nt (movie 11). Movies 9 and 10 show endosome motility in four magnified fields of different WT and kazKO cells, where longer and faster motility events can be observed when endogenous kazrin is expressed. Movies 12 to 14 show endosome motility in four magnified fields of different kazKO cells expressing, GFP-kazrin C (movie 12), GFP (movie 13) and GFP-kazrin C-Nt (movie 14). Longer and faster movements can be observed in the different insets of movie 12, as compared with movies 13 and 14. Finally, as suggested by the reviewer, we have re-worded centripetal movement to retrograde movement throughout the manuscript.

6) The error bars on most of the plots appear to be extremely small, especially in light of the accompanying data used for quantitation. The authors state that they used SEM instead of SD, but their reasoning is not stated. All the former does is lead to an artificial reduction in the real deviation (by dividing SD by the square root of whatever they define as 'n', which isn't clear to me) of the data which I find to be misleading and very nonrepresentative of biological data. For example, the error bars for cell migration speed in Figure 2B suggest that the speeds for WT cells ranged from ~1.7-1.9 µm/sec, which I'm assuming is largely underrepresenting the range of values. Although I'm not a statistician, as someone that studies biochemical and biological processes, I strongly urge the authors to use plots and error bars that more accurately describe the data to your readers (e.g., scatter plots with standard deviation are the most transparent way to display data).

We have now changed all plots to scattered plots with standard deviations, as suggested.

Author Response

Reviewer #2 (Public Review):

Wang et al. elegantly exploit single-cell RNA-seq datasets to question the putative involvement of lncRNAs in human germ cell development. In the first part of the study, the authors use computational approaches to identify and characterize, from existing data, lncRNAs expressed in the germline. Of note, the scRNA-seq data used were generated from polyA+ RNAs, and thus non-polyadenylated lncRNAs could not be retrieved. Most of the lncRNAs identified in the germ cells and in the somatic cells of the gonads were previously unannotated. While this increases the catalog of lncRNA genes in the human genome, further characterization is needed to determine which fraction of these newly identified lncRNAs represent bona fide transcripts or transcriptional noise.

Differential expression analysis between developmental stages, sexes, or cell types led to several observations: (i) whatever the stage of development, the number of expressed lncRNAs is higher in fetal germ cells compared to gonadal somatic cells; (ii) there is a continuous increase in the number of expressed lncRNA during the development of the germline; of note, a similar, although the more subtle trend is observed for protein-coding genes; (iii) the developmental stage at which there is the highest number of lncRNA expressed differs between male and female germ cells. While convincing, the significance of these observations is difficult to assess. However, the authors remain prudent with their conclusion and are not over-interpreting their findings.

We appreciate Reviewer #2 precise summary of our analysis and highlighting the significances of these datasets for other researchers and future studies.

Interestingly, integrating lncRNA expression to classify cell types led to the identification of a novel population of cells in the female germline that had not been revealed by protein-coding gene only-based classification. The biological relevance of this population, which cluster with mitotic populations, remains to be demonstrated. Finally, by examining lncRNA biotype, the authors could demonstrate an enrichment, in the germ cells, of the antisense head-to-head organization (in relation to the nearby protein-coding gene) compared to other biotypes. Whether this is different from the general distribution of lncRNA should be discussed.

We analyzed the lncRNAs in NONCODEv5 database (human genome), and the result showed that XH type occupied 21.73% of the intragenic lncRNA-mRNA pairs in NONCODEv5 database (human genome), which is lower than 26.58% in fGC and 26.23% in mGC (Response Figure 1).

Response Figure 1. Genomic distribution and biotypes of the lncRNAs in NONCODEv5 database and lncRNAs expressed in human gonad.

In the second part of the manuscript, Wang et al focus on one pair of divergent lncRNA-protein coding genes (LNC1845-LHX8). To document the choice of this particular pair, it would be informative to have its correlation score indicated in Figure 3C. he existence of this transcript was validated using female fetal ovaries, and its function was addressed in late primordial germ cells like cells (PGCLC) derived from human embryonic stem cells (hESCs). The authors have used an admirable set of orthogonal approaches that led them to conclude as to a role for LNC1845 in regulating in cis the nearby gene LHX8. They further went on to identify the underlying mechanisms, which involve modification of the chromatin landscape through direct interaction of LNC1845 with a histone modifier. Among the different strategies used (KO, stop transcription, overexpression), the shRNA-mediated knock-down is the only one to specifically address the function of the transcript itself, as opposed to the active transcription. The result of this experiment led the authors to conclude that the LNC1845 RNA is functional, a conclusion that is reinforced by the demonstration of physical interaction between the LNC1845 RNA and WDR5, a component of MLL methyltransferase complexes. The result of the KD experiment is however puzzling as RNAi has been shown not to be the method of choice for targeting nuclear lncRNAs (Lennox et al. NAR 2016).

We thank the Reviewer #2’s suggestion to add the correlation score of LNC1845-LHX8 pair and the Pearson Correlation of this pair is 0.3268. We have added the number to Figure 4C because which the expression correlation of LNC1845 and LHX8 was first mentioned. We have compared many other similar studies, shRNA knockdown has been widely used to target nuclear lncRNAs (Guttman et al. Nature 2011; Luo et al. Cell Stem Cell 2016; Subhash et al. Nucleic Acids Res. 2018; Li et al. Genome Res 2021), and the knockdown efficiency seemed to be feasible and acceptable to be used. The knockdown results are consistent with the deletion mutation and stop transcription approaches, all three showed that LNC1845 transcriptional expression is required for proper LHX8 expression in late PGCLCs.

Overall, the functional investigation is convincing and strengthened by the inclusion of multiple clones for each approach, and by the convergence in the outcome of each individual approach. The depth of characterization is also remarkable. The analyses of the mechanisms at stake are somehow less solid, as there is less evidence demonstrating the involvement of the LNC1845 RNA and its interaction with WDR5.

We have added more experimental evidence to strengthen the model especially the interaction of LNC1845 and WDR5. Apart from the RIP-qPCR results of WDR5 demonstrating the enrichment of LNC1845 by WDR5 pulldown (Figure S8D), we performed chromatin isolation by RNA purification (ChIRP) assay using antisense oligos along the entire LNC1845 transcript sequence. ChIRP results confirmed that WDR5 protein were enriched when anti-LNC1845 oligo probes were used to isolate the complex but not the controls without the probes or without overexpression of LNC1845 transcript (Response Figure 2). Taken together, the findings of both approaches support the model that LNC1845 directly interacts with WDR5 to modulate the H3K4me3 modification for LHX8 transcriptional activation. (Related to supplementary figure 8D and 8E.)

Response Figure 2. LNC1845 binding for WDR5 was verified by CHIRP-western blot.

Altogether, this study provides a convincing demonstration of the role of a lncRNA on the regulation of a nearby gene in the context of the germline. However, to have a better understanding of the functionality of lncRNA genes in general, it would be interesting to know whether other pairs of lncRNA-PC genes have been functionally investigated in this context, where no function for the lncRNA gene could be demonstrated. Negative results are highly informative and if so, these could be included in the manuscript.

We appreciate Reviewer #2 suggestion to add other lncRNA-PC gene pairs results. In fact, we have analyzed and presented the results of another 2 pairs in figure 7D. LncRNAs LNC3346 and LNC15266 were also transcriptionally regulated by FOXP3, and they may regulate their neighbor genes TMCO1 and MPP5, as figure 7D showed. Our analysis showed that other lncRNA-PC gene pairs may also have the similar transcriptional regulation as LNC1845-LHX8 during germ cell development.

Author Response

Reviewer #2 (Public Review):

Charme is a long non-coding RNA reported by the authors in their previous studies. Their previous work, mainly using skeletal muscles as a model, showed the functional relevance of Charme, and presented data demonstrating its nuclear role, primarily via modulating the sub-nuclear localization of Matrin 3 (MATR3). Their data from skeletal muscles suggested that loss of the intronic region of Charme affects the local 3D genome organization, affecting MATR3 occupancy and this gene expression. Loss of Charme in vivo leads to cardiac defects. In this manuscript, they characterize the cardiac developmental defects and present molecular data supporting how the loss of Charme affects the cardiac transcriptome repertoire. Specifically, by performing whole transcriptome analysis in E12.5 hearts, they identify gene expression changes affected in developing hearts due to loss of Charme. Based on their previous study in skeletal muscles, they assume that Charme regulates cardiac gene expression primarily via MATR3 also in developing cardiomyocytes. They provide CLIP-seq data for MATR3 (transcriptome-wide foot printing of MATR3) in wild-type E15.5 hearts and connect the binding of MATR3 to gene expression changes observed in Charme knockout hearts. I credit the authors for providing CLIP seq data from in vivo embryonic samples, which is technically demanding.

Major strengths:

Although, as previously indicated by the authors in Charme knockout mice, the major strength is the effect of Charme on cardiac development. While the phenotype might be subtle, the functional data indicate that the role of Charme is essential for cardiac development and function. The combinatorial analysis of MATR3 CLIP-seq and transcriptional changes in the absence of Charme suggests a role of Charme that could be dependent on MATR3.

We thank this reviewer for appreciating our methodological efforts and the importance of the MATR3 CLIP-seq data from in vivo embryonic samples.

Weakness:

(i) Nuclear lncRNAs often affect local gene expression by influencing the local chromatin.

Charme locus is in close proximity to MYBPC2, which is essential for cardiac function, sarcomerogenesis, and sarcomere maintenance. It is important to rule out that the cardiac-specific developmental defects due to Charme loss are not due to (a) the influence of Charme on MYBPC2 or, of that matter, other neighboring genes, (b) local chromatin changes or enhancer-promoter contacts of MYBPC2 and other immediate neighbors (both aspects in the developmental time window when Charme expression is prominent in the heart, ideally from E11 to E15.5)

Although the cis-activity represents a mechanism-of-action for several lncRNAs, our previous work does not reveal this kind of activity for pCharme. To add stronger evidence, we have now analysed the expression of pCharme neighbouring genes in cardiac muscle. Genes were selected by narrowing the analysis not only on the genes in “linear” proximity but also on eventual chromatin contacts, which may underlie possible candidates for in cis regulation. To this purpose, we made use of the analyses that in the meantime were in progress (to answer point iv) on available Hi-C datasets (Rosa- Garrido et al. 2017). Starting from a 1 Mb region around Charme locus, we found that most of the interactions with Charme occur in a region spanning from 240 kb upstream and 115 kb downstream of Charme for a total of 370 Kb (Rev#2_Capture Fig. 1A). This region includes 39 genes, 9 of them expressed in the neonatal heart but none showing significant deregulation (see Table S2). To note, this genomic region also included the MYBPC2 locus, for which we did not find a decreased expression in the heart from our RNA-seq data (Revised Figure 2-figure supplement 1C and Table S2). This trend was confirmed through RT-qPCR analyses of several genes from E15.5 extracts, which revealed no significant difference in their abundance upon Charme ablation (Rev#2_Capture fig. 1B).

Fig. 1. A) Contact map depicting Hi-C data of left ventricular mice heart retrived from GEO accession ID GSM2544836. Data related to 1 Mb region around Charme locus were visualized using Juicebox Web App (https://aidenlab.org/juicebox/). B) RT-qPCR quantification of Charme and its neighbouring genes in CharmeWT vs CharmeKO E15.5.5 hearts. Data were normalized to GAPDH mRNA and represent means ± SEM of WT and KO (n=3) pools. Data information: p < 0.05; p < 0.01, **p < 0.001 unpaired Student’s t test.

For a better understanding, we also checked possible “local” Charme activities in skeletal muscle cells, from previous datasets (Ballarino et al., 2018). We found that in murine C2C12 cells treated with two different gapmers against Charme, three of its neighbouring genes were expressed (Josd2, Emc10 and Pold1), but none showed significant alterations in their expression levels in response to Charme knock-down (Rev#2_Capture Fig. 2).

Taken together, these results would exclude the possibility of Charme in cis activity as responsible for the phenotype.

Fig. 2: Average expression from RNA-seq (FPKM) quantification of Charme neighbouring genes in C2C12 differentiated myotubes treated with Gap-scr vs Gap-Charme. Values for Gap-Charme represent the average values of gene expression after treatment with two different gapmers (GAP-2 and GAP-2/3).

(ii) The authors provide data indicating cardiac developmental defects in Charme knockouts. Detailed developmental phenotyping is missing, which is necessary to pinpoint the exact developmental milestones affected by Charme. This is critical when reporting the cell type/ organ-specific developmental function of a newly identified regulator.

We did our best to answer this concern.

Let us first emphasise that, since their generation, we have never observed any particular tissue alteration, morphological or physiological, when dissecting the CharmeKO animals other than the muscular ones. The high specificity of pCharme expression, as also shown here by ISH (Figure 1C-D, Figure 1-figure supplement 1A-B, Figure 3A), together with the minimal alteration applied to the locus for CRISPR-Cas-mediated KO (PolyA insertion), strongly excludes the presence of an alteration in other tissues and their involvement in the development of the phenotype.

Nevertheless, we now add more developmental details to the cardiac phenotype (see also Essential revision point 2).

1- First of all, gene expression analyses performed at 12.5E, 15.5E, 18.5E and neonatal (PN2) stages allowed us to identify, at the molecular level, the developmental time point when CharmeKO effects on the cardiac muscle can be found. Our new results clearly indicate that the pCharme-mediated regulation of morphogenic and cardiac differentiation genes is detectable from E15.5 fetal stage onward (Rev#2_Capture Fig. 3/Revised Figure 2E). Together with the analysis of pCharme targets and coherently with the altered cardiac maturation and performance, this evidence is also supported by the analysis of the myosins Myh6/Myh7 ratio, which diminution in CharmeKO hearts starts from E15.5 up to 69% of control levels at PN stages (Revised Figure 2F).

2- Hematoxylin-eosin staining of dorso-ventral cryosections from CharmeWT and CharmeKO hearts confirmed the fetal malformation at the E15.5 stage (Revised Figure 2G). Moreover, the hypotrabeculation phenotype of CharmeKO hearts, which was initially examined by immunofluorescence, now finds confirmation by the analysis of key trabecular markers (Irx3 and Sema3a), which expression significantly decreases upon pCharme ablation (Rev#1_Capture Fig. 3B/Revised Figure 2-figure supplement 1G).

3- Finally, the gene expression analysis on Ki-67, Birc5 and Ccna2 (Revised Figure 2-figure supplement 1E) definitively rules out the influence of pCharme ablation on cell-cycle genes and cardiomyocytes proliferation, thus allowing a more careful interpretation of the embryonic phenotype. Note that, coherently with the lncRNA implication at later stages of development, the expression of important cardiac regulators, such as Gata4, Nkx2-5 and Tbx5, is not altered by its ablation at any of the tested time points (Rev#2_Capture Fig.3), while pCharme absence mainly affects genes which are expressed downstream of these factors.

These new results have been included in the revised version of the manuscript and better discussed.

Fig. 3: RT-qPCR quantification Gata4, Nkx2-5 and Tbx5 in CharmeWT and CharmeKO cardiac extract at E12.5, E15.5 and E18.5 days of embryonal development. Data were normalized to GAPDH mRNA and represent means ± SEM of WT and KO (n=3) pools.

(iii) Along the same line, at the molecular level, the authors provide evidence indicating a change in the expression of genes involved in cardiogenesis and cardiac function. Based on changes in mRNA levels of the genes affected due to loss of Charme and based on immunofluorescence analysis of a handful of markers, they propose a role of Charme in cell cycle and maturation. Such claims could be toned down or warrant detailed experimental validation.

See above, response to Reviewer #2 (Public Review) weakness (ii).

(iv) Authors extrapolate the mechanistic finding in skeletal muscle they reported for Charme to the developing heart. While the data support this hypothesis, it falls short in extending the mechanistic understanding of Charme beyond the papers previously published by the authors. CLIP-seq data is a step in the right direction. MATR3 is a relatively abundant RBP, binding transcriptome-wide, mainly in the intronic region, based on currently available CLIP-seq data, as well as shown by the authors' own CLIP seq in cardiomyocytes. It is also shown to regulate pre-mRNA splicing/ alternative splicing along with PTB (PMID: 25599992) and 3D genome organization (PMID: 34716321). In addition, the authors propose a MATR3 depending molecular function for Charme primarily dependent on the intronic region of Charme and due to the binding of MATR3. Answering the following question would enable a better mechanistic understanding of how Charme controls cardiac development.

(i) what are the proximal genomic regions in the 3D space to Charme locus in embryonic cardiomyocytes? Authors can re-analysis published Hi-C data sets from embryonic cardiomyocytes or perform a 4-C experiment using Charme locus for this purpose.

See above, response to Reviewer #2 (Public Review) weakness (i).

(ii) does the loss of Charme affect the splicing landscape of MATR3 bound pre-mRNAs in E12.5 ventricles in general and those arising from the NCTC region specifically?

This is an intriguing issue, as also highlighted by new evidence showing that the reactivation of fetal-specific RNA-binding proteins, including MATR3, in the injured heart drives transcriptome-wide switches through the regulation of early steps of RNA transcription and processing (D'Antonio et al., 2022).

Using the rMATS software on our neonatal RNA-Seq datasets we then investigated the effect of pCharme depletion on splicing, with a focus on NCTC. As shown in the Rev#2_Capture Fig.4A, all classical splicing alterations were investigated, such as exon-skipping, alternative 5’ splice site, alternative 3’ splice site, mutually excluded exons and intron retention. Intriguingly, we did observe a slight alteration in the splicing patterns, in particular considering exon skipping events (62% corresponding to 381 genes). Among them, the majority corresponded to exon exclusion events (237 events = 209 genes) while a smaller fraction to exon inclusion (144 events = 133 genes). Moreover, by intersecting these genes with the MATR3-bound RNAs we found a slightly significant enrichment (p=0,038) for exon inclusion (Rev#2_Capture Fig.4B).

Regarding the NCTC locus, we demonstrate that in hearts pCharme acts through different target genes. Indeed, none of the NCTC-arising transcripts are bound by MATR3 (see Table S4) or substrate for alternative splicing regulation.

While these results are very interesting for deepening the investigation of pCharme/MATR3 interplay, their biological significance needs to be further investigated through one-by-one analysis of specific transcripts. As a prosecution of the project, Nanopore sequencing of these samples on a MinION platform is currently undergoing in the lab to obtain a better characterization of alternative splicing events in response to the lncRNA ablation during development.

Fig. 4: A) Left and middle panel: Pie Chart depicting the proportion of significantly altered (FDR < 0.05) splicing events detected by rMATS comparing neonatal CharmeWT and CharmeKO RNA-seq samples. All classical splicing alterations were investigated, such as exon-skipping, alternative 3’ splice site (A3SS), intron retention, alternative 5’ splice site (A5SS) and mutually excluded exons (MXE). Right panel. Volcano plot depicting significant exon skipping events in CharmeKO (FDR < 0.05, PSI<0 for excluded and included exons, FDR >= 0.05 for invariant exons). X-axis represent exon-inclusion ratio or Percentage Spliced In (PSI) while y-axis represent –log10 of p-value. B) Pie charts representing the fraction of transcripts with at least one significant excluded (left panel), invariant (middle panel) and included (right panel) exons that are bound by MATR3. P-values of MATR3 targets enrichment for each comparison is depicted below. Statistical significance was assessed with Fisher exact test.

(iii) MATR3 binds DNA, as also shown by authors in previous studies. Is the MATR3 genomic binding altered by Charme loss in cardiomyocytes globally, as well as on the loci differentially expressed in Charme knockout heart? Overlapping MATR3 genomic binding changes and transcriptome binding changes to differentially expressed genes in the absence of Charme would better clarify the MATR3-centric mechanisms proposed here. Further connecting that to 3D genome changes due to Charme loss could provide needed clarity to the mechanistic model proposed here.

Previous experience from our (Desideri et al., 2020) and other labs (Zeitz et al 2009 J Cell Biochem), indicate that Chromatin IP is not the most suitable approach for identifying MATR3 specific targets because of the broad distribution of MATR3 over the genome. Given the number of animals that would need to be sacrificed, we moved further to strengthen our MATR3 CLIP evidence by adding the i) CharmeKO MATR3 CLIP-seq control and the ii) combinatorial analysis of MATR3 CLIP-seq with the RNA-seq data.

We have better explained the reasoning within the text, which now reads “The known ability of MATR3 to interact with both DNA and RNA and the high retention of pCharme on the chromatin may predict the presence of chromatin and/or specific transcripts within these MATR3-enriched condensates. In skeletal muscle cells, we have previously observed on a genome-wide scale, a global reduction of MATR3 chromatin binding in the absence of pCharme (Desideri et al., 2020). Nevertheless, the broad distribution of the protein over the genome made the identification of specific targets through MATR3-ChIP challenging.” (lines 274-279).

Indeed, we found that MATR3 binding was significantly decreased on numerous peaks (434/626), while its increase was observed on a smaller fraction of regions (192/626) (Revised Figure 5C). As a control, we performed MATR3 motif enrichment analysis on the differentially bound regions revealing its proximity to the peak summit (+/- 50 nt) (Revised Figure 5-figure supplement 1D) close to the strongest enrichment of MATR3, further confirming a direct and highly specific binding of the protein to these sites. To better characterise the relationship between MATR3 and pCharme, we then intersected the newly identified regions with the MATR3-bound transcripts whose expression was altered by Charme depletion. While gain peaks were equally distributed across DEGs, loss peaks were significantly enriched in a subset of pCharme down-regulated DEGs (Revised Figure 5D), suggesting a crosstalk between the lncRNA and the protein in regulating the expression of this specific group of genes. Interestingly, these RNAs mainly distribute across the same GO categories as pCharme downregulated DEGs and include genes, such as Cacna1c, Notch3, Myo18B and Rbm20 involved in embryo development and validated as pCharme/Matr3 targets in primary cardiac cells (Revised Figure 5D, lower panel and 5E)

Author Response

Reviewer 2 (Public Review):

1) The authors developed a novel C.elegans model for studying extracellular amyloid beta aggregation and is therefore likely to be taken up broadly by the field. However, the new model should be fully characterized. Throughout the manuscript, the only method to detect amyloid deposition was the GFP fluorescence intensity and morphology, while direct characterization of amyloid aggregates is lacking.

We thank the reviewer for the feedback and the foresight that this model might be taken up by the field. To strengthen our model, as the reviewer had suggested, we confirmed that the GFP fluorescence is indeed amyloid aggregations. Please, see point 3 above and the new Supporting Figure 1.1.

2) A targeted RNA interference (RNAi) screen was used to identify the key regulators of Aβ aggregation and clearance, which is one of the strengths of the study. There should be evidence that RNAi works to knockdown the specific genes. Similarly, there should be evidence indicating that ADM-2 is indeed expressed in the overexpression experiments.

We aimed to verify our main hits (cri-2 and adm-2) with a mutation in these genes, as RNAi can have off-target effects. The adm-2(ok3178) allele is a 989 bp deletion leading to a splice/acceptor change leading to a probably truncated and out-of-frame protein.

Author response image 1.

The cri-2(gk314) allele is a 1213 bp deletion covering the whole cri-2 locus, suggesting to be a null allele.

Author response image 2.

For the overexpression, there is no ADM-2 antibody available. We tried to generate an ADM-2 antibody, unfortunately unsuccessfully. Thus, we can only, based on the induction and higher red fluorescence of ADM-2::mScarlet (Supporting Figure 6.1.) infer the ADM-2 overexpression.

3) It remains unknown whether ADM-2 directly degrades Aβ or facilitates the clearance of Aβ by remoulding the ECM. The effect of ADM-2 on ECM remodeing should be examined.

We addressed this in point 1 above and also in our discussion section.

Author Response

Reviewer #2 (Public Review):

The time-dependency of the model simulations was not analyzed, and the nature of the observed biphasic time-dependent APAP response remains elusive. It would be interesting to see how the model can explain the time course of the APAP stimulation experiment.

The alternative model at its current state can only describe steady state conditions. However, we understand that the reviewer is interested in the dynamic behavior of the model. However, our approach provides a proof of principle that the alternative model can phenomenologically explain the changes of YAP localization as a response to APAP treatment. The question of how to model Hippo pathway in a time-dependent manner as a response to APAP treatment is very challenging and would require further investigations and, most notably, further development of the PDE simulation algorithms and the SME software. Hence, a technical update of the software algorithms would be required, which cannot be in the scope of this manuscript.

Nevertheless, we decided to share our first and preliminary analyses on dynamic processes caused by APAP with the reviewer. For this, we simulated the steady state model in an arbitrary manner, where APAP initiates (early time-point) and slows down (late time-points) YAP phosphorylation in the nucleus (see Figure below).

The simulated alternative model shows that increased YAP phosphorylation about 50% leads to the cytoplasmic localization of YAP (Rebuttal Figure R5A/B). However, this shuttling is not detectable in our protein fractionation and live-cell imaging experiments (see also Rebuttal Figure R7C/D). At late time points, decreasing YAP phosphorylation (about 60%) led to a clear nuclear enrichment and dephosphorylation of YAP was observed in our experiments. Thus, our mathematical model nicely describes cellular events of Hippo pathway dynamics observed at later stages after APAP treatment (nuclear enrichment). However, early events cannot be completely explained (suggested nuclear YAP exclusion is not detectable).

We suggest two explanations for this observation. First, other molecular mechanisms (not yet identified and therefore not part of the model topology) oppose the exclusion YAP enrichment that is expected at early time points. Second, detection methods used in this study (Western Blotting and life cell imaging) cannot capture minimal changes and cellular heterogeneity in the chosen experimental setup. We clarify this aspect/limitation of our study in the discussion chapter of the manuscript. Page 12, lines 436-440

Time-dependency of YAP (orange) localization based on the simulated APAP treatment. (A): Simulated control (ctrl) and APAP treatment for 2 and 48h. The treatment was simulated by changing the phosphorylation coefficient of YAP in the nucleus. (B): Simulated pYAP/YAP ratio during control and APAP treatment for 2 and 48 hours at the steady state of the model. (C): Simulated NCR of the total YAP during control and APAP treatment for 2 and 48 hours at the steady state.

Author Response

Reviewer #1 (Public Review):

Because of the importance of brain and cognitive traits in human evolution, brain morphology and neural phenotypes have been the subject of considerable attention. However, work on the molecular basis of brain evolution has tended to focus on only a handful of species (i.e., human, chimp, rhesus macaque, mouse), whereas work that adopts a phylogenetic comparative approach (e.g., to identify the ecological correlates of brain evolution) has not been concerned with molecular mechanism. In this study, Kliesmete, Wange, and colleagues attempt to bridge this gap by studying protein and cis-regulatory element evolution for the gene TRNP1, across up to 45 mammals. They provide evidence that TRNP1 protein evolution rates and its ability to drive neural stem cell proliferation are correlated with brain size and/or cortical folding in mammals, and that activity of one TRNP1 cis-regulatory element may also predict cortical folding.

There is a lot to like about this manuscript. Its broad evolutionary scope represents an important advance over the narrower comparisons that dominate the literature on the genetics of primate brain evolution. The integration of molecular evolution with experimental tests for function is also a strength. For example, showing that TRNP1 from five different mammals drives differences in neural stem cell proliferation, which in turn correlate with brain size and cortical folding, is a very nice result. At the same time, the paper is a good reminder of the difficulty of conclusively linking macroevolutionary patterns of trait evolution to molecular function. While TRNP1 is a moderate outlier in the correlation between rate of protein evolution and brain morphology compared to 125 other genes, this result is likely sensitive to how the comparison set is chosen; additionally, it's not clear that a correlation with evolutionary rate is what should be expected. Further, while the authors show that changes in TRNP1 sequence have functional consequences, they cannot show that these changes are directly responsible for size or folding differences, or that positive selection on TRNP1 is because of selection on brain morphology (high bars to clear). Nevertheless, their findings contribute strong evidence that TRNP1 is an interesting candidate gene for studying brain evolution. They also provide a model for how functional follow-up can enrich sequence-based comparative analysis.

We thank the reviewer for the positive assessment. With respect to our set of control genes and the interpretation of the correlation between the evolution of the TRNP1 protein sequence and the evolution of brain size and gyrification, we would like to mention the following: we do think that the set is small, but we took all similarly sized genes with one coding exon that we could find in all 30 species. Furthermore, the control genes are well comparable to TRNP1 with respect to alignment quality and average omega (Figure 1-figure supplement 3). Hence, we think that the selection procedure and the actual omega distribution make them a valid, unbiased set to which TRNP1’s co-evolution with brain phenotypes can be compared to. Moreover, we want to point out that by using Coevol, we correlate evolutionary rates, that is the rate of protein evolution of TRNP1 as measured with omega and the rate of brain size evolution that is modeled in Coevol as a Brownian motion process. We think that this was unclear in the previous version of our manuscript, and appreciate that the reviewer saw some merit in our analyses in spite of it.

Finding conclusive evidence to link molecular evolution to concrete phenotypes is indeed difficult and necessarily inferential. This said, we still believe that correlating rates of evolution of phenotype and sequence across a phylogeny is one of the most convincing pieces of evidence available.

Reviewer #2 (Public Review):

In this paper, Kliesmete et al. analyze the protein and regulatory evolution of TRNP1, linking it to the evolution of brain size in mammals. We feel that this is very interesting and the conclusions are generally supported, with one concern.

The comparison of dN/dS (omega) values to 125 control proteins is helpful, but an important factor was not controlled. The fraction of a protein in an intrinsically disordered region (IDR) is potentially even more important in affecting dN/dS than the protein length or number of exons. We suggest comparing dN/dS of TRNP1 to another control set, preferably at least ~500 proteins, which have similar % IDR.

Thank you for this interesting suggestion. As mentioned in the public response to Reviewer #1, we are sorry that we did not explain the rationale of the approach very well in the previous version of the manuscript. As also argued above, we think that our control proteins are an unbiased set as they have a comparable alignment quality and an average omega (dN/dS) similar to TRNP1 (Figure 1-figure supplement 3). While IDR domains tend to have a higher omega than their respective non-IDR counterparts, we do not think that the IDR content should be more relevant than omega itself as we do not interpret this estimate on its own, but its covariance with the rate of phenotypic change. Indeed, the proteins of our control set that have a higher IDR content (D2P2, Oates et al. 2013) do not show stronger evidence to be coevolving with the brain phenotypes (IDR content vs. absolute brain size-omega partial correlation: Kendall's tau = 0.048, p-value = 0.45; IDR content vs. absolute GI-omega partial correlation: Kendall’s tau = -0.025, p-value = 0.68; 88 proteins (71%) contain >0% IDRs; 8 proteins contain >62% (TRNP1 content) IDRs.

Reviewer #3 (Public Review):

In this work, Z. Kliesmete, L. Wange and colleagues investigate TRNP1 as a gene of potential interest for the evolution of the mammalian cortex. Previous evidence suggests that TRNP1 is involved in self-renewal, proliferation and expansion in cortical cells in mouse and ferret, making this gene a good candidate for evolutionary investigation. The authors designed an experimental scheme to test two non-exclusive hypotheses: first, that evolution of the TRNP1 protein is involved in the apparition of larger and more convoluted brains; and second, that regulation of the TRNP1 gene also plays a role in this process alongside protein evolution.

The authors report that the rate of TRNP1 protein evolution is strongly correlated to brain size and gyrification, with species with larger and more convoluted brains having more divergent sequences at this gene locus. The correlation with body mass was not as strong, suggesting a functional link between TRNP1 and brain evolution. The authors directly tested the effects of sequence changes by transfecting the TRNP1 sequences from 5 different species in mouse neural stem cells and quantifying cell proliferation. They show that both human and dolphin sequences induce higher proliferation, consistent with larger brain sizes and gyrifications in these two species. Then, the authors identified six potential cis-regulatory elements around the TRNP1 gene that are active in human fetal brain, and that may be involved in its regulation. To investigate whether sequence evolution at these sites results in changes in TRNP1 expression, the authors performed a massively parallel reporter assay using sequences from 75 mammals at these six loci. The authors report that one of the cis-regulatory elements drives reporter expression levels that are somewhat correlated to gyrification in catarrhine monkeys. Consistent with the activity of this cis-regulatory sequence in the fetal brain, the authors report that this element contains binding sites for TFs active in brain development, and contains stronger binding sites for CTCF in catarrhine monkeys than in other species. However, the specificity or functional relevance of this signal is unclear.

Altogether, this is an interesting study that combines evolutionary analysis and molecular validation in cell cultures using a variety of well-designed assays. The main conclusions - that TRNP1 is likely involved in brain evolution in mammals - are mostly well supported, although the involvement of gene regulation in this process remains inconclusive.

Strengths:

• The authors have done a good deal of resequencing and data polishing to ensure that they obtained high-quality sequences for the TRNP1 gene in each species, which enabled a higher confidence investigation of this locus.

• The statistical design is generally well done and appears robust.

• The combination of evolutionary analysis and in vivo validation in neural precursor cells is interesting and powerful, and goes beyond the majority of studies in the field. I also appreciated that the authors investigated both protein and regulatory evolution at this locus in significant detail, including performing a MPRA assay across species, which is an interesting strategy in this context.

Weaknesses:

• The authors report that TRNP1 evolves under positive selection, however this seems to be the case for many of the control proteins as well, which suggests that the signal is non-specific and possibly due to misspecifications in the model.

• The evidence for a higher regulatory activity of the intronic cis-regulatory element highlighted by the authors is fairly weak: correlation across species is only 0.07, consistent with the rapid evolution of enhancers in mammals, and the correlation in catarrhine monkeys is seems driven by a couple of outlier datapoints across the 10 species. It is unclear whether false discovery rates were controlled for in this analysis.

• The analysis of the regulatory content in this putative enhancer provides some tangential evidence but no reliable conclusions regarding the involvement of regulatory changes at this locus in brain evolution.

We thank the reviewer for the detailed comments. Indeed, TRNP1 overall has a rather average omega value across the tree and hence also the proportion of sites under selection is not hugely increased compared to the control proteins. This is good because we want to have comparable power to detect a correlation between the rate of protein evolution (omega) and the rate of brain size or GI evolution for TRNP1 and the control proteins. Indeed, what makes TRNP1 special is the rather strong correlation between the rate of brain size change and omega, which was only stronger in 4% of our control proteins. Hence, we do not agree with the weakness of model misspecification for TRNP1 protein evolution.

We agree that the correlation of the activity induced by the intronic cis regulatory element (CRE) with gyrification is weak, but we dispute that the correlation is due to outliers (see residual plot below) or violations of model assumptions (see new permutation analysis in the Results section). There are many reasons why we would expect such a correlation not to be weak, including that a MPRA takes the CRE out of its natural genomic context. Our conclusions do not solely rest on those statistics, but also on independent corroborating evidence: Reilly et al (2015) found a difference in the activity of the TRNP1 intron between human and macaque samples during brain development. Furthermore, we used their and other public data to show that the intron CRE is indeed active in humans and bound by CTCF (new Figure 4 - figure supplement 2).

We believe that the combined evidence suggests a likely role for the intron CRE for the co-evolution of TRNP1 with gyrification.

Author Response

Reviewer #1 (Public Review):

Trudel and colleagues aimed to uncover the neural mechanisms of estimating the reliability of the information from social agents and non-social objects. By combining functional MRI with a behavioural experiment and computational modelling, they demonstrated that learning from social sources is more accurate and robust compared with that from non-social sources. Furthermore, dmPFC and pTPJ were found to track the estimated reliability of the social agents (as opposed to the non-social objects). The strength of this study is to devise a task consisting of the two experimental conditions that were matched in their statistical properties and only differed in their framing (social vs. non-social). The novel experimental task allows researchers to directly compare the learning from social and non-social sources, which is a prominent contribution of the present study to social decision neuroscience.

Thank you so much for your positive feedback about our work. We are delighted that you found that our manuscript provided a prominent contribution to social decision neuroscience. We really appreciate your time to review our work and your valuable comments that have significantly helped us to improve our manuscript further.

One of the major weaknesses is the lack of a clear description about the conceptual novelty. Learning about the reliability/expertise of social and non-social agents has been of considerable concern in social neuroscience (e.g., Boorman et al., Neuron 2013; and Wittmann et al., Neuron 2016). The authors could do a better job in clarifying the novelty of the study beyond the previous literature.

We understand the reviewer’s comment and have made changes to the manuscript that, first, highlight more strongly the novelty of the current study. Crucially, second, we have also supplemented the data analyses with a new model-based analysis of the differences in behaviour in the social and non-social conditions which we hope makes clearer, at a theoretical level, why participants behave differently in the two conditions.

There has long been interest in investigating whether ‘social’ cognitive processes are special or unique compared to ‘non-social’ cognitive processes and, if they are, what makes them so. Differences between conditions could arise during the input stage (e.g. the type of visual input that is processed by social and non-social system), at the algorithm stage (e.g. the type of computational principles that underpin social versus non-social processes) or, even if identical algorithms are used, social and non-social processes might depend on distinct anatomical brain areas or neurons within brain areas. Here, we conducted multiple analyses (in figures 2, 3, and 4 in the revised manuscript and in Figure 2 – figure supplement 1, Figure 3 – figure supplement 1, Figure 4 – figure supplement 3, Figure 4 – figure supplement 4) that not only demonstrated basic similarities in mechanism generalised across social and non-social contexts, but also demonstrated important quantitative differences that were linked to activity in specific brain regions associated with the social condition. The additional analyses (Figure 4 – figure supplement 3, Figure 4 – figure supplement 4) show that differences are not simply a consequence of differences in the visual stimuli that are inputs to the two systems1, nor does the type of algorithm differ between conditions. Instead, our results suggest that the precise manner in which an algorithm is implemented differs when learning about social or non-social information and that this is linked to differences in neuroanatomical substrates.

The previous studies mentioned by the reviewer are, indeed, relevant ones and were, of course, part of the inspiration for the current study. However, there are crucial differences between them and the current study. In the case of the previous studies by Wittmann, the aim was a very different one: to understand how one’s own beliefs, for example about one’s performance, and beliefs about others, for example about their performance levels, are combined. Here, however, instead we were interested in the similarities and differences between social and non-social learning. It is true that the question resembles the one addressed by Boorman and colleagues in 2013 who looked at how people learned about the advice offered by people or computer algorithms but the difference in the framing of that study perhaps contributed to authors’ finding of little difference in learning. By contrast, in the present study we found evidence that people were predisposed to perceive stability in social performance and to be uncertain about non-social performance. By accumulating evidence across multiple analyses, we show that there are quantitative differences in how we learn about social versus non-social information, and that these differences can be linked to the way in which learning algorithms are implemented neurally. We therefore contend that our findings extend our previous understanding of how, in relation to other learning processes, ‘social’ learning has both shared and special features.

We would like to emphasize the way in which we have extended several of the analyses throughout the revision. The theoretical Bayesian framework has made it possible to simulate key differences in behaviour between the social and non-social conditions. We explain in our point-by-point reply below how we have integrated a substantial number of new analyses. We have also more carefully related our findings to previous studies in the Introduction and Discussion.

Introduction, page 4:

[...] Therefore, by comparing information sampling from social versus non-social sources, we address a long-standing question in cognitive neuroscience, the degree to which any neural process is specialized for, or particularly linked to, social as opposed to non-social cognition 2–9. Given their similarities, it is expected that both types of learning will depend on common neural mechanisms. However, given the importance and ubiquity of social learning, it may also be that the neural mechanisms that support learning from social advice are at least partially specialized and distinct from those concerned with learning that is guided by nonsocial sources. However, it is less clear on which level information is processed differently when it has a social or non-social origin. It has recently been argued that differences between social and non-social learning can be investigated on different levels of Marr’s information processing theory: differences could emerge at an input level (in terms of the stimuli that might drive social and non-social learning), at an algorithmic level or at a neural implementation level 7. It might be that, at the algorithmic level, associative learning mechanisms are similar across social and non-social learning 1. Other theories have argued that differences might emerge because goal-directed actions are attributed to social agents which allows for very different inferences to be made about hidden traits or beliefs 10. Such inferences might fundamentally alter learning about social agents compared to non-social cues.

Discussion, page 15:

[…] One potential explanation for the assumption of stable performance for social but not non-social predictors might be that participants attribute intentions and motivations to social agents. Even if the social and non-social evidence are the same, the belief that a social actor might have a goal may affect the inferences made from the same piece of information 10. Social advisors first learnt about the target’s distribution and accordingly gave advice on where to find the target. If the social agents are credited with goal-directed behaviour then it might be assumed that the goals remain relatively constant; this might lead participants to assume stability in the performances of social advisors. However, such goal-directed intentions might not be attributed to non-social cues, thereby making judgments inherently more uncertain and changeable across time. Such an account, focussing on differences in attribution in social settings aligns with a recent suggestion that any attempt to identify similarities or differences between social and non-social processes can occur at any one of a number of the levels in Marr’s information theory 7. Here we found that the same algorithm was able to explain social and non-social learning (a qualitatively similar computational model could explain both). However, the extent to which the algorithm was recruited when learning about social compared to non-social information differed. We observed a greater impact of uncertainty on judgments about social compared to non-social information. We have shown evidence for a degree of specialization when assessing social advisors as opposed to non-social cues. At the neural level we focused on two brain areas, dmPFC and pTPJ, that have not only been shown to carry signals associated with belief inferences about others but, in addition, recent combined fMRI-TMS studies have demonstrated the causal importance of these activity patterns for the inference process […]

Another weakness is the lack of justifications of the behavioural data analyses. It is difficult for me to understand why 'performance matching' is suitable for an index of learning accuracy. I understand the optimal participant would adjust the interval size with respect to the estimated reliability of the advisor (i.e., angular error); however, I am wondering if the optimal strategy for participants is to exactly match the interval size with the angular error. Furthermore, the definitions of 'confidence adjustment across trials' and 'learning index' look arbitrary.

First, having read the reviewer’s comments, we realise that our choice of the term ‘performance matching’ may not have been ideal as it indeed might not be the case that the participant intended to directly match their interval sizes with their estimates of advisor/predictor error. Like the reviewer, our assumption is simply that the interval sizes should change as the estimated reliability of the advisor changes and, therefore, that the intervals that the participants set should provide information about the estimates that they hold and the manner in which they evolve. On re-reading the manuscript we realised that we had not used the term ‘performance matching’ consistently or in many places in the manuscript. In the revised manuscript we have simply removed it altogether and referred to the participants’ ‘interval setting’.

Most of the initial analyses in Figure 2a-c aim to better understand the raw behaviour before applying any computational model to the data. We were interested in how participants make confidence judgments (decision-making per se), but also how they adapt their decisions with additional information (changes or learning in decision making). In the revised manuscript we have made clear that these are used as simple behavioural measures and that they will be complemented later by more analyses derived from more formal computational models.

In what we now refer to as the ‘interval setting’ analysis (Figure 2a), we tested whether participants select their interval settings differently in the social compared to non-social condition. We observe that participants set their intervals closer to the true angular error of the advisor/predictor in the social compared to the non-social condition. This observation could arise in two ways. First, it could be due to quantitative differences in learning despite general, qualitative similarity: mechanisms are similar but participants differ quantitatively in the way that they learn about non-social information and social information. Second, it could, however, reflect fundamentally different strategies. We tested basic performance differences by comparing the mean reward between conditions. There was no difference in reward between conditions (mean reward: paired t-test social vs. non-social, t(23)= 0.8, p=0.4, 95% CI= [-0.007 0.016]), suggesting that interval setting differences might not simply reflect better or worse performance in social or non-social contexts but instead might reflect quantitative differences in the processes guiding interval setting in the two cases.

In the next set of analyses, in which we compared raw data, applied a computational model, and provided a theoretical account for the differences between conditions, we suggest that there are simple quantitative differences in how information is processed in social and nonsocial conditions but that these have the important impact of making long-term representations – representations built up over a longer series of trials – more important in the social condition. This, in turn, has implications for the neural activity patterns associated with social and non-social learning. We, therefore, agree with the reviewer, that one manner of interval setting is indeed not more optimal than another. However, the differences that do exist in behaviour are important because they reveal something about the social and non-social learning and its neural substrates. We have adjusted the wording and interpretation in the revised manuscript.

Next, we analysed interval setting with two additional, related analyses: interval setting adjustment across trials and derivation of a learning index. We tested the degree to which participants adjusted their interval setting across trials and according to the prediction error (learning index, Figure f); the latter analysis is very similar to a trial-wise learning rate calculated in previous studies11. In contrast to many other studies, the intervals set by participants provide information about the estimates that they hold in a simple and direct way and enable calculation of a trial-wise learning index; therefore, we decided to call it ‘learning index’ instead of ‘learning rate’ as it is not estimated via a model applied to the data, but instead directly calculated from the data. Arguably the directness of the approach, and its lack of dependence on a specific computational model, is a strength of the analysis.

Subsequently in the manuscript, a new analysis (illustrated in new Figure 3) employs Bayesian models that can simulate the differences in the social and non-social conditions and demonstrate that a number of behavioural observations can arise simply as a result of differences in noise in each trial-wise Bayesian update (Figure 3 and specifically 3d; Figure 3 – figure supplement 1b-c). In summary, the descriptive analyses in Figure 2a-c aid an intuitive understanding of the differences in behaviour in the social and non-social conditions. We have then repeated these analyses with Bayesian models incorporating different noise levels and showed that in such a way, the differences in behaviour between social and non-social conditions can be mimicked (please see next section and manuscript for details).

We adjusted the wording in a number of sections in the revised manuscript such as in the legend of Figure 2 (figures and legend), Figure 4 (figures and legend).

Main text, page 5:

The confidence interval could be changed continuously to make it wider or narrower, by pressing buttons repeatedly (one button press resulted in a change of one step in the confidence interval). In this way participants provided what we refer to as an ’interval setting’.

We also adjusted the following section in Main text, page 6:

Confidence in the performance of social and non-social advisors

We compared trial-by-trial interval setting in relation to the social and non-social advisors/predictors. When setting the interval, the participant’s aim was to minimize it while ensuring it still encompassed the final target position; points were won when it encompassed the target position but were greater when it was narrower. A given participant’s interval setting should, therefore, change in proportion to the participant’s expectations about the predictor’s angular error and their uncertainty about those expectations. Even though, on average, social and non-social sources did not differ in the precision with which they predicted the target (Figure 2 – figure supplement 1), participants gave interval settings that differed in their relationships to the true performances of the social advisors compared to the non-social predictors. The interval setting was closer to the angular error in the social compared to the non-social sessions (Figure 2a, paired t-test: social vs. non-social, t(23)= -2.57, p= 0.017, 95% confidence interval (CI)= [-0.36 -0.4]). Differences in interval setting might be due to generally lower performance in the nonsocial compared to social condition, or potentially due to fundamentally different learning processes utilised in either condition. We compared the mean reward amounts obtained by participants in the social and non-social conditions to determine whether there were overall performance differences. There was, however, no difference in the reward received by participants in the two conditions (mean reward: paired t-test social vs. non-social, t(23)= 0.8, p=0.4, 95% CI= [-0.007 0.016]), suggesting that interval setting differences might not simply reflect better or worse performance

Discussion, page 14:

Here, participants did not match their confidence to the likely accuracy of their own performance, but instead to the performance of another social or non-social advisor. Participants used different strategies when setting intervals to express their confidence in the performances of social advisors as opposed to non-social advisors. A possible explanation might be that participants have a better insight into the abilities of social cues – typically other agents – than non-social cues – typically inanimate objects.

As the authors assumed simple Bayesian learning for the estimation of reliability in this study, the degree/speed of the learning should be examined with reference to the distance between the posterior and prior belief in the optimal Bayesian inference.

We thank the reviewer for this suggestion. We agree with the reviewer that further analyses that aim to disentangle the underlying mechanisms that might differ between both social and non-social conditions might provide additional theoretical contributions. We show additional model simulations and analyses that aim to disentangle the differences in more detail. These new results allowed clearer interpretations to be made.

In the current study, we showed that judgments made about non-social predictors were changed more strongly as a function of the subjective uncertainty: participants set a larger interval, indicating lower confidence, when they were more uncertain about the non-social cue’s accuracy to predict the target. In response to the reviewer’s comments, the new analyses were aimed at understanding under which conditions such a negative uncertainty effect might emerge.

Prior expectations of performance First, we compared whether participants had different prior expectations in the social condition compared to the non-social condition. One way to compare prior expectations is by comparing the first interval set for each advisor/predictor. This is a direct readout of the initial prior expectation with which participants approach our two conditions. In such a way, we test whether the prior beliefs before observing any social or non-social information differ between conditions. Even though this does not test the impact of prior expectations on subsequent belief updates, it does test whether participants have generally different expectations about the performance of social advisors or non-social predictors. There was no difference in this measure between social or non-social cues (Figure below; paired t-test social vs. non-social, t(23)= 0.01, p=0.98, 95% CI= [-0.067 0.68]).

Figure. Confidence interval for the first encounter of each predictor in social and non-social conditions. There was no initial bias in predicting the performance of social or non-social predictors.

Learning across time We have now seen that participants do not have an initial bias when predicting performances in social or non-social conditions. This suggests that differences between conditions might emerge across time when encountering predictors multiple times. We tested whether inherent differences in how beliefs are updated according to new observations might result in different impacts of uncertainty on interval setting between social and non-social conditions. More specifically, we tested whether the integration of new evidence differed between social and non-social conditions; for example, recent observations might be weighted more strongly for non-social cues while past observations might be weighted more strongly for social cues. This approach was inspired by the reviewer’s comments about potential differences in the speed of learning as well as the reduction of uncertainty with increasing predictor encounters. Similar ideas were tested in previous studies, when comparing the learning rate (i.e. the speed of learning) in environments of different volatilities 12,13. In these studies, a smaller learning rate was prevalent in stable environments during which reward rates change slower over time, while higher learning rates often reflect learning in volatile environments so that recent observations have a stronger impact on behaviour. Even though most studies derived these learning rates with reinforcement learning models, similar ideas can be translated into a Bayesian model. For example, an established way of changing the speed of learning in a Bayesian model is to introduce noise during the update process14. This noise is equivalent to adding in some of the initial prior distribution and this will make the Bayesian updates more flexible to adapt to changing environments. It will widen the belief distribution and thereby make it more uncertain. Recent information has more weight on the belief update within a Bayesian model when beliefs are uncertain. This increases the speed of learning. In other words, a wide distribution (after adding noise) allows for quick integration of new information. On the contrary, a narrow distribution does not integrate new observations as strongly and instead relies more heavily on previous information; this corresponds to a small learning rate. So, we would expect a steep decline of uncertainty to be related to a smaller learning index while a slower decline of uncertainty is related to a larger learning index. We hypothesized that participants reduce their uncertainty quicker when observing social information, thereby anchoring more strongly on previous beliefs instead of integrating new observations flexibly. Vice versa, we hypothesized a less steep decline of uncertainty when observing non-social information, indicating that new information can be flexibly integrated during the belief update (new Figure 3a).

We modified the original Bayesian model (Figure 2d, Figure 2 – figure supplement 2) by adding a uniform distribution (equivalent to our prior distribution) to each belief update – we refer to this as noise addition to the Bayesian model14,21 . We varied the amount of noise between δ = [0,1], while δ= 0 equals the original Bayesian model and δ= 1 represents a very noisy Bayesian model. The uniform distribution was selected to match the first prior belief before any observation was made (equation 2). This δ range resulted in a continuous increase of subjective uncertainty around the belief about the angular error (Figure 3b-c). The modified posterior distribution denoted as 𝑝′(σ x) was derived at each trial as follows:

We applied each noisy Bayesian model to participants’ choices within the social and nonsocial condition.

The addition of a uniform distribution changed two key features of the belief distribution: first, the width of the distribution remains larger with additional observations, thereby making it possible to integrate new observations more flexibly. To show this more clearly, we extracted the model-derived uncertainty estimate across multiple encounters of the same predictor for the original model and the fully noisy Bayesian model (Figure 3 – figure supplement 1). The model-derived ‘uncertainty estimate’ of a noisy Bayesian model decays more slowly compared to the ‘uncertainty estimate’ of the original Bayesian model (upper panel). Second, the model-derived ‘accuracy estimate’ reflects more recent observations in a noisy Bayesian model compared to the ‘accuracy estimate’ derived from the original Bayesian model, which integrates past observations more strongly (lower panel). Hence, as mentioned beforehand, a rapid decay of uncertainty implies a small learning index; or in other words, stronger integration of past compared to recent observations.

In the following analyses, we tested whether an increasingly noisy Bayesian model mimics behaviour that is observed in the non-social compared to social condition. For example, we tested whether an increasingly noisy Bayesian model also exhibits a strongly negative ‘predictor uncertainty’ effect on interval setting (Figure 2e). In such a way, we can test whether differences in noise in the updating process of a Bayesian model might reproduce important qualitative differences in learning-related behaviour seen in the social and nonsocial conditions.

We used these modified Bayesian models to simulate trial-wise interval setting for each participant according to the observations they made when selecting a particular advisor or non-social cue. We simulated interval setting at each trial and examined whether an increase in noise produced model behaviours that resembled participant behaviour patterns observed in the non-social condition as opposed to social condition. At each trial, we used the accuracy estimate (Methods, equation 6) – which represents a subjective belief about a single angular error -- to derive an interval setting for the selected predictor. To do so, we first derived the point-estimate of the belief distribution at each trial (Methods, equation 6) and multiplied it with the size of one interval step on the circle. The step size was derived by dividing the circle size by the maximum number of possible steps. Here is an example of transforming an accuracy estimate into an interval: let’s assume the belief about the angular error at the current trial is 50 (Methods, equation 6). Now, we are trying to transform this number into an interval for the current predictor on a given trial. To obtain the size of one interval step, the circle size (360 degrees) is divided by the maximum number of interval steps (40 steps; note, 20 steps on each side), which results in nine degrees that represents the size of one interval step. Next, the accuracy estimate in radians (0,87) is multiplied by the step size in radians (0,1571) resulting in an interval of 0,137 radians or 7,85 degrees. The final interval size would be 7,85.

Simulating Bayesian choices in that way, we repeated the behavioural analyses (Figure 2b,e,f) to test whether intervals derived from more noisy Bayesian models mimic intervals set by participants in the non-social condition: greater changes in interval setting across trials (Figure 3 – figure supplement 1b), a negative ‘predictor uncertainty' effect on interval setting (Figure 3 – figure supplement 1c), and a higher learning index (Figure 3d).

First, we repeated the most crucial analysis -- the linear regression analysis (Figure 2e) and hypothesized that intervals that were simulated from noisy Bayesian models would also show a greater negative ‘predictor uncertainty’ effect on interval setting. This was indeed the case: irrespective of social or non-social conditions, the addition of noise (increased weighting of the uniform distribution in each belief update) led to an increasingly negative ‘predictor uncertainty’ effect on confidence judgment (new Figure 3d). In Figure 3d, we show the regression weights (y-axis) for the ‘predictor uncertainty’ on confidence judgment with increasing noise (x-axis). This result is highly consistent with the idea that that in the non-social condition the manner in which task estimates are updated is more uncertain and more noisy. By contrast, social estimates appear relatively more stable, also according to this new Bayesian simulation analysis.

This new finding extends the results and suggests a formal computational account of the behavioural differences between social and non-social conditions. Increasing the noise of the belief update mimics behaviour that is observed in the non-social condition: an increasingly negative effect of ‘predictor uncertainty’ on confidence judgment. Noteworthily, there was no difference in the impact that the noise had in the social and non-social conditions. This was expected because the Bayesian simulations are blind to the framing of the conditions. However, it means that the observed effects do not depend on the precise sequence of choices that participants made in these conditions. It therefore suggests that an increase in the Bayesian noise leads to an increasingly negative impact of ‘predictor uncertainty’ on confidence judgments irrespective of the condition. Hence, we can conclude that different degrees of uncertainty within the belief update is a reasonable explanation that can underlie the differences observed between social and non-social conditions.

Next, we used these simulated confidence intervals and repeated the descriptive behavioural analyses to test whether interval settings that were derived from more noisy Bayesian models mimic behavioural patterns observed in non-social compared to social conditions. For example, more noise in the belief update should lead to more flexible integration of new information and hence should potentially lead to a greater change of confidence judgments across predictor encounters (Figure 2b). Further, a greater reliance on recent information should lead to prediction errors more strongly in the next confidence judgment; hence, it should result in a higher learning index in the non-social condition that we hypothesize to be perceived as more uncertain (Figure 2f). We used the simulated confidence interval from Bayesian models on a continuum of noise integration (i.e. different weighting of the uniform distribution into the belief update) and derived again both absolute confidence change and learning indices (Figure 3 – figure supplement 1b-c).

‘Absolute confidence change’ and ‘learning index’ increase with increasing noise weight, thereby mimicking the difference between social and non-social conditions. Further, these analyses demonstrate the tight relationship between descriptive analyses and model-based analyses. They show that a noise in the Bayesian updating process is a conceptual explanation that can account for both the differences in learning and the difference in uncertainty processing that exist between social and non-social conditions. The key insight conveyed by the Bayesian simulations is that a wider, more uncertain belief distribution changes more quickly. Correspondingly, in the non-social condition, participants express more uncertainty in their confidence estimate when they set the interval, and they also change their beliefs more quickly as expressed in a higher learning index. Therefore, noisy Bayesian updating can account for key differences between social and non-social condition.

We thank the reviewer for making this point, as we believe that these additional analyses allow theoretical inferences to be made in a more direct manner; we think that it has significantly contributed towards a deeper understanding of the mechanisms involved in the social and non-social conditions. Further, it provides a novel account of how we make judgments when being presented with social and non-social information.

We made substantial changes to the main text, figures and supplementary material to include these changes:

Main text, page 10-11 new section:

The impact of noise in belief updating in social and non-social conditions

So far, we have shown that, in comparison to non-social predictors, participants changed their interval settings about social advisors less drastically across time, relied on observations made further in the past, and were less impacted by their subjective uncertainty when they did so (Figure 2). Using Bayesian simulation analyses, we investigated whether a common mechanism might underlie these behavioural differences. We tested whether the integration of new evidence differed between social and non-social conditions; for example, recent observations might be weighted more strongly for non-social cues while past observations might be weighted more strongly for social cues. Similar ideas were tested in previous studies, when comparing the learning rate (i.e. the speed of learning) in environments of different volatilities12,13. We tested these ideas using established ways of changing the speed of learning during Bayesian updates14,21. We hypothesized that participants reduce their uncertainty quicker when observing social information. Vice versa, we hypothesized a less steep decline of uncertainty when observing non-social information, indicating that new information can be flexibly integrated during the belief update (Figure 5a).

We manipulated the amount of uncertainty in the Bayesian model by adding a uniform distribution to each belief update (Figure 3b-c) (equation 10,11). Consequently, the distribution’s width increases and is more strongly impacted by recent observations (see example in Figure 3 – figure supplement 1). We used these modified Bayesian models to simulate trial-wise interval setting for each participant according to the observations they made by selecting a particular advisor in the social condition or other predictor in the nonsocial condition. We simulated confidence intervals at each trial. We then used these to examine whether an increase in noise led to simulation behaviour that resembled behavioural patterns observed in non-social conditions that were different to behavioural patterns observed in the social condition.

First, we repeated the linear regression analysis and hypothesized that interval settings that were simulated from noisy Bayesian models would also show a greater negative ‘predictor uncertainty’ effect on interval setting resembling the effect we had observed in the nonsocial condition (Figure 2e). This was indeed the case when using the noisy Bayesian model: irrespective of social or non-social condition, the addition of noise (increasing weight of the uniform distribution to each belief update) led to an increasingly negative ‘predictor uncertainty’ effect on confidence judgment (new Figure 3d). The absence of difference between the social and non-social conditions in the simulations, suggests that an increase in the Bayesian noise is sufficient to induce a negative impact of ‘predictor uncertainty’ on interval setting. Hence, we can conclude that different degrees of noise in the updating process are sufficient to cause differences observed between social and non-social conditions. Next, we used these simulated interval settings and repeated the descriptive behavioural analyses (Figure 2b,f). An increase in noise led to greater changes of confidence across time and a higher learning index (Figure 3 – figure supplement 1b-c). In summary, the Bayesian simulations offer a conceptual explanation that can account for both the differences in learning and the difference in uncertainty processing that exist between social and non-social conditions. The key insight conveyed by the Bayesian simulations is that a wider, more uncertain belief distribution changes more quickly. Correspondingly, in the non-social condition, participants express more uncertainty in their confidence estimate when they set the interval, and they also change their beliefs more quickly. Therefore, noisy Bayesian updating can account for key differences between social and non-social condition.

Methods, page 23 new section:

Extension of Bayesian model with varying amounts of noise

We modified the original Bayesian model (Figure 2d, Figure 2 – figure supplement 2) to test whether the integration of new evidence differed between social and non-social conditions; for example, recent observations might be weighted more strongly for non-social cues while past observations might be weighted more strongly for social cues. [...] To obtain the size of one interval step, the circle size (360 degrees) is divided by the maximum number of interval steps (40 steps; note, 20 steps on each side), which results in nine degrees that represents the size of one interval step. Next, the accuracy estimate in radians (0,87) is multiplied by the step size in radians (0,1571) resulting in an interval of 0,137 radians or 7,85 degrees. The final interval size would be 7,85.

We repeated behavioural analyses (Figure 2b,e,f) to test whether confidence intervals derived from more noisy Bayesian models mimic behavioural patterns observed in the nonsocial condition: greater changes of confidence across trials (Figure 3 – figure supplement 1b), a greater negative ‘predictor uncertainty' on confidence judgment (Figure 3 – figure supplement 1c) and a greater learning index (Figure 3d).

Discussion, page 14: […] It may be because we make just such assumptions that past observations are used to predict performance levels that people are likely to exhibit next 15,16. An alternative explanation might be that participants experience a steeper decline of subjective uncertainty in their beliefs about the accuracy of social advice, resulting in a narrower prior distribution, during the next encounter with the same advisor. We used a series of simulations to investigate how uncertainty about beliefs changed from trial to trial and showed that belief updates about non-social cues were consistent with a noisier update process that diminished the impact of experiences over the longer term. From a Bayesian perspective, greater certainty about the value of advice means that contradictory evidence will need to be stronger to alter one’s beliefs. In the absence of such evidence, a Bayesian agent is more likely to repeat previous judgments. Just as in a confirmation bias 17, such a perspective suggests that once we are more certain about others’ features, for example, their character traits, we are less likely to change our opinions about them.

Reviewer #2 (Public Review):

Humans learn about the world both directly, by interacting with it, and indirectly, by gathering information from others. There has been a longstanding debate about the extent to which social learning relies on specialized mechanisms that are distinct from those that support learning through direct interaction with the environment. In this work, the authors approach this question using an elegant within-subjects design that enables direct comparisons between how participants use information from social and non-social sources. Although the information presented in both conditions had the same underlying structure, participants tracked the performance of the social cue more accurately and changed their estimates less as a function of prediction error. Further, univariate activity in two regions-dmPFC and pTPJ-tracked participants' confidence judgments more closely in the social than in the non-social condition, and multivariate patterns of activation in these regions contained information about the identity of the social cues.

Overall, the experimental approach and model used in this paper are very promising. However, after reading the paper, I found myself wanting additional insight into what these condition differences mean, and how to place this work in the context of prior literature on this debate. In addition, some additional analyses would be useful to support the key claims of the paper.

We thank the reviewer for their very supportive comments. We have addressed their points below and have highlighted changes in our manuscript that we made in response to the reviewer’s comments.

(1) The framing should be reworked to place this work in the context of prior computational work on social learning. Some potentially relevant examples:

• Shafto, Goodman & Frank (2012) provide a computational account of the domainspecific inductive biases that support social learning. In brief, what makes social learning special is that we have an intuitive theory of how other people's unobservable mental states lead to their observable actions, and we use this intuitive theory to actively interpret social information. (There is also a wealth of behavioral evidence in children to support this account; for a review, see Gweon, 2021).

• Heyes (2012) provides a leaner account, arguing that social and non-social learning are supported by a common associative learning mechanism, and what distinguishes social from non-social learning is the input mechanism. Social learning becomes distinctively "social" to the extent that organisms are biased or attuned to social information.

I highlight these papers because they go a step beyond asking whether there is any difference between mechanisms that support social and nonsocial learning-they also provide concrete proposals about what that difference might be, and what might be shared. I would like to see this work move in a similar direction.

References<br /> (In the interest of transparency: I am not an author on these papers.)

Gweon, H. (2021). Inferential social learning: how humans learn from others and help others learn. PsyArXiv. https://doi.org/10.31234/osf.io/8n34t

Heyes, C. (2012). What's social about social learning?. Journal of Comparative Psychology, 126(2), 193.

Shafto, P., Goodman, N. D., & Frank, M. C. (2012). Learning from others: The consequences of psychological reasoning for human learning. Perspectives on Psychological Science, 7(4), 341-351.

Thank you for this suggestion to expand our framing. We have now made substantial changes to the Discussion and Introduction to include additional background literature, the relevant references suggested by the reviewer, addressing the differences between social and non-social learning. We further related our findings to other discussions in the literature that argue that differences between social and non-social learning might occur at the level of algorithms (the computations involved in social and non-social learning) and/or implementation (the neural mechanisms). Here, we describe behaviour with the same algorithm (Bayesian model), but the weighing of uncertainty on decision-making differs between social and non-social contexts. This might be explained by similar ideas put forward by Shafto and colleagues (2012), who suggest that differences between social and non-social learning might be due to the attribution of goal-directed intention to social agents, but not non-social cues. Such an attribution might lead participants to assume that advisor performances will be relatively stable under the assumption that they should have relatively stable goal-directed intentions. We also show differences at the implementational level in social and non-social learning in TPJ and dmPFC.

Below we list the changes we have made to the Introduction and Discussion. Further, we would also like to emphasize the substantial extension of the Bayesian modelling which we think clarifies the theoretical framework used to explain the mechanisms involved in social and non-social learning (see our answer to the next comments below).

Introduction, page 4:

[...]<br /> Therefore, by comparing information sampling from social versus non-social sources, we address a long-standing question in cognitive neuroscience, the degree to which any neural process is specialized for, or particularly linked to, social as opposed to non-social cognition 2–9. Given their similarities, it is expected that both types of learning will depend on common neural mechanisms. However, given the importance and ubiquity of social learning, it may also be that the neural mechanisms that support learning from social advice are at least partially specialized and distinct from those concerned with learning that is guided by nonsocial sources.

However, it is less clear on which level information is processed differently when it has a social or non-social origin. It has recently been argued that differences between social and non-social learning can be investigated on different levels of Marr’s information processing theory: differences could emerge at an input level (in terms of the stimuli that might drive social and non-social learning), at an algorithmic level or at a neural implementation level 7. It might be that, at the algorithmic level, associative learning mechanisms are similar across social and non-social learning 1. Other theories have argued that differences might emerge because goal-directed actions are attributed to social agents which allows for very different inferences to be made about hidden traits or beliefs 10. Such inferences might fundamentally alter learning about social agents compared to non-social cues.

Discussion, page 15:

[…] One potential explanation for the assumption of stable performance for social but not non-social predictors might be that participants attribute intentions and motivations to social agents. Even if the social and non-social evidence are the same, the belief that a social actor might have a goal may affect the inferences made from the same piece of information 10. Social advisors first learnt about the target’s distribution and accordingly gave advice on where to find the target. If the social agents are credited with goal-directed behaviour then it might be assumed that the goals remain relatively constant; this might lead participants to assume stability in the performances of social advisors. However, such goal-directed intentions might not be attributed to non-social cues, thereby making judgments inherently more uncertain and changeable across time. Such an account, focussing on differences in attribution in social settings aligns with a recent suggestion that any attempt to identify similarities or differences between social and non-social processes can occur at any one of a number of the levels in Marr’s information theory 7. Here we found that the same algorithm was able to explain social and non-social learning (a qualitatively similar computational model could explain both). However, the extent to which the algorithm was recruited when learning about social compared to non-social information differed. We observed a greater impact of uncertainty on judgments about social compared to non-social information. We have shown evidence for a degree of specialization when assessing social advisors as opposed to non-social cues. At the neural level we focused on two brain areas, dmPFC and pTPJ, that have not only been shown to carry signals associated with belief inferences about others but, in addition, recent combined fMRI-TMS studies have demonstrated the causal importance of these activity patterns for the inference process […]

(2) The results imply that dmPFC and pTPJ differentiate between learning from social and non-social sources. However, more work needs to be done to rule out simpler, deflationary accounts. In particular, the condition differences observed in dmPFC and pTPJ might reflect low-level differences between the two conditions. For example, the social task could simply have been more engaging to participants, or the social predictors may have been more visually distinct from one another than the fruits.

We understand the reviewer’s concern regarding low-level distinctions between the social and non-social condition that could confound for the differences in neural activation that are observed between conditions in areas pTPJ and dmPFC. From the reviewer’s comments, we understand that there might be two potential confounders: first, low-level differences such that stimuli within one condition might be more distinct to each other compared to the relative distinctiveness between stimuli within the other condition. Therefore, simply the greater visual distinctiveness of stimuli in one condition than another might lead to learning differences between conditions. Second, stimuli in one condition might be more engaging and potentially lead to attentional differences between conditions. We used a combination of univariate analyses and multivariate analyses to address both concerns.

Analysis 1: Univariate analysis to inspect potential unaccounted variance between social and non-social condition

First, we used the existing univariate analysis (exploratory MRI whole-brain analysis, see Methods) to test for neural activation that covaried with attentional differences – or any other unaccounted neural difference -- between conditions. If there were neural differences between conditions that we are currently not accounting for with the parametric regressors that are included in the fMRI-GLM, then these differences should be captured in the constant of the GLM model. For example, if there are attentional differences between conditions, then we could expect to see neural differences between conditions in areas such as inferior parietal lobe (or other related areas that are commonly engaged during attentional processes).

Importantly, inspection of the constant of the GLM model should capture any unaccounted differences, whether they are due to attention or alternative processes that might differ between conditions. When inspecting cluster-corrected differences in the constant of the fMRI-GLM model during the setting of the confidence judgment, there were no clustersignificant activation that was different between social and non-social conditions (Figure 4 – figure supplement 4a; results were familywise-error cluster-corrected at p<0.05 using a cluster-defining threshold of z>2.3). For transparency, we show the sub-threshold activation map across the whole brain (z > 2) for the ‘constant’ contrasted between social and nonsocial condition (i.e. constant, contrast: social – non-social).

For transparency we additionally used an ROI-approach to test differences in activation patterns that correlated with the constant during the confidence phase – this means, we used the same ROI-approach as we did in the paper to avoid any biased test selection. We compared activation patterns between social and non-social conditions in the same ROI as used before; dmPFC (MNI-coordinate [x/y/z: 2,44,36] 16), bilateral pTPJ (70% probability anatomical mask; for reference see manuscript, page 23) and additionally compared activation patterns between conditions in bilateral IPLD (50% probability anatomical mask, 20). We did not find significantly different activation patterns between social and non-social conditions in any of these areas: dmPFC (confidence constant; paired t-test social vs nonsocial: t(23) = 0.06, p=0.96, [-36.7, 38.75]), bilateral TPJ (confidence constant; paired t-test social vs non-social: t(23) = -0.06, p=0.95, [-31, 29]), bilateral IPLD (confidence constant; paired t-test social vs non-social: t(23) = -0.58, p=0.57, [-30.3 17.1]).

There were no meaningful activation patterns that differed between conditions in either areas commonly linked to attention (eg IPL) or in brain areas that were the focus of the study (dmPFC and pTPJ). Activation in dmPFC and pTPJ covaried with parametric effects such as the confidence that was set at the current and previous trial, and did not correlate with low-level differences such as attention. Hence, these results suggest that activation between conditions was captured better by parametric regressors such as the trial-wise interval setting, i.e. confidence, and are unlikely to be confounded by low-level processes that can be captured with univariate neural analyses.

Analysis 2: RSA to test visual distinctiveness between social and non-social conditions

We addressed the reviewer’s other comment further directly by testing whether potential differences between conditions might arise due to a varying degree of visual distinctiveness in one stimulus set compared to the other stimulus set. We used RSA analysis to inspect potential differences in early visual processes that should be impacted by greater stimulus similarity within one condition. In other words, we tested whether the visual distinctiveness of one stimuli set was different to the visual distinctiveness of the other stimuli set. We used RSA analysis to compare the Exemplar Discriminability Index (EDI) between conditions in early visual areas. We compared the dissimilarity of neural activation related to the presentation of an identical stimulus across trials (diagonal in RSA matrix) with the dissimilarity in neural activation between different stimuli across trials (off-diagonal in RSA matrix). If stimuli within one stimulus set are very similar, then the difference between the diagonal and off-diagonal should be very small and less likely to be significant (i.e. similar diagonal and off-diagonal values). In contrast, if stimuli within one set are very distinct from each other, then the difference between the diagonal and off-diagonal should be large and likely to result in a significant EDI (i.e. different diagonal and off-diagonal values) (see Figure 4g for schematic illustration). Hence, if there is a difference in the visual distinctiveness between social and non-social conditions, then this difference should result in different EDI values for both conditions – hence, visual distinctiveness between the stimuli set can be tested by comparing the EDI values between conditions within the early visual processing. We used a Harvard-cortical ROI mask based on bilateral V1. Negative EDI values indicate that the same exemplars are represented more similarly in the neural V1 pattern than different exemplars. This analysis showed that there was no significant difference in EDI between conditions (Figure 4 – figure supplement 4b; EDI paired sample t-test: t(23) = -0.16, p=0.87, 95% CI [-6.7 5.7]).

We have further replicated results in V1 with a whole-brain searchlight analysis, averaging across both social and non-social conditions.

In summary, by using a combination of univariate and multivariate analyses, we could test whether neural activation might be different when participants were presented with a facial or fruit stimuli and whether these differences might confound observed learning differences between conditions. We did not find meaningful neural differences that were not accounted for with the regressors included in the GLM. Further, we did not find differences in the visual distinctiveness between the stimuli sets. Hence, these control analyses suggest that differences between social and non-social conditions might not arise because of differences in low-level processes but are instead more likely to develop when learning about social or non-social information.

Moreover, we also examined behaviourally whether participants differed in the way they approached social and non-social condition. We tested whether there were initial biases prior to learning, i.e. before actually receiving information from either social or non-social information sources. Therefore, we tested whether participants have different prior expecations about the performance of social compared to non-social predictors. We compared the confidence judgments at the first trial of each predictor. We found that participants set confidence intervals very similarly in social and non-social conditions (Figure below). Hence, it did not seem to be the case that differences between conditions arose due to low level differences in stimulus sets or prior differences in expectations about performances of social compared to non-social predictors. However, we can show that differences between conditions are apparent when updating one’s belief about social advisors or non-social cues and as a consequence, in the way that confidence judgments are set across time.

Figure. Confidence interval for the first encounter of each predictor in social and non-social conditions. There was no initial bias in predicting the performance of social or non-social predictors.

Main text page 13:

[… ]<br /> Additional control analyses show that neural differences between social and non-social conditions were not due to the visually different set of stimuli used in the experiment but instead represent fundamental differences in processing social compared to non-social information (Figure 4 – figure supplement 4). These results are shown in ROI-based RSA analysis and in whole-brain searchlight analysis. In summary, in conjunction, the univariate and multivariate analyses demonstrate that dmPFC and pTPJ represent beliefs about social advisors that develop over a longer timescale and encode the identities of the social advisors.

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Author Response

Reviewer #2 (Public Review):

1) Although the images and videos were of great quality, the results derived from them provided little new knowledge and few conceptual insights into male reproductive tract biology and basically confirmed what has been published using traditional methods. For example, the high intensity of the vascular network in the initial segment was previously reported by Abe in 1984 and Suzuki in 1982; the pattern of the major lymphatic vessel and drainage was beautifully depicted by Perez-Clavier, 1982.

We thank the reviewer for his/her appreciative comments regarding the quality of the images/videos we provide in this study. We do not fully agree with his/her assessment of the lack of novelty. Our work confirms earlier reports that are now dated (1980s), which in itself is worth mentioning for the interested community, especially when the confirmation uses the most advanced technologies available today. We have never said that nothing was done in the past, and we have acknowledged all past contributors (including those mentioned by the reviewer) by pointing out the limitations of the technical tools that were available at the time. In addition, our current work provides a more comprehensive and global view by extending our approach to the entire mouse epididymis, whereas previous work was much more limited.

2) The authors were very cautious when interpreting the results of marker immunostaining however these markers were not specific for a definite cell type. For example, as the authors stated, VEGFR3 marks both lymphatic vessels and fenestrated blood vessels. how could the authors claim the VEGFR3+ network was lymphatic? The authors claimed that they used three markers for the lymphatic vessel. But staining results of the networks were very different. How could the author make conclusions about the network of lymphatic vessels in the epididymis?

We broadly agree with the reviewer and have made it clear that one cannot be 100% sure that all the VEGFR3+ structures we present are lymphatic. However, in total, we used 4 documented lymphatic markers (not 3 as mentioned by the reviewer) which are (VEGFR3, LYVE1, PROX1 and PDPN). Three of them give very similar profiles, while only PDPN shows some differences. We are currently studying in more detail the expression of PDPN in the mouse epididymis because we speculate that this marker may target a population of pluripotent cells in this tissue. Therefore, with the 3 similar profiles and with the subtraction of PVLAP+ structures, we are pretty confident that what we show corresponds to the different lymphatic structures.

3) To understand the vascular network development in the epididymis, would the authors please look at the fetal stage when the vascular network is established in the first place? Wolffian duct tissues are much smaller and thinner and would be amenable for 3D imaging probably even without clearing.

We generally agree with the reviewer that this could be an interesting addition. However, it represents a significant amount of additional work. Organ clearing will certainly be required because it is unlikely that Wolffian duct will be sufficiently transparent to allow lightsheet microscopy. In the literature, the study of Wolffian duct relies primarily on whole mounts, inclusions, and cryosections. Besides the fact that this represents a lot of extra work, we are not totally convinced that this would be of much use. A key reason is that the epididymis is an organ that differentiates completely after birth (Robaire and Hinton, 2015). It is reported that differentiation of mouse caput segment 1 occurs around 19DPN (Xu et al., 2016) and is intimately related to the development of the vasculature (Lebarr et al., 1986). Regarding the lymphatic network, Swingen et al, (2012) reports that lymphangiogenesis in the mouse testis and epididymis is initiated late in gestation after 15DPC. Videos showing the external lymphatic vessels of the testis and epididymis at 17.5DPC can be seen at https://doi.org/10.1371/journal.pone.0052620.s002. The authors indicate that lymphangiogenesis occurs via sprouting from the adjacent mesonephros. We hypothesize that the more internal lymphatics evolve between birth and 10DPN, which corresponds to the time when we observed LEPC Lyve1pos cells.

4) Immunofluorescence staining of VEGF factors was not convincing. As a secreted factor, VEGF will be secreted out of the cells, would it be detected more in the interstitium? I am always skeptical about the results of immunostaining secreted growth factors. Would it be possible to perform in situ or RNAscope to confirm the spatial expression pattern of VEGFs?

Well, active VEGF factors result from alternative mRNA splicing events and posttranslational proteolytic cleavage. Therefore, in our opinion, the study of VEGF mRNA by in situ hybridization or RNAscope analysis will not be very informative about the actual presence of active forms of VEGF in the epididymis. If necessary, we can provide as supplementary material immunohistochemistry data showing the presence of VEFG-A in the epididymal principal cells. Our major objective with these data was to show that VEGF factors and their respective receptors were present in the epididymis. Nevertheless, in an attempt to convince the reviewer, we provide as accompanying data to this rebuttal letter new sets of figures (Figures VEGF-A-response editor & VEGFC /VEGF-D-response editor) that we believe can improve the perception of our data. If the editorial office feels it is necessary, these figures could be added to the supplementary figure set (as Figure 6figure supplement 1 and Figure 6-figure supplement 2). For VEGF-A the data exists already in the literature as we have indicated (Korpelainen, 1998). In fine, our goal was not to show which cell types of the epididymis epithelium produce VEGFs but rather than VEGF factors and their receptors where there in order to support angiogenesis or lymphangiogenic activity in the tissue. In addition, we hypothesize that because septa have been reported to constitute barriers between segments restricting passive diffusion of molecules (Turner et al., 2003; Stammler et al., 2015), the VEGF factors are expected to be produced locally.

Figure VEGF-A - response editor : Immunofluorescence of the angiogenic ligand VEGF-A in the epididymis. Figure 6 shows that this ligand is mainly found in the caput and more precisely in S1.It is very strongly expressed in the peritubular microvascularization of the SI which expresses the VEGFR3:YFP transgene whereas it is less expressed by intertubular blood vessels (asterisk). This seems to indicate that it is the peritubular vessels that are in the majority responsible for the angiogenic activity measured in our study. Furthermore, it is expressed by the epithelium as secretory vesicles (IS, and S3 and enlargement) which is in agreement with in situ hybridization work performed by Korpelainene E.I et al J.Cell.biol 1998). The enlargement shown in S3_Z shows the sagital plane of the tubule where one can distinguish VEGFR:YFP positive cells that strongly express are also VEGF-A positive indicating that the same cells of the epithelium express both the receptor and the ligand. Here the transgene is detected directly without the use of an anti-GFP which allows to enhance the signal.

Figure VEGF-C / VEGF-D - response editor : Immunofluorescence of VEGF-C and VEGF-D lymphangiogenic ligands in the epididymis. This figure shows that these ligands are mainly found in the interstitial tissue throughout the organ with a higher proportion in the caudal part. This expression may be largely driven by fibroblasts, which are widely represented in the interstitium, or by endothelial cells, since these two ligands are expressed by these cell types. However, as shown in the figures and in the enlargement of panel A, VEGF-C is also produced by epithelial cells within what may appear as secretory vesicles. In contrast, for VEGF-D, we observe only few weakly positive epithelial cells (panel B). These ligands are also detected in the lumen of epididymal tubules (visible for VEGF-C Panel A S2). This presence may be explained by lumicrine transfer from the testis, in addition to secretion from epithelial cells. Here the transgene is detected directly without the use of an anti-GFP which allows to enhance the signal.

5) The study is descriptive and does not provide functional and mechanistic insights. Maybe, the combination of 3D imaging with lineage tracing of endothelium cells or ligation study (removal/ligation of the certain vessel) would help better understand how the vascular network is established and their functional significance.

The technical approaches suggested by the reviewer could certainly improve our understanding of the rather complex epididymal vascular network. Taken together, they represent the body of a comprehensive follow-up study that is worth undertaking.

6) Immune response is among many physiological processes in which vascular networks play significant roles. Discussion would be needed in other physiological processes, such as tissue metabolism and stem/progenitor cell niche microenvironment.

We agree with the reviewer that the mammalian vasculature is involved in other physiological processes beyond immune/inflammatory responses. We have deliberately chosen to focus our discussion on the inflammatory and immune context of the epididymis, as we believe this is the most relevant aspect. It is also in full agreement with the research that our team has been conducting for 15 years to try to understand the complex orchestration of tolerance versus immune surveillance in this territory. This is a finely tuned process that, if properly understood, can help to understand and appropriately treat clinical situations of infertility and/or urological problems. As our discussion section is already quite long, we feel that it was not justified to extend it further on other aspects. However, in response to the reviewer's suggestion, we now mention at the end of the first paragraph of the discussion that the epididymal vascular network is likely to serve different processes in this tissue (page 9, lines 299 to 303).

7) How could the author determine the Cd-A labeled vessel in Fig 1 was an artery, not a vein? This leads to another critical question. Would it be possible to stain with artery and vein markers to help illustrate the blood flow directions of the vessel?

The reviewer is right on the fact that we arbitrarily called the Cd-A vessel in Figure 1 an artery. Cd-A is not an acronym we use anymore. What we have done is to use the acronym SEA (superior epididymal artery) to indicate what we firmly believe to be an artery, as also suggested by previous literature (e.g., Suzuki, 1982; Abe et al, 1982) in which this same structure has been consistently referred to as an artery. For other blood vessels, we now have used the acronym "Cd-BV" because we do not know whether we are dealing with a vein or an artery as rightfully pointed out by the reviewer. This is clearly stated in the legend of Figure 1.

Author Response

Reviewer #1 (Public Review):

The authors ask an interesting question as to whether working memory contains more than one conjunctive representation of multiple task features required for a future response with one of these representations being more likely to become relevant at the time of the response. With RSA the authors use a multivariate approach that seems to become the standard in modern EEG research.

We appreciate the reviewer’s helpful comments on the manuscript and their encouraging comments regarding its potential impact.

I have three major concerns that are currently limiting the meaningfulness of the manuscript: For one, the paradigm uses stimuli with properties that could potentially influence involuntary attention and interfere in a Stroop-like manner with the required responses (i.e., 2 out of 3 cues involve the terms "horizontal" or "vertical" while the stimuli contain horizontal and vertical bars). It is not clear to me whether these potential interactions might bring about what is identified as conjunctive representations or whether they cause these representations to be quite weak.

We agree it is important to rule out any effects of involuntary attention that might have been elicited by our stimulus choices. To address the Reviewer’s concern, we conducted control analyses to test if there was any influence of Stroop-like interference on our measures of behavior or the conjunctive representation. To summarize these analyses (detailed in our responses below and in the supplemental materials), we found no evidence of the effect of compatibility on behavior or on the decoding of conjunctions during either the maintenance or test periods. Furthermore, we found that the decoding of the bar orientation was at chance level during the interval when we observe evidence of the conjunctive representations. Thus, we conclude that the compatibility of the stimuli and the rule did not contribute to the decoding of conjunctive representations or to behavior.

Second, the relatively weak conjunctive representations are making it difficult to interpret null effects such as the absence of certain correlations.

The reviewer is correct that we cannot draw strong conclusions from null findings. We have revised the main text accordingly. In certain cases, we have also included additional analyses. These revisions are described in detail in response the reviewer’s comments below.

Third, if the conjunctive representations truly are reflections of working memory activity, then it would help to include a control condition where memory load is reduced so as to demonstrate that representational strength varies as a function of load. Depending on whether these concerns or some of them can be addressed or ruled out this manuscript has the potential of becoming influential in the field.

This is a clever suggestion for further experimentation. We agree that observing the adverse effect of memory load is one of the robust ways to assess the contributions of working memory system for future studies. However, given that decoding is noisy during the maintenance period (particularly for the low-priority conjunctive representation) even with a relatively low set-size, we expect that in order to further manipulate load, we would need to alter the research design substantially. Thus, as the main goal of the current study is to study prioritization and post-encoding selection of action-related information, we focused on the minimum set-size required for this question (i.e., load 2). However, we now note this load manipulation as a direction for future research in the discussion (pg. 18).

Reviewer #2 (Public Review):

Kikumoto and colleagues investigate the way visual-motor representations are stored in working memory and selected for action based on a retro-cue. They make use of a combination of decoding and RSA to assess at which stages of processing sensory, motor, and conjunctive information (consisting of sensory and motor representations linked via an S- R mapping) are represented in working memory and how these mental representations are related to behavioral performance.

Strengths

This is an elaborate and carefully designed experiment. The authors are able to shed further light on the type of mental representations in working memory that serve as the basis for the selection of relevant information in support of goal- directed actions. This is highly relevant for a better understanding of the role of selective attention and prospective motor representations in working memory. The methods used could provide a good basis for further research in this regard.

We appreciate these helpful comments and the Reviewer’s positive comments on the impact of the work.

Weaknesses

There are important points requiring further clarification, especially regarding the statistical approach and interpretation of results.

• Why is there a conjunction RSA model vector (b4) required, when all information for a response can be achieved by combining the individual stimulus, response, and rule vectors? In Figure 3 it becomes obvious that the conjunction RSA scores do not simply reflect the overlap of the other three vectors. I think it would help the interpretation of results to clearly state why this is not the case.

Thank you for the suggestion, we’ve now added the theoretical background that motivates us to include the RSA model of conjunctive representation (pg. 4 and 5). In particular, several theories of cognitive control have proposed that over the course of action planning, the system assembles an event (task) file which binds all task features at all levels – including the rule (i.e., context), stimulus, and response – into an integrated, conjunctive representation that is essential for an action to be executed (Hommel 2019; Frings et al. 2020). Similarly, neural evidence of non-human primates suggests that cognitive tasks that require context-dependency (e.g., flexible remapping of inputs to different outputs based on the context) recruit nonlinear conjunctive representations (Rigotti et al. 2013; Parthasarathy et al. 2019; Bernardi et al. 2020; Panichello and Buschman, 2021). Supporting these views, we previously observed that conjunctive representations emerge in the human brain during action selection, which uniquely explained behavior such as the costs in transition of actions (Kikumoto & Mayr, 2020; see also Rangel & Hazeltine & Wessel, 2022) or the successful cancelation of actions (Kikumoto & Mayr, 2022). In the current study, by using the same set of RSA models, we attempted to extend the role of conjunctive representations for planning and prioritization of future actions. As in the previous studies (and as noted by the reviewer), the conjunction model makes a unique prediction of the similarity (or dissimilarity) pattern of the decoder outputs: a specific instance of action that is distinct from others actions. This contrasts to other RSA models of low-level features that predict similar patterns of activities for instances that share the same feature (e.g., S-R mappings 1 to 4 share the diagonal rule context). Here, we generally replicate the previous studies showing the unique trajectories of conjunctive representations (Figure 3) and their unique contribution on behavior (Figure 5).

• One of the key findings of this study is the reliable representation of the conjunction information during the preparation phase while there is no comparable effect evident for response representations. This might suggest that two potentially independent conjunctive representations can be activated in working memory and thereby function as the basis for later response selection during the test phase. However, the assumption of the independence of the high and low priority conjunction representations relies only on the observation that there was no statistically reliable correlation between the high and low priority conjunctions in the preparation and test phases. This assumption is not valid because non-significant correlations do not allow any conclusion about the independence of the two processes. A comparable problem appeared regarding the non-significant difference between high and low-priority representations. These results show that it was not possible to prove a difference between these representations prior to the test phase based on the current approach, but they do not unequivocally "suggest that neither action plan was selectively prioritized".

We appreciate this important point. We have taken care in the revision to state that we find evidence of an interference effect for the high-priority action and do not find evidence for such an effect from the low-priority action. Thus, we do not intend to conclude that no such effect could exist. Further, although it is not our intention to draw a strong conclusion from the null effect (i.e., no correlations), we performed an exploratory analysis where we tested the correlation in trials where we observed strong evidence of both conjunctions. Specifically, we binned trials into half within each time point and individual subject and performed the multi-level model analysis using trials where both high and low priority conjunctions were above their medians. Thus, we selected trials in such a way that they are independent of the effect we are testing. The figure below shows the coefficient of associated with low-priority conjunction predicting high-priority conjunction (uncorrected). Even when we focus on trials where both conjunctions are detected (i.e., a high signal-to-noise ratio), we observed no tradeoff. Again, we cannot draw strong conclusions based on the null result of this exploratory analysis. Yet, we can rule out some causes of no correlation between high and low priority conjunctions such as the poor signal-to-noise ratio of the low priority conjunctions. We have further clarified this point in the result (pg. 14).

Fig. 1. Trial-to-trial variability between high and low priority conjunctions, using above median trials. The coefficients of the multilevel regression model predicting the variability in trial-to-trial highpriority conjunction by low-priority conjunction.

• The experimental design used does not allow for a clear statement about whether pure motor representations in working memory only emerge with the definition of the response to be executed (test phase). It is not evident from Figure 3 that the increase in the RSA scores strictly follows the onset of the Go stimulus. It is also conceivable that the emergence of a pure motor representation requires a longer processing time. This could only be investigated through temporally varying preparation phases.

We agree with the reviewer. Although we detected no evidence of response representations of both high and low priority action plans during the preparation phase, t(1,23) = -.514, beta = .002, 95% CI [-.010 .006] for high priority; t(1,23) = -1.57, beta = -.008, 95% CI [-.017 .002] for low priority, this may be limited by the relatively short duration of the delay period (750 ms) in this study. However, in our previous studies using a similar paradigm without a delay period (Kikumoto & Mayr, 2020; Kikumoto & Mayr, 2022), response representations were detected less than 300ms after the response was specified, which corresponds to the onset of delay period in this study. Further, participants in the current study were encouraged to prepare responses as early as possible, using adaptive response deadlines and performance-based incentives. Thus, we know of no reason why responses would take longer to prepare in the present study. But we agree that we can’t rule this out. We have added the caveat noted above, as well as this additional context in the discussion (pg. 16-17).

• Inconsistency of statistical approaches: In the methods section, the authors state that they used a cluster-forming threshold and a cluster-significance threshold of p < 0.05. In the results section (Figure 4) a cluster p-value of 0.01 is introduced. Although this concerns different analyses, varying threshold values appear as if they were chosen in favor of significant results. The authors should either proceed consistently here or give very good reasons for varying thresholds.

We thank the reviewer for noting this oversight. All reported significant clusters with cluster P-value were identified using a cluster-forming threshold, p < .05. We fixed the description accordingly.

• Interpretation of results: The significant time window for the high vs. low priority by test-type interaction appeared quite late for the conjunction representation. First, it does not seem reasonable that such an effect appears in a time window overlapping with the motor responses. But more importantly, why should it appear after the respective interaction for the response representation? When keeping in mind that these results are based on a combination of time-frequency analysis, decoding, and RSA (quite many processing steps), I find it hard to really see a consistent pattern in these results that allows for a conclusion about how higher-level conjunctive and motor representations are selected in working memory.

Thank you for raising this important point. First, we fixed reported methodological inconsistencies such as the cluster P-value and cluster-forming threshold). Further, we fully agree that the difference in the time course for the response and conjunctive representations in the low priority, tested condition is unexpected and would complicate the perspective that the conjunctive representation contributes to efficient response selection. However, additional analysis indicates that this apparent pattern in the stimulus locked result is misleading and there is a more parsimonious explanation. First, we wish to caution that the data are relatively noisy and likely are influenced by different frequency bands for different features. Thus, fine-grained temporal differences should be interpreted with caution in the absence of positive statistical evidence of an interaction over time. Indeed, though Figure 4 in the original submission shows a quantitative difference in timing of the interaction effect (priority by test type) across conjunctive representation and response representation, the direct test of this four way interaction [priority x test type x representation type (conjunction vs. response), x time interval (1500 ms to 1850 ms vs. 1850 to 2100 ms)] is not significant, t(1,23) = 1.65, beta = .058, 95% CI [-.012 .015]). The same analysis using response-aligned data is also not significant, t(1,23) = -1.24, beta = -.046, 95% CI [-.128 .028]). These observations were not dependent on the choice of time interval, as other time intervals were also not significant. Therefore, we do not have strong evidence that this is a true timing difference between these conditions and believe this is likely driven by noise.

Further, we believe the apparent late emergence of difference in two conjunctions when the low priority action is tested is more likely due to a slow decline in the strength of the untested high priority conjunction rather than a late emergence of the low priority conjunction. This pattern is clearer when the traces are aligned to the response. The tested low priority conjunction emerges early and is sustained when it is the tested action and declines when it is untested (-226 ms to 86 ms relative to the response onset, cluster-forming threshold, p < .05). These changes eventually resulted in a significant difference in strength between the tested versus untested low priority conjunctions just prior to the commission of the response (Figure 4 - figure supplement 1, the panel on right column of the middle row, the black bars at the top of panel). Importantly, the high priority conjunction also remains active in its untested condition and declines later than the untested low priority conjunction does. Indeed, the untested high priority conjunction does not decline significantly relative to trials when it is tested until after the response is emitted (Figure 4 - figure supplement 1, the panel on right column of the middle row, the red bars at the top of panel). This results in a late emerging interaction effect of the priority and test type, but this is not due to a late emerging low priority conjunctive representation.

In summary, we do not have statistical evidence of a time by effect interaction that allows us to draw strong inferences about timing. Nonetheless, even the patterns we observe are inconsistent with a late emerging low priority conjunctive representation. And if anything, they support a late decline in the untested high priority conjunctive representation. This pattern of the result of the high priority conjunction being sustained until late, even when it is untested, is also notable in light of our observation that the strength of the high priority conjunctive representation interferes behavior when the low priority item is tested, but not vice versa. We now address this point about the timing directly in the results (pg. 15-16) and the discussion (pg. 21), and we include the response locked results in the main text along with the stimulus locked result including exploratory analyses reported here.

Reviewer #3 (Public Review):

This study aims to address the important question of whether working memory can hold multiple conjunctive task representations. The authors combined a retro-cue working memory paradigm with their previous task design that cleverly constructed multiple conjunctive tasks with the same set of stimuli, rules, and responses. They used advanced EEG analytical skills to provide the temporal dynamics of concurrent working memory representation of multiple task representations and task features (e.g., stimulus and responses) and how their representation strength changes as a function of priority and task relevance. The results generally support the authors' conclusion that multiple task representations can be simultaneously manipulated in working memory.

We appreciate these helpful comments, and were pleased that the reviewer shares our view that these results may be broadly impactful.

Author Response

Reviewer #2 (Public Review):

Reviewer #2 was critical of every aspect of our manuscript and we were disappointed that they failed to appreciate the significance of our findings. However, we have responded to each point as described below:

1) The experiment displayed in Figure 5 is deeply flawed for multiple reasons and should be removed from the manuscript entirely. A Michaelis-Menton plot compares the initial rate of a reaction versus substrate concentration. Instead, the authors plotted the fraction of SsrB that is phosphorylated after 10 minutes at various substrate concentrations. Such a plot must reach saturation because the enzyme is limiting, whereas it is not always possible to achieve saturation in a genuine Michaelis-Menton plot. Because no reaction rates were measured, it is not possible to derive kcat values from the data.

Mea culpa. We now plot our phosphorylation data and describe the mid-point as a k0.5 and have removed Fig. 1g. When we directly compare the H12 mutant to wt at neutral pH, its phosphorylation level is less compared to the wt (see new Fig. 4a). The wt phosphorylation is reduced at acid pH, (Fig 4b), but with His12Q, there was no difference in phosphorylation between neutral and acid pH (Fig 4c). It is important to include this data, because in RcsB, a close homolog of SsrB, an H12A mutant was not phosphorylated by acetyl phosphate and it was incapable of binding to DNA, unlike what we show here with SsrB.

(i) Increasing the concentration of the phosphoramidite substrate increased ionic strength. Response regulator active sites contain many charged moieties and autophosphorylation of at least one response regulator (CheY) is inhibited by increasing ionic strength (PMID 10471801).

The reviewer raises some interesting points and they are based on CheY phosphorylation by small molecules. We have a long history of studying OmpR and SsrB as well as other RRs and we know that they can all behave very differently from “canonical signaling”. We examined the effect of ionic strength on SsrB phosphorylation and it was relatively insensitive to changes in ionic strength (our original buffer was 267-430 mOsm and in each case, we have 90% phosphorylation). However, we repeated all of the phosphorylation experiments and kept ionic strength constant. These data are now presented in the revised manuscript.

(ii) Autophosphorylation with phosphoramidite is pH dependent because the nitrogen on the donor must be protonated to form a good leaving group (PMID 9398221). The pKa of phosphoramidite is ~8. Therefore, the fraction of phosphoramidite that is reactive (i.e., protonated) will be very different at pH 6.1 and 7.4.

We are aware of those findings, but we are comparing the H12 mutant with the wt protein in each case. There is no reason to believe that the presence of the mutant should alter the phosphoramidate substrate, so we are comparing how the wt phosphorylation compares with the mutant (Fig 4b, c).

(iii) Response regulator autophosphorylation absolutely depends on the presence of a divalent metal ion (usually Mg2+) in the active site (PMID 2201404). There is no guarantee that the 20 mM Mg2+ included in the reaction is sufficient to saturate SsrB. Furthermore, as the authors themselves note, the amino acid at SsrB position 12 is likely to affect the affinity of Mg2+ binding. Therefore, the fraction of SsrB that is reactive (i.e. has Mg2+ bound) may differ between wildtype and the H12Q mutant, and/or between wildtype at different pHs (because the protonation state of His12 changes).

This is exactly the point that we are making. And why we varied the magnesium concentration (increasing to 50-100 mM). There was a slight increase in phosphorylation at 50 mM MgCl2 compared to 20 mM, and only a slight increase between 50 and 100 mM at pH 6.1. The revised phosphorylation experiments all contain 100 mM MgCl2.

2) The data in Figures 1abcd and 3de are clearly sigmoidal rather than hyperbolic, indicating cooperativity. However, there are insufficient data points between the upper and lower bounds to accurately calculate the Hill coefficient or KD values. This limitation of the data means that comparisons of apparent Hill coefficient or KD values under different conditions cannot be the basis of credible conclusions.

We respectfully disagree. In every curve that we provide, there is at least one data point in the transition between low and high binding. With the mutant H12Q, we did manage to get two data points in the transition and the KD was the same as the wildtype (Fig. 2). We provide an analysis of the binding curve which nicely demonstrates the range of KD values based on the lowest and highest error in the point (132-168 nM) and it doesn’t significantly change the value (this is now shown in Fig.1– figure supplement 1). The very high affinity we observed at pH 6.1 (KD ~5 nM) makes the range of possibilities between 4-8 nM (i.e. still VERY high affinity). These range in affinities at neutral and acid pH are very reminiscent of affinities we measured for OmpR and OmpR~P at the porin promoters, suggesting that acid pH puts SsrB in an activated state even in the absence of phosphorylation. A similar argument holds for the Hill coefficient (see Figure).

3) There are hundreds of receiver domain structures in PDB. There is some variation, but to a first approximation receiver domain structures, all exhibit an (alpha/beta)5 fold. The structure of SsrB predicted by i-TASSER breaks the standard beta-2 strand into two parts, which throws off the numbering for subsequent beta strands. Given the highly conserved receiver domain fold, I am skeptical that the predicted i-TASSER structure is correct or adds any value to the manuscript. If the authors wish to retain the structure of the manuscript, then they should point out the unusual feature and the consequence of strand numbering.

We now include a new model based on the RcsB/DNA crystal structure that eliminates this problem (see new Fig.2– figure supplement 2). We have replaced this model with an Alphafold prediction that was energy minimized to align with the RcsB dimer crystal structure (Fig.5– figure supplement 2). This model retains the original (beta/alpha)5 fold, so the classical numbering is retained.

4) The detailed predictions of active site structure in Supplementary Figure 5 are not physiologically relevant because Mg2+ was not included in the simulation. The presence of a divalent cation binding to Asp10 and Asp11 is likely to substantially alter interactions between Asp 10, Asp11, His12, and Lys109.

See response to 1iii, above and new Fig.5– figure supplement 2. Author response image 1 is a zoomed-in snapshot of supplementary Figure 8c that has been modelled using the RcsB dimer bound to BeF3 and Mg2+(6ZIX). Both the i-TASSER and Alphafold model receiver domains align well with this structure, and the polar contacts and pi-cation interactions made by His12 are maintained.

Author response image 1.

5) The authors present an AlphaFold model of an SsrB dimer, and note that His12 is at the dimer interface. However, the authors also believe that a higher-order oligomer of SsrB binds to DNA in a pH-dependent manner. Do the authors have any suggestions or informed speculation about how His12 might affect higher-order oligomerization than dimerization?

As mentioned to point 3, above, we now include a new model of an SsrB dimer bound to DNA based on our NMR structure of the CTD and the RcsB/DNA structure. In the RcsB paper, they also have evidence for a higher-order oligomer in the crystal structure of unphosphorylated (and BeF3-) RcsB, which showed an asymmetric unit containing 6 molecules of RcsB, which form 3 dimers arranged in a hexameric structure that resembles a cylinder. This configuration involves a crossed conformation with the REC of one molecule interacting with the DBD of another and interestingly, His12 is interacting with the DBD of another molecule. We modelled an SsrB oligomer structure using the RcsB hexamer as a template and have included it as a new figure (see Fig.5– figure supplement 3) and in the revised discussion (lines 432-448).

Author Response

Reviewer #1 (Public Review):

1) One nagging concern is that the category structure in the CNN reflects the category structure baked into color space. Several groups (e.g. Regier, Zaslavsky, et al) have argued that color category structure emerges and evolves from the structure of the color space itself. Other groups have argued that the color category structure recovered with, say, the Munsell space may partially be attributed to variation in saturation across the space (Witzel). How can one show that these properties of the space are not the root cause of the structure recovered by the CNN, independent of the role of the CNN in object recognition?

We agree that there is overlap with the previous studies on color structure. In our revision, we show that color categories are directly linked to the CNN being trained on the objectrecognition task and not the CNN per se. We repeated our analysis on a scene-trained network (using the same input set) and find that here the color representation in the final layer deviates considerably from the one created for object classification. Given the input set is the same, it strongly suggests that any reflection of the structure of the input space is to the benefit of recognizing objects (see the bottom of “Border Invariance” section; Page 7). Furthermore, the new experiments with random hue shifts to the input images show that in this case stable borders do not arise, as might be expected if the border invariance was a consequence of the chosen color space only.

A crucial distinction to previous results is also, is that in our analysis, by replacing the final layer, specifically, we look at the representation that the network has built to perform the object classification task on. As such the current finding goes beyond the notion that the color category structure is already reflected in the color space.

2) In Figure 1, it could be useful to illustrate the central observation by showing a single example, as in Figure 1 B, C, where the trained color is not in the center of the color category. In other words, if the category structure is immune to the training set, then it should be possible to set up a very unlikely set of training stimuli (ones that are as far away from the center of the color category while still being categorized most of the time as the color category). This is related to what is in E, but is distinctive for two reasons: first, it is a post hoc test of the hypothesis recovered in the data-driven way by E; and second, it would provide an illustration of the key observation, that the category boundaries do not correspond to the median distance between training colors. Figure 5 begins to show something of this sort of a test, but it is bound up with the other control related to shape.

We have now added a post-hoc test where we shift the training bands from likely to unlikely positions using the original paradigm: Retraining output layers whilst shifting training bands from the left to the right category-edge (in 9 steps) we can see the invariance to the category bounds specifically (see Supp. Inf.: Figure S11). The most extreme cases (top and bottom row) have the training bands right at the edge of the border, which are the interesting cases the reviewer refers to. We also added 7 steps in between to show how the borders shift with the bands.

Similarly, if the claim is that there are six (or seven?) color categories, regardless of the number of colors used to train the data, it would be helpful to show the result of one iteration of the training that uses say 4 colors for training and another iteration of the training that uses say 9 colors for training.

We have now included the figure presented in 1E, but for all the color iterations used (see SI: Figure S10. We are also happy to include a single iteration, but believe this gives the most complete view for what the reviewer is asking.

The text asserts that Figure 2 reflects training on a range of color categories (from 4 to 9) but doesn’t break them out. This is an issue because the average across these iterations could simply be heavily biased by training on one specific number of categories (e.g. the number used in Figure 1). These considerations also prompt the query: how did you pick 4 and 9 as the limits for the tests? Why not 2 and 20? (the largest range of basic color categories that could plausibly be recovered in the set of all languages)?

The number of output nodes was inspired by the number of basic color categories that English speakers observe in the hue spectrum (in which a number of the basic categories are not represented). We understand that this is not a strong reason, however, unfortunately the lack of studies on color categories in CNNs forced us to approach this in an explorative manner. We have adapted the text to better reflect this shortcoming (Bottom page 4). Naturally if the data would have indicated that these numbers weren’t a good fit, we would have adapted the range. (if there were more categories, we would have expected more noise and we would have increased the number of training bands to test this). As indicated above, we have now also included the classification plots for all the different counts, so the reader can review this as well (SI: Section 9).

3) Regarding the transition points in Figure 2A, indicated by red dots: how strong (transition count) and reliable (consistent across iterations) are these points? The one between red and orange seems especially willfully placed.

To answer the question on the consistency we have now included a repetition of the ResNet18, with the ResNet34, ResNet50 and ResNet101 in the SI (section 1). We have also introduced a novel section presenting the result of alternate CNNs to the SI (section S8). Despite small idiosyncrasies the general pattern of results recurs.

Concerning the red-orange border, it was not willfully placed, but we very much understand that in isolation it looks like it could simply be the result of noise. Nevertheless, the recurrence of this border in several analyses made us confident that it does reflect a meaningful invariance. Notably:

• We find a more robust peak between red and orange in the luminance control (SI section 3).

• The evolutionary algorithm with 7 borders also places a border in this position.

• We find the peak recurs in the Resnet-18 replication as well as several of the deeper ResNets and several of the other CNNs (SI section 1)

• We also find that the peak is present throughout the different layers of the ResNet-18.

4) Figure 2E and Figure 5B are useful tests of the extent to which the categorical structure recovered by the CNNs shifts with the colors used to train the classifier, and it certainly looks like there is some invariance in category boundaries with respect to the specific colors uses to train the classifier, an important and interesting result. But these analyses do not actually address the claim implied by the analyses: that the performance of the CNN matches human performance. The color categories recovered with the CNN are not perfectly invariant, as the authors point out. The analyses presented in the paper (e.g. Figure 2E) tests whether there is as much shift in the boundaries as there is stasis, but that’s not quite the test if the goal is to link the categorical behavior of the CNN with human behavior. To evaluate the results, it would be helpful to know what would be expected based on human performance.

We understand the lack of human data was a considerable shortcoming of the previous version of the manuscript. We have now collected human data in a match-to-sample task modeled on our CNN experiment. As with the CNN we find that the degree of border invariance does fluctuate considerably. While categorical borders are not exact matches, we do broadly find the same category prototypes and also see that categories in the red-to-yellow range are quite narrow in both humans and CNNs. Please, see the new “Human Psychophysics” (page 8) addition in the manuscript for more details.

5) The paper takes up a test of color categorization invariant to luminance. There are arguments in the literature that hue and luminance cannot be decoupled-that luminance is essential to how color is encoded and to color categorization. Some discussion of this might help the reader who has followed this literature.

We have added some discussion of the interaction between luminance and color categories (e.g., Lindsay & Brown, 2009) at the bottom of page 6/ top of page 7. The current analysis mainly aimed at excluding that the borders are solely based on luminance.

Related, the argument that “neighboring colors in HSV will be neighboring colors in the RGB space” is not persuasive. Surely this is true of any color space?

We removed the argument about “neighboring colors”. Our procedure requires the use of a hue spectrum that wraps around the color space while including many of the highly saturated colors that are typical prototypes for human color categories. We have elected to use the hue spectrum from the HSV color space at full saturation and brightness, which is represented by the edges of the RGB color cube. As this is the space in which our network was trained, it does not introduce any deformations into the color space. Other potential choices of color space either include strong non-linear transformations that stretch and compress certain parts of the RGB cube, or exclude a large portion of the RGB gamut (yellow in particular).

We have adapted the text to better reflect our reasoning (page 6, top of paragraph 2).

6) The paper would benefit from an analysis and discussion of the images used to originally train the CNN. Presumably, there are a large number of images that depict manmade artificially coloured objects. To what extent do the present results reflect statistical patterns in the way the images were created, and/or the colors of the things depicted? How do results on color categorization that derive from images (e.g. trained with neural networks, as in Rosenthal et al and presently) differ (or not) from results that derive from natural scenes (as in Yendrikhovskij?).

We initially hoped we could perhaps analyze differences between colors in objects and background like in Rosenthal, unfortunately in ImageNet we did not find clear differences between pixels in the bounding boxes of objects provided with ImageNet and pixels outside these boxes (most likely because the rectangular bounding boxes still contain many background pixels). However, if we look at the results from the K-means analysis presented in Figure S6 (Suppl. Inf.) of the supplemental materials and the color categorization throughout the layers in the objecttrained network (end of the first experiment on page 7) as well as the color categorization in humans (Human Psychophysics starting on page 8), we see very similar border positions arise.

7) It could be quite instructive to analyze what's going on in the errors in the output of the classifiers, as e.g. in Figure 1E. There are some interesting effects at the crossover points, where the two green categories seem to split and swap, the cyan band (hue % 20) emerges between orange and green, and the pink/purple boundary seems to have a large number of green/blue results. What is happening here?

One issue with training the network on the color task, is that we can never fully guarantee that the network is using color to resolve the task and we suspected that in some cases the network may rely on other factors as well, such as luminance. When we look at the same type of plots for the luminance-controlled task (see below left) presented in the supplemental materials we do not see these transgressions. Also, when we look at versions of the original training, but using more bands, luminance will be less reliable and we also don’t see these transgressions (see right plot below).

8) The second experiment using an evolutionary algorithm to test the location of the color boundaries is potentially valuable, but it is weakened because it pre-determines the number of categories. It would be more powerful if the experiment could recover both the number and location of the categories based on the "categorization principle" (colors within a category are harder to tell apart than colors across a color category boundary). This should be possible by a sensible sampling of the parameter space, even in a very large parameter space.

The main point of the genetic algorithm was to see whether the border locations would be corroborated by an algorithm using the principle of categorical perception. Unfortunately, an exact approach to determining the number of borders is difficult, because some border invariances are clearly stronger than others. Running the algorithm with the number of borders as a free parameter just leads to a minimal number of borders, as 100% correct is always obtained when there is only one category left. In general, as the network can simply combine categories into a class at no cost (actually, having less borders will reduce noise) it is to be expected that less classes will lead to better performance. As such, in estimating what the optimal category count would be, we would need to introduce some subjective trade-off between accuracy and class count.

9) Finally, the paper sets itself up as taking "a different approach by evaluating whether color categorization could be a side effect of learning object recognition", as distinct from the approach of studying "communicative concepts". But these approaches are intimately related. The central observation in Gibson et al. is not the discovery of warm-vscool categories (these as the most basic color categories have been known for centuries), but rather the relationship of these categories to the color statistics of objects-those parts of the scene that we care about enough to label. This idea, that color categories reflect the uses to which we put our color-vision system, is extended in Rosenthal et al., where the structure of color space itself is understood in terms of categorizing objects versus backgrounds (u') and the most basic object categorization distinction, animate versus inanimate (v'). The introduction argues, rightly in our view, that "A link between color categories and objects would be able to bridge the discrepancy between models that rely on communicative concepts to incorporate the varying usefulness of color, on the one hand, and the experimental findings laid out in this paragraph on the other". This is precisely the link forged by the observation that the warmcool category distinction in color naming correlates with object-color statistics (Gibson, 2017; see also Rosenthal et al., 2018). The argument in Gibson and Rosenthal is that color categorization structure emerges because of the color statistics of the world, specifically the color statistics of the parts of the world that we label as objects, which is the same approach adopted by the present work. The use of CNNs is a clever and powerful test of the success of this approach.

We are sorry we did not properly highlight the enormous importance of these two earlier papers in our previous version of the manuscript. We have now elaborated our description of Gibson’s work to better reflect the important relation between the usefulness of colors and color categories (Page 2, middle and Page 19 par. above methods). We think our work nicely extends the earlier work by showing that their approach works even at a more general level with more color categories,

Author Response

Reviewer #1 (Public Review):

Using health insurance claims data (from 8M subjects), a retrospective propensity score matched cohort study was performed (450K in both groups) to quantify associations between bisphosphonate (BP) use and COVID- 19 related outcomes (COVID-19 diagnosis, testing and COVID-19 hospitalization. The observation periods were 1-1-2019 till 2-29-2020 for BP use and from 3-1-2020 and 6-30-2020 for the COVID endpoints. In primary and sensitivity analyses BP use was consistently associated with lower odds for COVID-19, testing and COVID-19 hospitalization.

The major strength of this study is the size of the study population, allowing a propensity-based matched- cohort study with 450K in both groups, with a sizeable number of COVID-19 related endpoints. Health insurance claims data were used with the intrinsic risk of some misclassification for exposure. In addition there probably is misclassification of endpoints as testing for COVID-19 was limited during the study period. Furthermore, the retrospective nature of the study includes the risk of residual confounding, which has been addressed - to some extent - by sensitivity analyses.

In all analyses there is a consistent finding that BP exposure is associated with reduced odds for COVID-19 related outcomes. The effect size is large, with high precision.

The authors extensively discuss the (many) potential limitations inherent to the study design and conclude that these findings warrant confirmation, preferably in intervention studies. If confirmed BP use could be a powerful adjunct in the prevention of infection and hospitalization due to COVID-19.

We thank the reviewer for this overall very positive feedback. We appreciate the reviewer's comments regarding the potential risks associated with misclassification of exposure and other potential limitations, which we have sought to address in a number of sensitivity analyses and are also addressing in the discussion of our paper. In addition, as noted by the reviewer, the observed effect size of BP use on COVID-19 related outcomes is large, with high precision, which we feel is a strong argument to explore this class of drugs in further prospective studies.

Reviewer #2 (Public Review):

The authors performed a retrospective cohort study using claims data to assess the causal relationship between bisphosphonate (BP) use and COVID-19 outcomes. They used propensity score matching to adjust for measured confounders. This is an interesting study and the authors performed several sensitivity analyses to assess the robustness of their findings. The authors are properly cautious in the interpretation of their results and justly call for randomized controlled trials to confirm a causal relationship. However, there are some methodological limitations that are not properly addressed yet.

Strengths of the paper include:

(A) Availability of a large dataset.

(B) Using propensity score matching to adjust for confounding.

(C) Sensitivity analyses to challenge key assumptions (although not all of them add value in my opinion, see specific comments)

(D) Cautious interpretation of results, the authors are aware of the limitations of the study design.

Limitation of the paper are:

(A) This is an observational study using register data. Therefore, the study is prone to residual confounding and information bias. The authors are well aware of that.

(B) The authors adjusted for Carlson comorbidity index whereas they had individual comorbidity data available and a dataset large enough to adjust for each comorbidity separately.

(C) The primary analysis violates the positivity assumption (a substantial part of the population had no indication for bisphosphonates; see specific comments). I feel that one of the sensitivity analyses 1 or 2 would be more suited for a primary analysis.

(D) Some of the other sensitivity analyses have underlying assumptions that are not discussed and do not necessarily hold (see specific comments).

In its current form the limitations hinder a good interpretation of the results and, therefore, in my opinion do not support the conclusion of the paper.

The finding of a substantial risk reduction of (severe) COVID-19 in bisphosphonate users compared to non- users in this observational study may be of interest to other researchers considering to set up randomized controlled trials for evaluation of repurpose drugs for prevention of (severe) COVID-19.

We thank the reviewer for the insightful comments and questions related to our manuscript. Our response to the concerns regarding limitations of our study is as follows:

(A) We agree that there is likely residual confounding and information bias due to use of US health insurance claims datasets which do not include information on certain potentially relevant variables. Nonetheless, given the large effect size and precision of our analysis, we feel that our findings support our main conclusion that additional prospective trials appear warranted to further explore whether BPs might confer a meaure of protection against severe respiratory infections, including COVID-19. We have added a sentence on the second page of our Discussion (line 859-860) to emphasize this point: "Specifically, there is the potential that key patient characteristics impacting outcomes could not be derived from claims data."

(B) The progression of this study mirrors the real-world performance of the analysis where we initially used the CCI in matching to control for comorbidity burden on a broader scale. This was our a priori approach. After observing large effect sizes, we performed more stringent matching for sensitivity analyses 1 and 2. Irrespective of the matching strategy chosen, effect sizes remained similar for all outcome parameters. Therefore, we elected to include both the primary analysis and the sensitivity analyses with more stringent matching in order to more transparently show what was done in entirety during our analyses, as we feel it displays all of the efforts taken to identify sources of unmeasured confounding which could have impacted our results.

(C) We agree that the positivity assumption is a key factor to consider when building comparable treatment cohorts. We also agree that it is the important to separately perform the analysis for either all patients with an indication for use of BPs and for other anti-osteoporosis medications, as we have done in our analysis of the Osteo-Dx-Rx cohort and Bone-Rx cohort, respectively. However, we did not have sufficient data, a priori, to determine whether BP users would be more similar in their risk of COVID-19 outcomes to non- users or to other users of anti-resorptive medications. In addition, we believe that this specific limitation does not negate our findings in the primary analysis for the following reasons: (1) ‘Type of Outcome’: the outcomes in this study are related to infectious disease and are not direct clinical outcomes of any known treatment benefits of BPs. The clinical benefits being assessed - impact of BP use on COVID-19-related outcomes - were essentially unknown at the time of the study data; this fact mitigates the impact of any violation of the positivity assumption; and (2) ‘Clinical Population’: after propensity score matching, both the BP user and the BP non-user group in the primary analysis mainly consisted of older females (90.1% female, 97.2% age>50), which is the main population with clinical indications for BP use. According to NCHS Data Brief No. 93 (April 2012) released by the CDC, ~75% and 95% of US women between 60-69 and 70-79 suffer from either low bone mass or osteoporosis, respectively, and essentially all women (and 70% of men) above age 80 suffer from these conditions, which often go undiagnosed (https://www.cdc.gov/nchs/data/databriefs/db93.pdf). Women aged 60 and older make up ~75% of our study population (Table 1). Although bone density measurements are not available for non- BP users in the matched primary cohort, there is a high probability that the incidence of osteoporosis and/or low bone mass in these patients was similar to the national average. This justifies the assumption that BP therapy was indicated for most non-BP users in the matched primary cohort. Arguably, for these patients the positivity assumption was not violated.

(D) We will discuss in detail below the specific issues raised by the reviewer regarding our sensitivity analyses. In general we acknowledge that individual analytical and/or matching approaches may each have their own limitations, but the analyses performed herein were done to test in a systematic fashion the different critical threats to the validity of our initial results in the primary cohort analysis, which were based on a priori-defined methods and yielded a large and robust effect size. Thus, the individual sensitivity analyses should be considered in the greater context of the entire project.

Specific comments (in order of manuscript):

Methods:

Line 158: it is unclear how the authors dealt with patients who died during the follow-up period. The wording suggests they were excluded which would be inappropriate.

When this study was executed, we were unable to link the patient-level US insurance claims data with patient-level mortality data due to HIPAA concerns. Therefore, line 158 (now 177) defines continuous insurance coverage during the observation period as a verifiable eligibility criterion we used for patient inclusion. It was necessary to disqualify individuals who discontinued insurance coverage for a variety of reasons, e.g. due to loss or change of coverage, relocation etc., but our approach also eliminated patients who died. Appendix 3 (line 2449ff) describes methods we employed post hoc to assess how censoring due to death could have impacted our analyses. We discuss our conclusions from this post hoc analysis in the main text (lines 1053-1058) as follows: "An additional limitation is potential censoring of patients who died during the observation period, resulting in truncated insurance eligibility and exclusion based on the continuous insurance eligibility requirement. However, modelling the impact of censoring by using death rates observed in BP users and non-users in the first six months of 2020 and attributing all deaths as COVID-19-related did not significantly alter the decreased odds of COVID-19 diagnosis in BP users (see Appendix 3)."

Why did the authors use CCI for propensity matching rather than the individual comorbid conditions? I presume using separate variables will improve the comparability of the cohorts. The authors discuss imbalances in comorbidities as a limitation but should rather have avoided this.

CCI was the a priori approach defined at the study outset and was chosen due to the widespread use and understanding of this score. The general CCI score was originally planned for matching in order to have the largest possible study population since we did not know how many patients would meet all criteria as well as have an event of interest. After realizing we had adequate sample size to power matching using stricter criteria, we proceeded to perform subsequent sensitivity analyses on more stringently matched cohorts (sensitivity analysis 2).

Line 301-10: it seems unnecesary to me to adjust for the given covariates while these were already used for propensity score matching (except comorbidities, but see previous comment). The manuscript doesn't give a rationale why did the authors choose for this 'double correction'.

The following language was added to the methods section (lines 325-327): “Demographic characteristics used in the matching procedure were also included in the final outcome regressions to control for the impact of those characteristics on outcomes modelled.”

The following language was added to the Discussion section regarding the potential limitations of our srudy (lines 1078-1085): “Another limitation in the current study is related to a potential ‘double correction’ of patient characteristics that were included in both the propensity score matching procedure as well as the outcome regression modelling, which could lead to overfitting of the regression models and an overestimation of the measured treatment effect. Covariates were included in the regression models since these characteristics could have differential impacts on the outcomes themselves, and our results show that the adjusted ORs were in fact larger (showing a decreased effect size) when compared to the unadjusted ORs, which show the difference in effect sizes of the matched populations alone.”

In causal research a very important assumption is the 'positivity assumption', which means that none of the individuals has a probability of zero or one to be exposed. Including everyone would therefore not be appropriate. My suggestion is to include either all patients with an indication (based on diagnosis) or all that use an anti-osteoporosis (AOP) drug (or one as the primary and the other as the sensitivity analysis) instead of using these cohorts as sensitivity analyses. The choice should in my opinion be based on two aspects: whether it is likely that other AOP drugs have an effect on the COVID-19 outcomes and whether BP users are deemed to be more similar (in their risk of COVID-19 outcomes) to non-users or to other AOP drug users. Or alternatively, the authors might have discussed the positivity assumption and argue why this is not applicable to their primary analysis.

The following text has been added to the Discussion section addressing potential limitations of our study (lines 987-1009): " Another potential limitation of this study relates to the positivity assumption, which when building comparable treatment cohorts is violated when the comparator population does not have an indication for the exposure being modelled 56. This limitation is present in the primary cohort comparisons between BP users and BP non-users, as well as in the sensitivity analyses involving other preventive medications. This limitation, however, is mitigated by the fact that the outcomes in this study are related to infectious disease and are not direct clinical outcomes of known treatment benefits of BPs. The fact that the clinical benefits being assessed – the impact of BPs on COVID-related outcomes – was essentially unknown clinically at the time of the study data minimizes the impact of violation of the positivity assumption. Furthermore, our sensitivity analyses involving the “Bone-Rx” and “Osteo-Dx- Rx” cohorts did not suffer this potential violation, and the results from those analyses support those from the primary analysis cohort comparisons. Moreover, we note that the propensity score matched BP users and BP non-users in the primary analysis cohort mainly consisted of older females. According to the CDC, ~75% and 95% of US women between 60-69 and 70-79 suffer from either low bone mass or osteoporosis, respectively (https://www.cdc.gov/nchs/data/databriefs/db93.pdf). Essentially all women (and 70% of men) above age 80 suffer from these conditions, which often go undiagnosed. Women aged 60 and older represent ~75% of our study population (Table 1). Although bone density measurements are not available for non-BP users in the matched primary cohort, there is a high probability that the incidence of osteoporosis and/or low bone mass in these patients was similar to the national average.Thus, BP therapy would have been indicated for most non-BP users in the matched primary cohort, and arguably, for these patients the positivity assumption was not violated."

Sensitivity Analysis 3: Association of BP-use with Exploratory Negative Control Outcomes: what is the implicit assumption in this analysis? I think the assumption here is that any residual confounding would be of the same magnitude for these outcomes. But that depends on the strength of the association between the confounder and the outcome which needs not be the same. Here, risk avoiding behavior (social distancing) is the most obvious unmeasured confounder, which may not have a strong effect on other health outcomes. Also it is unclear to me why acute cholecystitis and acute pancreatitis-related inpatient/emergency-room were selected as negative controls. Do the authors have convincing evidence that BPs have no effect on these outcomes? Yet, if the authors believe that this is indeed a valid approach to measure residual confounding, I think the authors might have taken a step further and present ORs for BP → COVID-19 outcomes that are corrected for the unmeasured confounding. (e.g. if OR BP → COVID-19 is ~ 0.2 and OR BP → acute cholecystitis is ~ 0.5, then 'corrected' OR of BP → COVID-19 would be ~ 0.4.

We appreciate the reviewer’s thoughtful comments regarding the differential strength of the association between unmeasured confounders and outcome. We had initially selected acute cholecystitis and pancreatitis-related inpatient and emergency room visits as negative controls because we deemed them to be emergent clinical scenarios that should not be impacted by risk avoiding behavior. However, upon further search, we identified several publications that suggest a potential impact of osteoporosis and/or BPs on gallbladder diseases (DOIhttps://doi.org/10.1186/s12876-014-0192-z; http://dx.doi.org/10.1136/annrheumdis-2017-eular.3900), thus calling the validity our strategy into question. We therefore agree that the designation of negative control outcomes is problematic and adds relatively little to the overall story. Therefore, we have removed these analyses from the revised manuscript.

Sensitivity Analysis 4: Association of BP-use with Exploratory Positive Control Outcomes: this doesn't help me be convinced of the lack of bias. If previous researchers suffered from residual confounding, the same type of mechanisms apply here. (It might still be valuable to replicate the previous findings, but not as a sensitivity analysis of the current study).

We agree that the same residual confounding in previous research papers could be present in our study. Nonetheless, it was important to assess whether our analysis would be potentially subject to additional (or different) confounding due to the nature of insurance claims data as compared to the previous electronic record-based studies. Therefore, it was relevant to see if previous findings of an association between BP use and upper respiratory infections are observable in our cohort.

The second goal of sensitivity analysis #4 (now #3) was to see whether associations could be found on different sets of respiratory infection-based conditions, both during the time of the pandemic/study period as well as during the pre-pandemic time, i.e. before medical care in the US was significantly impacted by the pandemic. In light of these considerations, we feel that sensitivity analysis 4 adds value by showing consistency in our core findings.

Sensitivity Analysis 5: Association of Other Preventive Drugs with COVID-19-Related Outcomes: Same here as for sensitivity analysis 3: the assumption that the association of unmeasured confounders with other drugs is equally strong as for BPs. Authors should explicitly state the assumptions of the sensitivity analyses and argue why they are reasonable.

The following sentence was added to the Discussion section (lines 1019-1020): “ "These analyses were based on the assumption that the association of unmeasured confounders with other drugs is comparable in magnitude and quality as for BPs."

Results: The data are clearly presented. The C-statistic / ROC-AUC of the propensity model is missing.

Unfortunately, a significant amount of time has passed since execution of our original analysis of the Komodo dataset by our co-authors at Cerner Enviza. To date, our ability to perform follow-up studies with the Komodo dataset (which is exclusively housed on Komodo's secure servers) has become limited because business arrangements between these companies have been terminated, and the pertinent statistical software is no longer active. This issue prevents us from attaining the original C-statistic and ROC-AUC information, however, we were able to extract the actual; propensity scores themselves for the base cohort matching (BP-users versus non-users). The table below illustrates that the distribution of propensity scores for the base cohort match ranged from <0.01 to a max of 0.49, with 81.4% of patients having a propensity score of 10-49%, and 52.9% of patients having a propensity score of 20-49%. This distribution is unlikely to reflect patients who had a propensity score of either all 0 or all 1.

Discussion:

When discussing other studies the authors reduce these results to 'did' or 'did not find an association'. Although commonly practiced, it doesn't justify the statistical uncertainty of both positive and negative findings. Instead I encourage the authors to include effect estimates and confidence intervals. This is particularly relevant for studies that are inconclusive (i.e. lower bound of confidence interval not excluding a clinically relevant reduction while upper bound not excluding a NULL-effect).

We appreciate the reviewer’s suggestion and have added this information on p.21/22 in the Discussion.

Line 1145 "These retrospective findings strongly suggest that BPs should be considered for prophylactic and/or therapeutic use in individuals at risk of SARS-CoV-2 infection." I agree for prophylactic use but do not see how the study results suggest anything for therapeutic use.

We have removed “and/or therapeutic use” from this sentence (line 1088-1090).

The authors should discuss the acceptability of using BPs as preventive treatment (long-term use in persons without osteoporosis or other indication for BPs). This is not my expertise but I reckon there will be little experience with long-term inhibiting osteoblasts in people with healthy bones. The authors should also discuss what prospective study design would be suitable and what sample size would be needed to demonstrate a reasonable reduction. (Say 50% accounting for some residual confounding being present in the current study.)

Although BPs are also used in pediatric populations and in patients without osteoporosis (for example, patients with malignancy), we do recognize the lack of long-term safety data in use of BPs as preventative treatments. We tried to partially address this concern in our sub-stratified analysis of COVID-19 related outcomes and time of exposure to BP. Reassuringly, we observed that patients newly prescribed alendronic acid in February 2020 also had decreased odds of COVID-19 related outcomes (Figure 3B), suggesting that the duration of BP treatment may not need to be long-term. This was further discussed in the last paragraph of our Discussion where we state that " BP use at the time of infection may not be necessary for protection against COVID-19. Rather, our results suggest that prophylactic BP therapy may be sufficient to achieve a potentially rapid and sustained immune modulation resulting in profound mitigation of the incidence and/or severity of infections by SARS- CoV-2."

We agree that a future prospective study on the effect of BPs on COVID-19 related outcomes will require careful consideration of the study design, sample size, statistical power etc. However, we feel that a detailed discussion of these considerations is beyond the scope of the present study.

The authors should discuss the fact that confounders were based on registry data which is prone to misclassification. This can result in residual confounding.

Some potential sources of misclassification have been discussed on line 932-948. In addition, the following language was added (line 970-985): "Additionally, limitations may be present due to misclassification bias of study outcomes due to the specific procedure/diagnostic codes used as well as the potential for residual confounding occurring for patient characteristics related to study outcomes that are unable to be operationalized in claims data, which would impact all cohort comparisons. For SARS- CoV-2 testing, procedure codes were limited to those testing for active infection, and therefore observations could be missed if they were captured via antibody testing (CPT 86318, 86328). These codes were excluded a priori due to the focus on the symptomatic COVID-19 population. Furthermore, for the COVID-19 diagnosis and hospitalization outcomes, all events were identified using the ICD-10 code for lab-confirmed COVID-19 (U07.1), and therefore events with an associated diagnosis code for suspected COVID-19 (U07.2) were not included. This was done to have a more stringent algorithm when identifying COVID-19-related events, and any impact of events identified using U07.2 is considered minimal, as previous studies of the early COVID-19 outbreak have found that U07.1 alone has a positive predictive value of 94%55, and for this study U07.1 captured 99.2%, 99.0%, and 97.5% of all COVID-19 patient-diagnoses for the primary, “Bone-Rx”, and “Osteo-Dx-Rx” cohorts, respectively."

Author Response:

Evaluation Summary:

The study provides evidence that specific transcriptional responses may underpin the observation that metabolic rates often scale inversely with body mass. The conclusions are supported by direct measurement of metabolic fluxes in mouse and rat livers, although generalizations to other settings remain to be rigorously tested. The study has broad implications for researching and studying animal metabolism and physiology.

We thank the reviewers and editors for this summary. We are pleased that they agree that the conclusions “are supported by direct measurements of metabolic fluxes in mouse and rat livers,” and that “the study has broad implications for researching and studying animal metabolism and physiology. While we fully agree that “generalizations to other settings remain to be rigorously tested,” we have now added a comment comparing our measured liver fluxes in rodents to those recently measured in people:

“While we did not have the capacity to measure liver fluxes in larger mammals in the current study, endogenous glucose production, VPC, and VCS previously measured using PINTA were 50-60% lower in overnight fasted humans than in rats (Petersen et al., 2019), assuming a liver size of 1,500 g in humans.”

Reviewer #1 (Public Review):

It is well established that the energy expenditure and metabolic rate of metazoan organisms scale inversely to body mass, based on the measurement of oxygen consumption and caloric intake. However, the underlying regulatory mechanisms for this observation are poorly defined. To investigate whether metabolic scaling is associated with reduced levels of transcription of metabolic genes in larger animals, the authors reviewed existing transcriptional datasets from liver tissues of five animals (mice, rats, monkeys, humans and cattle) with a 30,000-fold range in average adult body weights. They identified a number of metabolic genes in different pathways of central carbon metabolism whose expression inversely scaled with body size, a majority of which required oxygen, NAD/H or ATP/ADP. Metabolic flux studies on intact liver sections, as well as in live animals also revealed decreased liver metabolic fluxes in rats compared to mice. Interestingly, these differences were not observed in primary hepatocyte cultures, indicating that metabolic scaling is primarily regulated by cell-extrinsic factors and tissue context. These are interesting findings and highlight the importance of measuring metabolic processes in vivo. The measurement of cellular metabolic fluxes in different contexts (cultured, ex vivo tissue sections and live animals) is a major strength of this study. The lack of direct evidence that enzyme levels correlate with mRNA, and the absence of both transcriptional and enzyme activity measurements in cultured cells are potential weaknesses.

We are delighted, and thank Reviewer #1 for stating that “These are interesting findings and highlight the importance of measuring metabolic processes in vivo” and that “The measurement of cellular metabolic fluxes in different contexts (cultured, ex vivo tissue sections and live animals) is a major strength of this study.” In addition, we sincerely thank the reviewer for raising important weaknesses related to the importance of proteomics, transcriptional and enzyme activity measurements in cultured cells, and are pleased to have had the opportunity to add data to address each of these points.

Reviewer #2 (Public Review):

Akingbesote et al. aim to determine the molecular basis of metabolic scaling - the phenomenon that metabolic rates scale inversely with (0.75) body mass. More specifically, they test the hypothesis that expression of genes involved in the regulation of oxygen consumption and substrate metabolism as well as respective fluxes provide a molecular basis for metabolic scaling across five species: mice, rats, monkeys, humans, and cattle. To this end, Akingbesote et al. use publicly available transcriptomics data and identify genes that show decreasing (normalized) expression with increasing mass of organisms. This descriptive analysis is followed by discussing a few relevant examples and (KEGG) pathway enrichment analysis. The authors then used their published PINTA approach with data from their experiments with mice and rats to provide estimates of selected cytosolic and mitochondrial fluxes in vitro, ex vivo, and in vivo; these estimates are then employed in determining if metabolic fluxes scale. The conclusion drawn from these analyses is that estimates of selected fluxes do not differ in vitro between plated hepatocytes of mice and rats, but that differences can be detected using metabolic flux analysis in vivo. As a result, in vivo flux profiling is more relevant to assessing metabolic scaling.

The conclusions are only in part supported by the data and clarifications are needed both with respect to the analysis of transcriptomics data as well as flux estimates:

1. In looking for scaling in gene expression, the authors rely on the assumption that mRNA expression correlates well with protein abundance (citing Schwanhäusser et al., 2011); however, transcripts explain about 40% of variance in protein abundance (this observation holds across multiple species). Hence, the identified patterns based on the transcript data may have little implications for protein abundance or flux.

We agree that, despite the data in the cited publication, gene expression should not be assumed to directly correlate with protein expression, and the two certainly cannot be assumed – without data to equate to metabolic flux. We have removed the citation, and replaced it with proteomics data. Half of the genes available in the proteomics analysis which were found to correlate negatively with body size in our liver transcriptomics analysis also correlated negatively with body size at the level of liver protein expression:

Author Response Figure 1

Additionally, we analyzed available proteomics assessment of left ventricular expression of the three proteins observed to correlate negatively with body mass in the liver proteomics analysis. One of the three genes observed to correlate negatively with body mass in the proteomics analysis of liver, GLUL, was also shown to correlate negatively with body mass when its expression was assessed in the heart:

Author Response Figure 2

However, as discussed in our response to the editor’s point 1, we are limited by the available data, and fully acknowledge that without the capacity to statistically compare groups, we cannot make conclusive statements regarding the proteomics data.

Additionally, we have substantially softened the description of the implications of the transcriptomics data in the Abstract, Introduction, and Discussion, including: - Editing “Together, these data reveal that metabolic scaling extends beyond oxygen consumption to numerous other metabolic pathways, and is likely regulated at the level of gene and protein expression, enzyme activity, and substrate supply” to add the parameters in red. - Removing “Considering that mRNA expression correlates well with protein expression under basal conditions, especially for metabolic genes (Schwanhäusser et al., 2011), we used mRNA expression as a proxy for the relative abundance of metabolic enzymes.” - Added “Further analysis of liver proteomics revealed that approximately half of the genes in liver that scaled at the transcriptional level also scaled at the level of protein expression,” now linking gene expression to protein expression to metabolic flux. - Editing “Numerous metabolic genes…followed the pattern of metabolic scaling, and informed our isotope tracer based in vitro and in vivo metabolic flux studies” to “Numerous metabolic genes…followed the pattern of metabolic scaling. Further analysis of liver proteomics revealed that approximately half of the genes in liver that scaled at the transcriptional level also scaled at the level of protein expression. To determine if gene and protein expression would correlate with scaling at the level of metabolic flux, we performed a comprehensive assessment of liver metabolism in vivo and in vitro using modified Positional Isotopomer NMR Tracer Analysis (PINTA)…” - Edited “Taken together, this study demonstrates systems regulation of metabolic scaling: gene expression in livers showed that scaling occurs to regulate oxygen consumption and substrate supply, isotope-based tracer studies in mice and rats demonstrated the mechanistic function of these enzymes in vivo which was only apparent in the living organism rather than plated cells” to “Taken together, this study demonstrates systems regulation of the ordering of metabolic fluxes according to body size, and provides unique insight into the regulation of metabolic flux across species.” - Removed “Interestingly, the scaling of GPT and ADIPOR1 further suggest that there is dependence on extra-hepatic organs in the scaling of in vivo gluconeogenesis and fatty acid oxidation: that is, skeletal muscle supply of alanine for the liver mediated glucose-alanine cycle and adipose tissue-derived adiponectin signaling. These findings also suggests that the scaling of mitochondrial mass (Porter and Brand, 1995) or mitochondrial proton leak (Porter and Brand, 1993) cannot fully explain metabolic scaling.” - Added “However, it should be noted that metabolic scaling cannot fully be explained at the transcriptional level, because many rate-limiting enzymes in the metabolic processes measured in vivo did not scale at the transcriptional level, and only approximately half of genes that scaled at the level of mRNA scaled at the level of protein. Thus, it is likely that both transcriptional and other mechanisms – such as enzyme activity – are responsible for variations in metabolic flux per unit mass, inversely proportionally to body size. Additionally, the currently available data do not allow us to assess whether expression of certain isoforms of key metabolic enzymes scale differentially across species.”

1. While the procedure used to identify transcripts whose expression scale is clearly described, focusing the enrichment on KEGG pathways can only identify metabolic genes that scale. It would be informative and instructive to investigate if and to what extent genes involved in non-metabolic processes, that affect metabolic rates, also scale.

We acknowledge that focusing the enrichment on KEGG pathways does enrich for the identification of metabolic processes that scale. However, we would respectfully submit that because this manuscript focuses on metabolic scaling, this seems to be the most appropriate setting in which to conduct the analysis. New data added in this revision demonstrate that three metabolic enzymes that scaled in the transcriptomics analysis also scale relative to β-actin, further suggesting that the inverse correlation of gene expression with body weight is primarily confined to metabolic processes:

Author Response Figure 3

In addition, we measured the expression of two structural proteins (collagenase 3 [Mmp3] and Larp6) outside of metabolic pathways, relative to β-actin (Actb), and found that neither was differentially expressed relative to actin in mice versus rats:

Author Response Figure 4

We recognize that these data may be confounded by the fact that Actb expression could potentially be different in mice versus rats; however, the fact that metabolic genes scale relative to β-actin (Actb) expression shows that it is unlikely that global mRNA scaling is unlikely to be the sole cause of the metabolic scaling phenotype.

1. The result on flux ratios and absolute fluxes, based on the equations in Table S1, rely on certain assumptions (e.g. metabolic and isotopic steady state, among the others listed in PINTA); the current presentation does not ensure that all assumptions of PINTA are met in the present setting, so the estimates may be biased, leading to alternative explanations for the observed differences in vivo or the lack thereof in vitro.

However, we fully agree with the reviewer that it is critical to ensure that key assumptions are met when presenting tracer data, and thank them for raising this important point. Thus, we have now added data demonstrating that plasma m+1, m+2, and m+7 glucose are in steady state at 100 min of the 120 min in vivo tracer infusion:

Author Response Figure 5

Additionally, we now show that blood glucose and plasma lactate concentrations have reached steady state as well:

Author Response Figure 6

With these data, we validate that the mice and rats are at metabolic and isotopic steady state by the end of the 120 min tracer infusion. We recognize that we have not validated that liver m+1 and m+2 glucose are at steady state, as that would require two additional groups of mice and rats (to sacrifice at 100 and 110 min, compared to the animals euthanized after 120 min of infusion) and introduce additional variability. Additionally, plasma m+1 and m+2 glucose come from endogenous glucose production from 13C tracer, so if m+1 and m+2 glucose are in steady state in plasma, they must be in steady state in liver.

An additional assumption is that liver glycogen is effectively depleted after the overnight fast utilized in these studies. We have now verified this assumption by comparing fed and overnight fasted liver glycogen concentrations, and detect negligible glycogen after the fast in both rats and mice:

Author Response Figure 7

Additionally, we validated isotopic steady state in our hepatocytes incubated in 3-13C lactate. As expected in plated cell studies, cells reached steady state in both [13C] lactate enrichment and m+1 and m+2 glucose enrichment within 60 min. Because net glucose production is measured using the accumulation of glucose, we do not expect – and did not measure – glucose concentration at steady state, but we did confirm that the accumulation of glucose is linear throughout the 6 hr incubation (thus confirming that 6 hr is a reasonable endpoint):

Author Response Figure 8

We very respectfully submit that after 8 prior publications using PINTA called as such (PMID 28986525, 29307489, 29483297, 31545298, 31578240, 32610084, 32132708, 32179679), in addition to several prior publications that utilized PINTA without the acronym, it would not be the most responsible use of animals to try to prove in this manuscript that PINTA is a legitimate means of assessing substrate fluxes in the current manuscript. However, we thank the reviewer for raising the important point regarding assumptions of the method, thereby allowing us to insert data verifying that the key assumptions are met.

1. The findings regarding the flux estimates seem to be fully determined by observed differences in gluconeogenesis (as demonstrated in Fig. 4). Usage of more involved approaches for metabolic flux analysis may provide wider-reaching conclusions beyond selected fluxes that appear fully coupled.

Fluxes are back-calculated from total glucose production so that methodologically they are “coupled”, but this does not mean that glucose production will always mirror other flues. For example, in our 2015 manuscript using PINTA – although we had not yet named the method “PINTA” – we measured decreased endogenous glucose production (EGP) simultaneously with increased citrate synthase flux (mitochondrial oxidation, VTCA, which we have subsequently begun to call VCS in recognition of the fact that different reactions in the TCA cycle can proceed at different rates, but the calculation is the same) (Perry et al. Science 2015).

Similarly, another study demonstrated that the same mitochondrial uncoupler (CRMP) increased VCS while EGP decreased in nonhuman primates (Goedeke et al. Sci. Transl. Med. 2019).

These data demonstrate that, while fluxes are back-calculated from EGP with PINTA, the method is fully capable of detecting differences in oxidative fluxes without, or in the opposite direction of, changes in EGP. We very respectfully submit that we are not aware of what a more “involved” approach for metabolic flux analysis would entail, and that after the 8 prior publications listed in response to the previous point, we are not trying to validate PINTA in the current manuscript.

Reviewer #3 (Public Review):

This manuscript addresses a fundamental aspect of mammalian biology referred to as scaling, in which metabolic processes calibrate to the size of the organism. Longstanding observations related to scaling have been established based on rates of oxygen consumption. This manuscript extends these observations to gene expression and metabolic fluxes in order to discover the metabolic pathways that scale with body mass. The analyses are focused on the liver, which is the metabolic hub of the organism. Gene expression levels gleaned from available databases for organisms of varied sizes are analyzed and queried for scaling based on body mass. This analysis reveals that scaling is mainly a characteristic of metabolic genes. These data inform metabolic flux studies in cultured cells, liver slices and whole organisms. These studies demonstrate that scaling of metabolic fluxes occurs, but not out of the context of the whole organism or intact liver (in the form of liver slices). Scaling of metabolic fluxes is not observed in cultured hepatocytes. Overall, this is an interesting line of inquiry. The data are largely correlative in nature but add important texture to traditional characterization of oxygen consumption rates. The application of flux studies is a particular strength because these reflect the true metabolic processes. Enthusiasm was tempered by certain claims that extend beyond data (e.g., the title that suggests that metabolic scaling applies to tissues other than the liver, which was studied), as well as low numbers of biological replicates in some experiments, studies conducted in a single-gender and a writing style that includes excessive technical jargon.

We thank the reviewer for their time spent evaluating the paper, and for their very helpful comments. We agree that “the application of flux studies is a particular strength because these reflect the true metabolic processes.” We agree that the study was focused on liver, although the previous iteration did include a small amount of white adipose tissue flux data, and have edited the manuscript to make clear that this is a liver-focused manuscript. We have now added specific numbers to each figure legend, and have also added in vivo flux measurements in female rats and mice. Additionally, the manuscript has been edited extensively. We have further detailed these modifications in our point-by-point responses to the reviewer.

Author Response

Reviewer #1 (Public Review):

Bornstein and colleagues address an important question regarding the molecular makeup of the different cellular compartments contributing to the muscle spindle. While work focusing on single components of the spindle in isolation - proprioceptors, gamma-motor neurons, and intrafusal muscle fibres - have been recently published, a comprehensive analysis of the transcriptome and proteome of the spindle was missing and it fills an important gap considering how local translation and protein synthesis can affect the development and function of such a specialised organ.

The authors combine bulk transcriptome and proteome analysis and identify new markers for neuronal, intrafusal, and capsule compartments that are validated in vivo and are shown to be useful for studying aspects of spindle differentiation during development. The methodology is sound and the conclusions in line with the results.

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

I feel a bit more analysis regarding the specificity and developmental expression profiles of the identified markers would be a great addition. In particular:

• Are any of the proprioceptive sensory neurons markers specific for fibres innervating the muscle spindles or also found in Golgi tendon organs?

We thank the reviewer for the important question, following which we performed two additional analyses. First, in order to study the specificity of spindle afferent genes we identified, we examined the overlap between our list of 260 potential proprioceptive neuron genes and markers for the three proprioceptive neurons subtypes (Ia, II and Ib) identified by Wu and colleagues (Wu et al. 2021). As shown in the newly added Figure 1- figure supplement 2F, while we found many genes that are common to all subtypes, 69 genes exclusively overlapped with subtype markers (22 genes with type Ia neurons, 45 genes with type II neurons and 2 genes with both; lists are shown in Supplementary File 4). These results suggest that the 69 genes are expressed by muscle spindle afferents and not by GTO afferents.

Second, to study the specificity of our validated markers, we examined the expression of ATP1a3, VCAN and GLTU1, marking proprioception neurons, extracellular matrix and outer capsule, respectively, in GTOs. Results showed that all three markers were also detected in the different tissues composing the GTOs (newly added Figure 3 – figure supplement 3, below). As ATP1a3 is not in the 69 unique marker list, this analysis verified that it is expressed by all proprioceptive neurons. The expression of both VCAN and GLUT1 in GTO capsules highlights the similarity between the capsules of the two proprioceptors.

• On the same line are any of the gamma motor neurons markers found also in alpha?

We thank the reviewer for raising this issue. Following the reviewer’s question, we conducted a detailed analysis of the expression of potential γ motor neuron genes. To this end, we first generated a list of α-motor neurons genes in our data by performing ranked GSEA using published expression profiles of these neurons (Blum et al., 2021). Then, we compared between the three lists of neuronal genes, i.e. γ motor neurons, α motor neurons and proprioceptive neurons (newly added Figure 1 – figure supplement 2G), and found an overlap between the three lists. Nonetheless, we also identified 40 spindle genes that are specific to γ motor neuron (Figure 1 – figure supplement 2G and Supplementary File 4) and, therefore, are potential markers for these neurons.

• How early expression of ATP1A3 is found in neurons at the spindle or fibres starting to innervating the muscle? A couple of late embryonic timepoints would be great.

We thank the reviewer for this suggestion. We performed late embryonic (E15.5-E17.5) staining for ATP1a3, which showed its expression as early as E15.5 (new Figure 4 – figure supplement 1).

• Given that the approach used allows to obtain insights on whether local translation plays a major role into the differentiation of the spindle it would be interesting to assess whether the proprioceptor and gamma motor neuron markers identified are also found in the cell body or exclusively at the spindle.

The reviewer raises an interesting question about local translation of the neuronal genes. Going through the literature, several lines of evidence indicate that the genes expressed at the neuronal end are also expressed in the neuron soma. In a study on retinal ganglion cell translatome, Holt and colleagues found that the axonal translatome is a subset of the significantly larger somal translatome (Shigeoka et al., Cell, 2016). Similarly, a study by Shuman and colleagues that compared the translatome of neuronal cell bodies, dendrites, and axons of rat hippocampal neurons showed that many common genes are translated, albeit at different levels (Glock et al., PNAS, 2021). Finally, following the reviewer’s suggestion, we studied the expression of ATP1a3 in the DRG, and found it to be expressed there as well (Figure L1). Thus, we predict that the markers we found in the neurons ends are likely also expressed in the soma. While this issue is very interesting, we believe that further validation of our assumption exceeds the scope of this study.

Figure L1. ATP1a3 expression in the DRG. Confocal images of DRG sections from adult PValb-Cre;tdTomato mice stained for ATP1a3 (magenta). Scale bars represent 50 μm.

Altogether, this is a novel and important work that will benefit scientists studying the neuromuscular and musculoskeletal systems by pushing the field toward an holistic understanding of the muscle spindle. These datasets in combination with the previous ones can be used to develop new genetic and viral strategies to study muscle spindle development and function in healthy and pathological states by analysing the roles and relative contributions of different components of this fascinating and still mysterious organ.

We thank again the reviewer for highlighting the importance of our study.

Reviewer #2 (Public Review):

The data presented are of high quality. Through complementary experiments involving the isolation of masseter muscle spindles, the authors perform RNA-seq and proteomic analysis, and identify genes and proteins that are differentially expressed in the muscle spindle versus the adjacent muscle fiber, and proteins that accumulate specifically in capsule cells and nerve endings. These data, while essentially descriptive, provide important information about the developmental framework of the sensory apparatus present in each muscle that accounts for its tension/contraction state. The data presented thus allow for a better characterization of muscle spindles and provide the community with a set of new markers for better identification of these structures. Analysis of the expression pattern of the Tomato reporter in transgenic animals under the control of Piezo2-CRE, Gli1-CRE and Thy1-YFP reporter reinforces the findings and the specificity of the expression pattern of the specific genes and proteins identified by the multi-omics approach and further validated by immunohistochemistry.

We thank the reviewer for the positive and encouraging feedback.

Author Response

Reviewer #1 (Public Review):

In this manuscript, Marmor and colleagues reanalyze a previously published dataset of chronic widefield Ca2+ imaging from the dorsal cortex of mice as they learn a go/no-go somatosensory discrimination task. Comparing hit trials that have a distinct history (i.e. are preceded by distinct trial types), the authors find that hit trials preceded by correct rejections of the nontarget stimulus are associated with larger subsequent neural responses than trials precede by other hits, across the cortex. The authors analyze the time course over which this effect emerges in the barrel cortex (BC) and the rostrolateral visual area (RL), and find that its magnitude increases as the animals become expert task performers. Although the findings are potentially interesting, I, unfortunately, believe that there are important methodological concerns that could put them into question. I also disagree with the rationale that singles out BC and RL as being especially important for the emergence of trial history effects on neural responses during decision-making. I detail these points below .

1) The authors did not perform correction for hemodynamic contamination of GCaMP fluorescence. In widefield imaging, blood vessels divisively decrease neural signals because they absorb green-wavelength photons, which could lead to crucial confounds in the interpretation of the main results because of neurovascular coupling, which lags neural activity by seconds. For example, if a reward response from the previous trial is associated with a lagged hemodynamic contamination that artificially decreases the signal in the following trial, one could get artificially higher activity in trials that were not preceded by a reward (i.e. CR), which is what the authors observed. Ideally, the experiments would be repeated with proper hemodynamic correction, but at the very least the authors should try to address this with control analyses.

Done. We basically redone the experiment with proper hemodynamic correction and maintained trial history results. Please see point 1 above for more details (Figures S4 and S5). In addition to hemodynamic controls, we also present novel two-photon single cell data with similar results in Figure S6. We also added a dedicated section for this in the Methods section (pg. 12).

For example, what is the time course of reward-related responses in BC and elsewhere?

In general, and specifically in BC, reward related responses return to baseline up to 5 seconds after the start of the reward period and at least 5 seconds before the stimulus presentation of the next trial. In the novel experiments we even extended the baseline period by an additional 2 seconds just in case. Trial history information was still present with an extended inter-trial interval.

The text now reads (pg. 4): "We further report that responses during the reward period in cortex and specifically in BC went back to baseline 4-5 seconds after the start of the reward period and 6-8 seconds before the presentation of the next stimulus (total inter-trial interval ranged between 10-12 seconds)."

Do hemodynamics artifacts have a trial-by-trial correlation with the subsequent trial history effect?

We have now done the proper hemodynamic control (Figure 2) and we did not find a strong effect of hemodynamic responses on trial history information.

What is the learning time course of reward responses?

Responses during the reward period as a function of learning were not significantly modulated. We further show the whole learning profile for BC response during the reward period in Author response image 1.

Author response image 1.

Response in BC averaged during the reward period (2-4 sec after texture stop) as a function of learning for each mouse separately.

The text now reads (pg. 4): "In addition, responses in BC during the reward period were not consistently modulated as a function of learning (p>0.05; Wilcoxon signed-rank test between naïve and expert, BC response averaged during the reward period, 2-4 seconds after stimulus onset; n=7 mice). Taken together, we find that direct responses from the reward period do not effect history-related responses during the next trial."

Note that I don't believe the FA-Hit condition analysis that the authors have already presented provides adequate control, as punishment responses are also pervasive in the cortex and therefore suffer from the same interpretational caveat. Unfortunately, I believe this is a serious methodological issue given the above. However, I will proceed to take the reported results at face value .

We hope that our additional control analysis regarding the hemodynamic controls are satisfactory.

2) The statistics used to assess the effect of trial history over learning are inadequate (e.g., Fig 2b). The existence of a significant effect in one condition (e.g., CR-Hit vs. Hit-Hit in expert) but not in another (e.g., same comparison in naive) does not imply that these two conditions are different. This needs to be tested directly. Moreover, the present analysis does not account for the fact that measures across learning stages are taken from the same animals. Thus, the appropriate analysis for these cases would be to first use a two-way ANOVA with repeated measures with factors of trial history and learning stage (or equivalent non-parametric test) and then derive conclusions based on post hoc pairwise tests, corrected for multiple comparisons .

Done. We performed 2 way ANOVA as suggested and found significant history and learning effects along with a significant interaction effect for BC.

The text now reads (pg. 4): "This difference was significant during the stim period in learning and expert phases across mice (Fig. 2b; 2-way ANOVA with repeated measures; DF (1-6) F=51 p<0.001, DF (2-12) F=18 p<0.001, DF(2-12) F=5 p<0.05 for trial history, learning and the interaction between trial history and learning; Post hoc Tukey analysis p<0.05 for trial history in learning and expert phases; p>0.05 in the naïve phase)."

3) I am not convinced that BC and RL are especially important for trial-history-dependent effects. Figures 4 and 5 suggest that this modulation is present across the cortex, and in fact, the difference between CR-Hit and Hit-Hit in some learning stages appears stronger in other areas. BC and RL do have the highest absolute activity during the epochs in Figs 4 and 5, but I would argue that this is likely due to other aspects of the task (e.g., touch) and therefore is not necessarily relevant to the issue of trial history .

Done. First, we would like to point out that RL during the pre period displays the largest difference between the CR-Hit and Hit-Hit conditions (Fig. 5c bottom). Second, we now show difference maps (i.e., activity in CR-Hit minus Hit-Hit) which clearly show a positive activity patch in BC during the stim period for 5 out of the 7 mice (Fig. S10a). Example maps also highlight RL during the pre period (Fig. S10b). We note that activity patches somewhat spread over to other areas and also slightly vary across mice. This is why the grand average may slightly average out trial history information. Taken together, we strongly feel that during the pre period, trial history information emerges in RL (and adjacent posterior association areas) which shift towards BC during the stim period

Nevertheless, we agree with the reviewer that other areas (that do not necessarily display high activity) may encode trial history information and we now clearly report this in the text (pg. 5): "We note that other areas, e.g., different association areas, also encoded historydependent information especially during learning and expert phases. In addition, we present activity difference maps between CR-Hit and Hit-Hit conditions during the stim period (Fig. S10a). These maps clearly show the highest trial history information (i.e., difference in activity) in BC. Taken together, these results indicate that BC encodes history-dependent information that emerges during the stim period and just after learning. "

And also in (pg. 6): " In addition, we present activity difference maps between CR-Hit and HitHit conditions during the pre period (Fig. S10b). These maps localize trial history information to RL which also spreads to other adjacent association areas. Moreover, activity patches slightly vary across the different mice which may affect the grand average (averaged across mice) of each area."

4) Because of similar arguments to the above, and because this was not directly assessed, I do not believe the conclusion that history information emerges in RL and is transferred to BC is warranted. For instance, there is no direct comparison between areas, but inspection of the ROC plots in Fig 6b suggests that history information emerges concomitantly across cortical areas. I suggest directly comparing the time course between these and other areas

Done. We now add example history AUC maps and quantify history AUC for all 25 areas during the pre and stim periods. During the pre period (Fig. 6), AUC values are concentrated around the RL (and other PPC areas), whereas during the stim periods AUC values shift to BC. Again, due to the inter-mouse variability, these differences are slightly averaged out which also makes it tough to have strong statistical test (with only 7 mice).

The text now reads (pg. 7): "We next calculated the history AUC for each pixel during either the pre or stim period. The history AUC maps during the pre period display AUC values around the RL areas (Fig. 6f). In contrast, the history AUC maps during the stim period display AUC values mostly in BC (Fig. 6g). Quantified across 25 areas and averaged across mice, RL displays the highest history AUC during the pre period, whereas BC displays the highest history AUC values during the stim period (Fig. 6h). We note that other cortical areas such as other association areas also display high history AUC values. Taken together, we find that trial history emerges in RL before the texture arrives and then shifts to BC during stimulus presentation. "

5) How much is task performance itself modulated by trial history? How does this change over the course of learning? These behavioral analyses would greatly help interpret the neural findings and how this trial history might be used behaviorally .

Done, we have now calculated the dprime for Hit-Hit and CR-Hit trials separately. We find no significant differences between conditions both within and across mice (see Fig. S2 below).

The text now reads pg. 3): "We note that learning curves that are calculated separately for each pair (i.e., either a preceding Hit or CR trial) were not significantly different (Fig. S2)."

Reviewer #2 (Public Review):

Marmor et al. mine a previously published dataset to examine whether recent reward/stimulus history influences responses in sensory (and other) cortices. Bulk L2/3 calcium activity is imaged across all of the dorsal cortex in transgenic mice trained to discriminate between two textures in a go/no-go behavior. The authors primarily focus on comparing responses to a specific stimulus given that the preceding trial was or was not rewarded. There are clear differences in activity during stimulus presentation in the barrel cortex along with other areas, as well as differences even before the second stimulus is presented. These differences only emerge after task learning. The data are of high quality and the paper is clear and easy to follow. My only major criticism is that I am not completely convinced that the observed difference in response is not due to differences in movement by the animal on the two trial types. That said, the demonstration of differences in sensory cortices is relatively novel, as most of the existing literature on trial history effect demonstrates such differences only in higher-order areas .

Major :

1a) The claim that body movements do not account for the results is in my view the greatest weakness of the paper - if the difference in response simply reflects a difference in movement, perhaps due to "excitement" in anticipation of reward after not receiving one on CR-H vs. HH trials, then this should show up in movement analysis. The authors do a little bit of this, but to me, more is needed .  

Done. We have now extensively and carefully analyzed body and whisker movements for CRHit and Hit-Hit conditions. First, In the figure below we decomposed body movements into 22 different body parts using DeepLabCut. In short, we find no significant difference between CRHit and Hit-Hit conditions in each body part separately (Fig. S7 below). This was true for the naïve, learning and expert phases. Please see additional analyses in the points below.

This is now reported in the text (pg. 4): “In addition, we performed a more detailed body and whisker analysis, e.g., decomposing the movement to different body parts and obtaining single whisker dynamics. These analyses did not find significant differences in movement parameters between CR-Hit and Hit-Hit conditions (Fig. s7 and s8).”

First, given the small sample size and use of non-parametric tests, you will only get p<.05 if at least 6 of the 7 mice perform in the same way. So getting p>.05 is not surprising even if there is an underlying effect. This makes it especially important to do analyses that are likely to reveal any differences; using whisker angle and overall body movement, which is poorly explained, is in my opinion insufficient. An alternative approach would be to compare movements within animals; small as the dataset is, it is feasible to do an animal-by-animal analysis, and then one could leverage the large trial count to get much greater statistical power, foregoing summary analyses that pool over only n=7 .

We agree with this point and are have now dramatically improved our statistical analysis.

1) We now perform within mouse statistics for responses in BC during naïve, learning and expert (see Fig. S4 below). In short, we find statistical significance for 7 out of 7 mice during the expert phase, 6 out of 7 mice in the learning phase and 0 out of 7 in the naive phase. For RL during the pre period we find significant difference in 5 out of 7 expert mice.

This is now reported in the text (pg. 4): "In addition, a statistical comparison between CR-Hit and Hit-Hit responses within each mouse separately maintained significance for expert (7/7 mice Mann-Whitney U-test p<0.05) and learning (6/7 mice) but not for naïve (0/7 mice. Fig. S3)."

And also in (pg. 5): "In addition, a statistical comparison between CR-Hit and Hit-Hit responses in RL within each mouse separately maintained significance for expert (5/7 mice; MannWhitney U-test p<0.05)."

2) We would like to point out that we have now added 3 additional mice (with hemodynamics control) and performed within mouse statistics in BC and RL (Fig. S5), adding to our initial observations.

3) In terms of body movements, we now performed within mice statistics and compared body movements between CR-Hit and Hit-Hit conditions. In general, most mice did not show a significant difference in body movements or whisker envelope.

This is now reported in the text (pg. 4): "A within mouse statistical comparison between body or whisker parameters in CR-Hit and Hit-Hit maintained a non-significant difference in expert (1/7 mice displayed a significant difference; Mann-Whitney U-test p>0.05), learning (2/7 mice) and naïve (0/7 mice)."

And also in (pg. 4): "Body movements and whisker parameters did not significantly differ between CR-Hit and Hit-Hit conditions during the pre-period (Similar to the stim period. Across and within mice. P>0.05; Mann-Whitney U-test)."

In summary, we have now substantially improved our statistical analysis and further decomposed the body movements, maintaining the trial history results.

The authors only consider a simple parametrization of movement (correlation across successive frames), and given the high variability in movement across animals, it is likely that different mice adopt different movements during the task, perhaps altering movement in specific ways. Aggregating movement across different body parts after an analysis where body parts are treated separately seems like an odd choice - perhaps it is fine, but again, supporting evidence for this is needed. As it stands, it is not clear if real differences were averaged out by combining all body parts, or what averaging actually entails .

Please see the above point where we decomposed body movements (Fig. S7 and Methods section in Pg. 14).

If at all possible, I would recommend examining curvature and not just the whisker angle, since the angle being the same is not too surprising given that the stimulus is in the same place. If the animal is pressing more vigorously on CR-H trials, this should result in larger curvature changes .

Done. We now decompose whisker dynamics (i.e., curvature) using DeepLabCut (Fig. S8 see below). In general, we find no significant differences in whisker parameters between Hit-Hit and CR-Hit conditions.

This is now reported in the text (pg. 4): "In addition, we performed a more detailed body and whisker analysis, e.g., decomposing the movement to different body parts. This analysis did not find significant differences between CR-Hit and Hit-Hit conditions (Fig. S7 and S8)."

Finally, the authors presumably have access to lick data. Are reaction times shorter on CR-H trials? Is lick count or lick frequency shorter?

Done. We now calculated lick reaction time and lick rate and find a significant difference for the lick reaction time but not in lick rate. We show a figure below for the reviewer and report this in the text

The text now reads (pg. 3): "In addition, the lick reaction time (but not the lick rate) between Hit-Hit and CR-Hit were significantly different (p<0.05; Wilcoxon signed-rank test) ,maybe indicating a more considered response after a previous stop signal."

If movement differs across trial types, it is entirely plausible that at least barrel cortex activity differences reflect differences in sensory input due to differences in whisker position/posture/etc. This would mitigate the novelty of the present results .

As detailed above, have now meticulously analyzed the whisker parameter differences between both conditions and did not find any significant differences.

1b) Given the importance of this control to the story, both whisker and body movement tracking frames should be explicitly shown either in the primary paper or as a supplement. Moreover, in the methods, please elaborate on how both whisker and body tracking were performed .

Done. Please see Figs. S7 and S8 for tracking frames. This is now detailed in the above points and also the revised relevant methods section

2) .Did streak length impact the response? For instance, in Fig. 1f "Learning", there is a 6-trial "no-go" streak; if the data are there, it would be useful to plot CR-H responses as a function of preceding unrewarded trials.

Done. We have now calculated response in CR-Hit as a function of the number of preceding CRs. In general, we obtain inconsistent results across mice that may be due to the small number of trials that have more than one preceding CR. Nevertheless, some mice have a trend, sometimes significant, in which CR-Hit responses are higher for longer CR preceding streaks. This is especially true during the learning phase. We have decided not to include this in the manuscript and present this figure only to the reviewer.

Author response:

Reviewer #1 (Public Review):

This is an important and very well conducted study providing novel evidence on the role of zinc homeostasis for the control of infection with the intracellular bacterium S. typhimurium also disentangling the underlying mechanisms and providing clear evidence on the importance of spatio-temporal distribution of (free) zinc within the cell.

We thank the reviewer for the positive comments.

1) It would be important to provide more information on the genotype of mice.

As suggested by the reviewer, we have added the detailed genotype of Slc30a1flagEGFP/+ and Slc30a1fl/flLysMCre mice to the revised supplementary Figure supplement 10.

2) It is rather unlikely that C57Bl6 mice survive up to two weeks after i.p. injection of 1x10E5 bacteria.

According to the reviewer comment, we have tested survival rate using a group of our experimental animals and C57BL/6 wild type.

The Salmonella stain is a gift from our friend, Professor Ge Bao-xue. We have sent this stain for genetic characterisation which we found 100% identity to Salmonella enterica Typhimurium with many strains originated from poultry. One of them is Salmonella enterica subsp. enterica serovar Typhimurium strain MeganVac1 (Accession: CP112994.1), a live attenuated stain. We hope that this would support the relationship between the high infectious dose and mice survive.

Author response image 1.

(A) Survival rate of Slc30a1fl/fl and Slc30a1fl/flLysMCre (n = 14-15/group) and (B) Survival rate of C57BL/6 wild type (n = 8) after Salmonella infection for two weeks. (C) A fulllength sequence (1,478 bases) of 16S rDNA genes sequences of Salmonella stain and (D) the sequencing electropherogram.

3) To be sure that macrophages Slc30A1 fl/fl LysMcre mice really have an impaired clearance of bacteria it would be important to rule out an effect of Slc30A1 deletion of bacterial phagocytosis and containment (f.e. evaluation of bacterial numbers after 30 min of infection).

As the reviewer advised, we have repeated the experiment and measured the bacterial numbers after 30 min of infection (dashed line in A). The results show that there is no statistical difference in the bacterial numbers after 30 min between Slc30a1fl/flLysMCre and Slc30a1fl/fl BMDMs. Therefore, the reduction of bacterial numbers after 24 hours occurs due to the impairment of intracellular pathogen-killing capacity as the reviewer pointed out.

Author respnse image 2.

(A) Time course of the intracellular pathogen-killing capacity of Salmonellainfected Slc30a1fl/flLysMCre and Slc30a1fl/fl BMDMs measured in colony-forming units per ml (n = 5). (B) Fold change in Salmonella survival (CFU/mL) at different time points from A. (C) Representative images of Salmonella colonies on solid agar medium at 24 hours. Data are represented as mean ± SEM. P values were determined using 2-tailed unpaired Student’s t-test. P<0.05, *P<0.01, and ns, not significant.

4) Does the addition of zinc to macrophages negatively affect iNOS transcription as previously observed for the divalent metal iron and is a similar mechanism also employed (CEBPß/NF-IL6 modulation) (Dlaska M et al. J Immunol 1999)?

The reviewer has raised an important point here since free zinc also play a role in multiple levels of cellular signaling components (Kembe et al., 2015). Dlaska and colleague reported that NF-IL6, a protein responsible for iNOS transcription is negatively regulated by iron perturbation under IFNg/LPS stimulation in macrophages (Dlaska and Weiss, 1999). As the reviewer suggested, our results showed that zinc supplementation decreases the iNOS expression in macrophages after Salmonella infection, suggesting that free zinc might play a role in iNOS regulation.

However, in Slc30a1fl/flLysMCre macrophages, despite increase intracellular free zinc, lacking Slc30a1 also induces Mt1, a zinc reservoir which might negatively affect NO production (Schwarz et al., 1995) or alternatively inhibits iNOS through NF-kB pathway (Cong et al., 2016) as reported by previous studies. Therefore, we couldn’t rule out the possibility that defects in Salmonella clearance due to iNOS/NO inhibition may be caused by a complex combination of excess free zinc and overexpression of the zinc reservoir. To prove this hypothesis, further studies using the specific target, for example Mtfl/fliNOSfl/flLysMCre model might be needed to investigate the precision mechanism.

Author response image 3.

RT-qPCR analysis of mRNA encoding Nos2 in BMDMs after infected with Salmonella and Salmonella plus ZnSO4 (20 μM) for 4 h.

Reference:

Dlaska M, Weiss G. 1999. Central role of transcription factor NF-IL6 for cytokine and ironmediated regulation of murine inducible nitric oxide synthase expression. The Journal of Immunology. 162:6171-6177, PMID: 10229861

Kambe T, Tsuji T, Hashimoto A, Itsumura N. 2015. The physiological, biochemical, and molecular roles of zinc transporters in zinc homeostasis and metabolism. Physiological Reviews. 95:749-784. https://doi: 10.1152/physrev.00035.2014, PMID: 26084690

Schwarz MA, Lazo JS, Yalowich JC, Allen WP, Whitmore M, Bergonia HA, Tzeng E, Billiar TR, Robbins PD, Lancaster JR Jr, et al. 1995. Metallothionein protects against the cytotoxic and DNA-damaging effects of nitric oxide. Proceedings of the National Academy of Sciences of the United States of America. 92: 4452-4456. https://doi: 10.1073/pnas.92.10.4452, PMID: 7538671

Cong W, Niu C, Lv L, Ni M, Ruan D, Chi L, Wang Y, Yu Q, Zhan K, Xuan Y, Wang Y, Tan Y, Wei T, Cai L, Jin L. 2016. Metallothionein prevents age-associated cardiomyopathy via inhibiting NF-κB pathway activation and associated nitrative damage to 2-OGD. Antioxidants & Redox Signaling. 25: 936-952. https://doi: 10.1089/ars.2016.6648, PMID: 27477335

5) How does Zinc or TPEN supplementation to bacteria in LB medium affect the log growth of Salmonella?

We found that zinc supplementation at both low (20 µM) and high (640 µM) concentrations negatively effects Salmonella growth, especially during log phase and stationary phase in the broth culture medium, but not TPEN (20 µM) supplementation. These indicates that high zinc conditions occur at cellular levels such as within phagosomes (Botella et al., 2011) can limit bacterial growth.

Author response image 4.

Growth curve (optical density, OD 600 nm) of Salmonella in LB medium at different concentrations of ZnSO4 and/or TPEN. Bar graph indicating Salmonella growth at specific time points. Each value was expressed as mean of triplicates for each testing and data were determined using 2-tailed unpaired Student’s t-test. P<0.05, P<0.01, **P<0.001 and ns, not significant.

Reference:

Botella H, Peyron P, Levillain F, Poincloux R, Poquet Y, Brandli I, Wang C, Tailleux L, Tilleul S, Charrière GM, Waddell SJ, Foti M, Lugo-Villarino G, Gao Q, Maridonneau-Parini I, Butcher PD, Castagnoli PR, Gicquel B, de Chastellier C, Neyrolles O. 2011. Mycobacterial p(1)-type ATPases mediate resistance to zinc poisoning in human macrophages. Cell Host Microbe. 10:248-59. https://doi: 10.1016/j.chom.2011.08.006, PMID: 21925112

Reviewer #2 (Public Review):

This paper explores the importance of zinc metabolism in host defense against the intracellular pathogen Salmonella Typhimurium. Using conditional mice with a deletion of the Slc30a1 zinc exporter, the authors show a critical role for zinc homeostasis in the pathogenesis of Salmonella. Specifically, mice deficient in Slc30a1 gene in LysM+ myeloid cells are hypersusceptible to Salmonella infection, and their macrophages show alter phenotypes in response to Salmonella. The study adds important new information on the role metal homeostasis plays in microbe host interactions. Despite the strengths, the manuscript has some weaknesses. The authors conclude that lack of slc30a1 in macrophages impairs nos2-dependent anti-Salmonella activity. However, this idea is not tested experimentally. In addition, the research presented on Mt1 is preliminary. The text related to Figure 7 could be deleted without affecting the overall impact of the findings.

We thank the reviewer for his/her positive comments and constructive suggestions.

Reviewer #3 (Public Review):

Na-Phatthalung et al observed that transcripts of the zinc transporter Slc30a1 was upregulated in Salmonella-infected murine macrophages and in human primary macrophages therefore they sought to determine if, and how, Slc30a1 could contribute to the control of bacterial pathogens. Using a reporter mouse the authors show that Slc30a1 expression increases in a subset of peritoneal and splenic macrophages of Salmonella-infected animals. Specific deletion of Slc30a1 in LysM+ cells resulted in a significantly higher susceptibility of mice to Salmonella infection which, counter to the authors conclusions, is not explained by the small differences in the bacterial burden observed in vivo and in vitro. Although loss of Slc30a1 resulted in reduced iNOS levels in activated macrophages, the study lacks experiments that mechanistically link loss of NO-mediated bactericidal activity to Salmonella survival in Slc30a1 deficient cells. The additional deletion of Mt1, another zinc binding protein, resulted in even lower nitrite levels of activated macrophages but only modest effects on Salmonella survival. By combining genetic approaches with molecular techniques that measure variables in macrophage activation and the labile zinc pool, Na-Phattalung et al successfully demonstrate that Slc30a1 and metallothionein 1 regulate zinc homeostasis in order to modulate effective immune responses to Salmonella infection. The authors have done a lot of work and the information that Slc30a1 expression in macrophages contributes to control of Salmonella infection in mice is a new finding that will be of interest to the field. Whether the mechanism by which SLC30A1 controls bacterial replication and/or lethality of infection involves nitric oxide production by macrophages remains to be shown.

We very much appreciate the reviewer’s detailed evaluation and suggestions. The manuscript has been revised thoroughly according to the reviewer’s advice.

Author Response

Reviewer #1 (Public Review):

This work focuses on the mechanisms that underlie a previous observation by the authors that the type VI secretion system (T6SS) of a Pseudomonas chlororaphis (Pchl) strain can induce sporulation in Bacillus subtilis (Bsub). The authors bioinformatically characterize the T6SS system in Pchl and identify all the core components of the T6SS, as well as 8 putative effectors and their domain structures. They then show that the Pchl T6SS, and in particular its effector Tse1, is necessary to induce sporulation in Bsub. They demonstrate that Tse1 has peptidoglycan hydrolase activity and causes cell wall and cell membrane defects in Bsub. Finally, the authors also study the signaling pathway in Bsub that leads to the induction of sporulation, and their data suggest that cell wall damage may lead to the degradation of the anti-sigma factor RsiW, leading to activation of the extracellular sigma factor σW that causes increased levels of ppGpp. Sensing of high ppGpp levels by the kinases KinA and KinB may lead to phosphorylation of Spo0F, and induction of the sporulation cascade.

The findings add to the field's understanding of how competitive bacterial interactions work mechanistically and provide a detailed example of how bacteria may antagonize their neighbors, how this antagonism may be sensed, and the resulting defensive measures initiated.

While several of the conclusions of this paper are supported by the data, additional controls would bolster some aspects of the data, and some of the final interpretations are not substantiated by the current data.

• The Bsub signaling pathway that is proposed is intricate and extensive as shown in Fig 5A. However, the data supporting that is very sparse:

a) The authors show no data showing that the proteases PrsW and/or RasP, or the extracellular sigma factor σW are necessary, or that the cleavage of RsiW is needed, for induction of sporulation - this could presumably be tested using mutants of those genes.

It has been previously demonstrated that the proteases PrsW and/or RasP cleave RsiW under certain conditions such as alkaline-shock (Heinrich et al., 2009). In first place, PrsW cleaves RsiW and the resulting cleaved-RsiW serves as substrate to RasP. In the previous version of the manuscript, we already demonstrated that treatment with Tse1 causes damage to PG and delocalization of RsiW, however as the reviewer comments we did not show the participation of any of these proteases in the proposed signaling pathway. We have now generated single mutants in rsiW and prsW and they have been treated with Tse1. We have observed no variation in the levels of sporulation compared to untreated strains (Figure 1) a finding according to their suggested implication in the sporulation signaling pathway activated by Tse1. Positive controls, that is the single mutants grown at 37ºC, were still able to sporulate. This data has been added to Figure 6B in the new version of the manuscript.

As suggested by other reviewers, we have generated a sister plot of this figure showing the raw CFUs in each case. These data are included in Supplementary file 3. This experiment and the related figure have been incorporated into the new version of the manuscript.

Figure 1. A) Quantification of the percentage of sporulated Bsub, rsiW and prsW cells after treatment with purified Tse1 showing that rsiW and prsW single mutants are blind to the presence of Tse1. B) Cell density (CFUs/mL) of total (blue bars) and sporulated population (brown bars) of different Bacillus strains (Bsub, ∆rsiW and ∆prsW) untreated and treated with Tse1. Sporulation at 37ºC is shown as positive control in each strain. Statistical significance was assessed via t-tests. p value < 0.1, p value < 0.001, **p value < 0.0001.

Similarly, they don't demonstrate that the levels of ppGpp increase in the cell upon exposure to Pchl.

We have not been able to measure the levels of ppGpp, however, given that in the same proposed sporulation cascade the levels of different nucleotides are altered (Kriel et al., 2013, Tojo et al., 2013, López and Kolter, 2010), we have alternatively analyzed the levels of ATP using an ATP Determination Kit (Thermo, A22066). We have found that ATP levels increased by 3-fold in Bsub cells treated with Tse1 compared to untreated control cells. Consistently, no increase in ATP levels were observed in rsiW or prsW mutants treated with Tse1. We have incorporated all the raw luminescence data obtained for each sample and treatment in Figure 6-source data 1. This experiment, figures (Figure 6A in the new version of the manuscript) and description in “Materials and Methods” have been added to the new version of the manuscript.

c) There is some data showing that kinA and kinB mutants don't induce sporulation (Fig supplement 7A), but that is lacking the 'no attacker' control that would demonstrate an induction.

We have included in the new version of the manuscript the ‘no attacker’ control sporulation (%). The figure shows that the presence of Pchl strains induces the sporulation of all kinase mutants. This new data has been incorporated in Figure 6-figure supplement 1A in the new version of the manuscript.

d) There is some data showing that RsiW may be cleaved (Fig 5C, D), but that data would benefit from a positive control showing that the lack of YFP foci is seen in a condition where RsiW is known to be cleaved, as well as from a time-course showing that the foci are present prior to the addition of Tse1, and then disappear. As it is shown now, it is possible that the addition of Tse1 just blocks the production of RsiW or its insertion into the membrane (especially given the membrane damage seen). Further, there is no data that the disappearance of the YFP loci requires the proteases PrsW and /or RasP - such data would also support the idea that the disappearance is due to cleavage of RsiW.

Thank you for your useful suggestion. It is important to consider that we have not seen repression of the expression of genes that encode any of the two proteases on cells treated with Tse1 in our transcriptomics analysis. However, we agree that additional experiments would enhance the significance of our findings. We have repeated the whole experiment including a positive control to demonstrate that YFP foci disappears in a condition in which RsiW is known to be degraded by PrsW and RasP. Bacillus cells have been incubated in medium at pH 10 which provokes an alkaline shock that triggers RsiW cleavage (Asai, 2017; Heinrich et al., 2009). As shown in Fiugre 6D under this condition we also observed disappearance of YFP foci . We have also provided extra images with quantification of average signal from YFP-foci in Figure 6-figure supplement 2 .

• The entire manuscript suggests that T6SS is solely responsible for the induction of sporulation. While T6SS does appear to play a major part in explaining the sporulation induction seen, in the absence of 'no attacker' controls for Fig. 2A, it is impossible to see this. From the data shown in Fig. 2C, and figure supplement 2A, the 'no attacker' sporulation rate seems to be ~20%, while the rate is ~40% with Pchl strains lacking T6SS, suggesting that an additional factor may be playing a role.

This must be a misunderstanding of the message of this manuscript. The conceptual fundament of this study was settled in our previous manuscript (Molina-Santiago et al., 2019). We demonstrated that B. subtilis sporulated in the presence of P. chlororaphis. Interestingly, the overgrowth of P. chlororaphis over B. subtilis colony did not eliminate cells of B. subtilis, given that most of them were sporulated. The data we obtained strongly suggested that a functional T6SS was involved in the cellular response of Bacillus in the close cell to cell contact. In this new manuscript, we have explored this idea, and found that indeed, the T6SS of P. chlororaphis mobilized at least one effector, Tse1, which is able to trigger sporulation in Bacillus. Thus we did not conclude, and neither have done in this new study, that T6SS is the only factor expressed by P. chlororaphis responsible for sporulation activation in Bacillus. We have accordingly rephrased some sentences of the manuscript to clarify the proposed implication of T6SS in B. subtilis sporulation.

In addition, as mentioned above, we have included data of sporulation percentages in the absence of an attacker to better compare the induction of sporulation observed in the presence of the different Pchl strains and in the presence of Tse1.

Reviewer #2 (Public Review):

In a previous study, the authors showed that cell-cell contact with Pseudomonas chlororaphis induces sporulation in Bacillus subtilis. Here, the authors build on this finding and elucidate the mechanism behind this observation. They describe the enzymatic activity of a protein (Tse1) secreted by the type VI secretion system (T6SS) of P. chlororaphis (Pch), which partially degrades the peptidoglycan (PG) of targeted B. subtilis cells and triggers a signal cascade culminating in sporulation.

Most of the key conclusions of this paper (Tse1 being secreted by the T6SS and inducing sporulation in targeted cells) are well supported by the data. One conclusion (sporulation response being an anti-T6SS "defense" strategy) is not well supported by the data and should be removed or rephrased.

The authors elucidate the enzymatic activity of Tse1, a T6SS effector protein, in a genus (Pseudomonas) of great interest to microbiologists, and to researchers studying the T6SS specifically. They also carefully dissect the cellular response (signal cascade and sporulation) of an important model organism (B. subtilis; Bsub) specifically to exposure to Tse1. The results describing this cellular response contribute substantially to our understanding of how T6SS effector proteins interact with cells of Gram-positive species.

My only major concerns regard the interpretation of these results as sporulation being an adaptive and/or specific response to attacks by the T6SS. I outline my reasoning below.

• Interpretation of sporulation as a "defense" mechanism/strategy against the T6SS. In order for a phenotype X to be regarded as a "defense against Y" mechanism, it has to be shown that phenotype X (sporulation in response to Tse1) evolved - at least in part - for the purposes of increasing survival in the presence of Y (T6SS attacker). There are no experiments in this study comparing e.g. a sporulating Bsub with a non-sporulating Bsub, that would allow testing if sporulation increases survival. The experiments carefully describe the cellular response to Tse1, but no inference can be made with regards to this being adaptive for Bsub, or if it helps the cells survive against T6SS attacks, etc. A more parsimonious explanation would be that Tse1 happens to target the PG and causes envelope stress, triggering sporulation. So, it would be a general stress response that also happens to be triggered by T6SS. Now, some general (cell envelope) stress responses are known to be very effective at protecting against the T6SS. But in those instances, a beneficial effect for survival in the face of T6SS attacks has been shown in dedicated experiments. Purely observing a response to a T6SS effector, as this study does (very well), is not evidence that the response has evolved for the purpose of surviving T6SS attacks. Tucked away in the supplement (and briefly mentioned in the main text) is data on Bsub and Bacillus cereus, showing that i) cell densities of the sporulating Bsub and a sporulating B. cereus strain are not affected by an active T6SS, and ii) cell densities of an asporogenic B. cereus are slightly reduced by an active T6SS. However, the effect sizes of density reduction by the T6SS in the asporogenic B. cereus are minute (20x10^6 vs. ~50x10^6). In typical killing assays against e.g. gram-negative strains, a typical effect size for T6SS killing would be a several order of magnitude reduction in survival of the target strain when exposed to a T6SS attacker. Based on this dataset alone (Figure Suppl. 8), I would say that all three Bacillus strains are not experiencing any "fitness-relevant" killing by the T6SS, which is in line with the T6SS often being useless against gram-positives when it comes to killing. Hence, no claims about fitness benefits of sporulation in response to a T6SS attack, or this being a "defense mechanism/strategy" should be made in the manuscript.

Thanks for this interesting introductory and specific comments. We agree with the reviewer and have rephrased some sentences of the manuscript. Sporulation is not an adaptive or specific response of Bacillus to T6SS, indeed and as stated by reviewer 2, sporulation is a general stress response. It might happen that the way the manuscript was written, at some points, gave the wrong impression. In consequence we have rephrased some sentences. Nevertheless, in Figure supplement 8 (in the new version of the manuscript is Figure 6-figure supplement 3) we made a mistake during generation of the Figure. We have again done this experiment and we have generated a new and corrected chart that shows three orders of magnitude reduction in survival of the asporogenic B. cereus strain in competition with Pchl mutant strains compared to Pchl WT strain. These new findings show that the absence of sporulation ability leads to a severe reduction in survival of Bacillus cereus DSM 2302 population in competition with Pchl with an active T6SS compared to the survival in competition with Pchl hcp mutant. In this figure, it is also shown that Bacillus population also decreased in competition with tse1 mutant, demonstrating that Tse1 is responsible for killing Bacillus. However, there is a statistical difference in the survival of Bacillus competing with hcp or tse1 mutants. The increased survival of Bacillus in the interaction with tse1 strain compared to Bacillus-hcp competition, is suggestive of the ability of this strain to deliver additional T6SS-dependent toxins. This observation is in accordance to the data presented in Fig. 2B, which indicated that tse1 mutant has an active T6SS able to kill E. coli.

• Data supporting baseline "no competitor" sporulation rates being no different from those triggered by T6SS mutants is not convincing. For the data shown in Fig. 2A, a key comparison here would be to show baseline Bsub sporulation rates in absence of a competitor. This measurement is shown in Fig supplement 2A, and the value shown there (roughly 22% on average) appears to be much lower than the average T6SS mutant shown in Fig. 2A. The main text states that sporulation rates induced rate by the different T6SS mutants are "statistically" similar to the no-competitor baseline (L206/207). I am not convinced by this, since i) overall sporulation rates (incl of WT Pch) appear to have been lower in the experiment shown in supplement 2A, so a direct comparison between the no-competitor baseline and the data shown in Fig. 2A is not possible; and ii) hcp and tse1 mutants were tested in different experiments throughout the study, and sporulation rates appear to consistently hover around 30-40%, which is higher than the roughly 22% for "no competitor" depicted in Supplement Fig2A. I am focussing on this, because for the interpretation of the results, and the main narrative of the paper, knowing if "simply interacting with a T6SS-negative P. chlororaphis" induces some sporulation would make a big difference. One sentence in the discussion adds to my confusion about this: L464/465, "... a strain lacking paar (Δpaar) had an active T6SS that triggered sporulation comparably to Δhcp, ΔtssA, and Δtse1 strains", suggesting that the authors' claims that even strains lacking active T6SS trigger increased sporulation (which I would agree with, based on the data).

We understand the reviewer's comment that a direct comparison between the two figures is not correct due to fluctuations of the baseline sporulation rates between experiments. To solve this issue, we have added the baseline "no competitor" sporulation percentages in the experiments represented in Figure 2B in the new version of the manuscript.

Related with the sporulation provoked by a T6SS-negative P. chlororaphis, the reviewer is right. Bacillus sporulation occurs due to many external factors (abiotic and biotic stresses) so the presence of P. chlororaphis in the competition already has an effect on the sporulation percentage of B. subtilis. Accordingly, we have removed the statement on the sporulation rates induced by the different T6SS mutants are "statistically" similar to the no-competitor. However, our previous data (Molina-Santiago, Nat Comm 2019) and current findings convincedly demonstrate the relevance of the T6SS and, specifically the Tse1 toxin, in the induction of sporulation at least in the close cell to cell contact.

• Claim regarding "bacteriolytic activity" when tse1 is heterologously expressed in E. coli. The data supporting this claim (Fig2-supplement 2C) only shows a lower net population growth rate after induction of tse1 (truncated vs. non-truncated) expression. This could be caused by: slower growth (but no death), equal growth (with some death), or a combination of the two. The claim of "bacteriolytic" activity in E. coli is therefore not supported by this dataset.

We agree with the reviewer and we have decided to remove this figure and the experiment of “bacteriolytic activity” given that it does not contribute conceptually to the message of the manuscript.

I cannot comment in more detail on the validity of the biochemistry/enzymatic activity assays as these are not my area of expertise.

Reviewer #3 (Public Review):

The authors identify tse1, a gene located in the type 6 secretion system (T6SS) locus of the bacterium Pseudomonas chlororaphis, as necessary and sufficient for induction of Bacillus subtilis sporulation. The authors demonstrate that Tse1 is a hydrolase that targets peptidoglycan in the bacterial cell wall, triggering activation of the regulatory sigma factor sigma-w. The sporulation-inducing effects of sigma-w are dependent on the downstream presence of the sensor histidine kinases KinA and KinB. Overall, this is a well-structured paper that uses a combination of methods including bacterial genetics, HPCL, microscopy, and immunohistochemistry to elucidate the mechanism of action of Tse1 against B. subtilis peptidoglycan. There are some concerns regarding a few experimental controls that were not included/discussed and (in a few figures) the visual representation of the data could be improved. The structure of the manuscript and experiments is such that key questions are addressed in a logical flow that demonstrates the mechanisms described by the authors.

To begin, we have concerns regarding the sporulation assays and their results. The data should be presented as "Percent sporulation" or "Sporulation (%)" - not as a "sporulation rate": there is no kinetic element to any of these measurements, so no rate is being measured (be careful of this in the text as well, for instance near lines 204). More importantly, there is no data provided to indicate that changes in percent spores are not instead just the death of non-sporulated cells. For example, imagine that within a population of B. subtilis cells, 85% of the cells are vegetative and 15% are spores. If, upon exposure to tse1, a large proportion of the vegetative cells are killed (say, 80% of them), this could lead to an apparent increase in sporulation: from 15% for the untreated population to ~50% of the treated, but the difference would be entirely due to a change in the vegetative population, not due to a change in sporulation. The authors need to clearly describe how they conducted their sporulation assays (currently there is no information about this in the methods) as well as provide the raw data of the counts of vegetative cells for their assays to eliminate this concern.

Thanks for the suggestion. We have changed all the titles and data presented as “sporulation rate” by “sporulation (%)” or “sporulation percentage”. As also suggested by reviewer 2, we have included the raw data of the CFUs counts of total population and sporulated cells to show that there is no substantial change in the rate of death. Also, we have added a section in Material and Methods to specify how sporulation assays have been done. Quote text:

“Sporulation assays

Spots of bacteria were resuspended in 1 mL sterile distilled water. Then, serial dilutions were made and cultured in LB solid media for vegetative cells CFU counts. The same serial dilutions were further heated at 80ºC for 10 minutes to kill vegetative cells and immediately cultured again in LB solid media. Plates were grown overnight at 28 ºC and the resulting colonies were counted to calculate the percentage of Bsub sporulation (%). A list of raw CFUs (total and spore population) from all figures with sporulation percentage is shown in Supplementary file 3.”

A related concern is regarding the analysis of the kinases and the effects of their deletions on the impact of Tse1. Previous literature shows that the basal levels of sporulation in a B. subtilis kinA or a kinB mutant are severely defective relative to a wild-type strain; these mutants sporulate poorly on their own. Therefore, the data presented on Lines 394+ and the associated Supplemental Figure regarding the sporulation defects of these two mutants are not compelling for showing that these kinases are required for this effector to act. It is likely that simply missing these kinases would severely impact the ability of these strains to sporulate at all, irrespective of the presence of Tse1, and no discussion of this confounding concern is discussed.

Previous literature shows that mutation of kinases affects sporulation of B. subtilis. Histidine kinases KinA and KinB are the first responsible for initiation of sporulation cascade upon phosphorylation of spo0F. However, as shown in Figure 6-figure supplement 1A, single mutants in these kinases (ΔkinA, ΔkinB) still sporulate given that the phosphorylation cascade is controlled by numerous intermediaries and other histidine kinases that form a multicomponent phosphorelay (KinA-E). In this context, the sporulation of B. subtilis can be also triggered by KinC or KinD in the absence of KinA or KinB, as KinC/KinD can act directly on the master regulator of sporulation Spo0A (Burbulys et al., 1991; Wang et al., 2017).

In addition, as suggested by reviewer 1, we have added to Figure 6-figure supplement 1A of the new version of the manuscript, the sporulation percentage 'no competitor' control of each kinase mutant and B. subtilis WT. The results show that, as commented by the reviewer and also supported by literature, these mutants sporulate poorly on their own in the absence of an attacker (none). However, as shown in the figure, all kinase mutants increase the sporulation percentage in the presence of a competitor.

Another concern is regarding the statistical tests used in Figure 2. For statistical tests in A, B, and D, it should be stated whether a post-test was used to correct for multiple comparisons, and, if so, which post-test was used. to provide a stronger control comparison. For C, we suggest the inclusion of a mock control in addition to the two conditions already included (i.e., an extraction from an E. coli strain expressing the empty vector)

We have clarified the statistical tests used in Figure 2. Briefly, we have used one-way ANOVA followed by the Dunnett test in Figure 2A, B and D for the statistical analysis of the sporulation percentage of Bsub in competition with Pchl as control group. In relation to Figure 2C, it is not possible to add a mock control with a strain carrying the empty vector, because this is a suicide plasmid (pDEST17) unable to replicate in E. coli without chromosome integration.

An additional concern regarding controls is that there is an absence of loading controls for the immunoblot assays. In Figure 5D and all immunoblot assays, there is no mention of a loading control, which is a critical control that should be included.

In the previous version of the manuscript, we already included a loading control for Figure 5D in Figure supplement 7B, both for cell and for supernatant fractions. In the new version of the manuscript, the loading control of Figure 6E (in the previous version of the manuscript Figure 5D) is shown in Figure 6-figure supplement 2C. We have also included the original unedited gels and blot (Figure 6-figure supplement 2- source data 1 and Figure 6-figure supplement 2-source data 2).

Some of the visualizations could be improved to help the reader understand and appropriately interpret the data presented. For instance, in Figures 3 and 4 the scale bars are different across each of the Figure's imaging panels. These should be scaled consistently for better comparison. Additionally, the red false colorization makes the printed images difficult to see. Black-and-white would be easier to see and would not subtract from the images.

The reviewer is right. Scales bar equal 2 in Figure 3A, but the length of the bars was not the same. We have edited the images to have the same magnifications for better comparison.

In relation to Figure 4, we have changed the magnifications and now all the figures have the same scale bars and magnifications. In addition, we have added more images of broader fields in Figure 4-figure supplement 1 which were used to measure the percentage of permeabilized cells and to obtain the fluorescence intensity measures shown in Figure 4.

An additional weakness of the paper is that the RNA-seq data is not fully investigated, and there is an absence of methods included regarding the RNA-seq differential abundance analysis (it is mentioned on L379-380 but no information is provided in the methods). As stated by the authors, 58% of differentially regulated genes belonged to the sw regulon, but the other 42% of genes are not discussed, and will hopefully be a target of future investigations.

The methods section has been modified for a better explanation of the RNA-seq differential abundance analysis. Quote text: “The raw reads were pre-processed with SeqTrimNext (Falgueras et al., 2010) using the specific NGS technology configuration parameters. This pre-processing removes low-quality, ambiguous and low-complexity stretches, linkers, adapters, vector fragments, and contaminated sequences while keeping the longest informative parts of the reads. SeqTrimNext also discarded sequences below 25 bp. Subsequently, clean reads were aligned and annotated using the Bsub reference genome with Bowtie2 (Langmead and Salzberg, 2012) in BAM files, which were then sorted and indexed using SAMtools v1.484(Li et al., 2009). Uniquely localized reads were used to calculate the read number value for each gene via Sam2counts (https://github.com/vsbuffalo/sam2counts). Differentially expressed genes (DEGs) were analyzed via DEgenes Hunter, which provides a combined p value calculated (based on Fisher’s method) using the nominal p values provided by edgeR (Robinson et al., 2010) and DEseq2. This combined p value was adjusted using the Benjamini-Hochberg (BH) procedure (false discovery rate approach) and used to rank all the obtained DEGs. For each gene, combined p value < 0.05 and log2-fold change > 1 or < −1 were considered as the significance threshold”

Regarding the RNA-seq analysis, we are aware of the amount of information that can be extracted. Previous to filtering the information shown in the manuscript, we have done bioinformatic analysis trying to find a connection with the cellular response, that is increase of sporulation. Besides this, we had some observations but with no direct connection to sporulation, which would be interesting to pursue in future studies, but not for the clarity of this story (Figure 23 below). In any case, we are including the whole picture of the transcriptomics changes occurring in Bsub after treatment with Tse1. KEGG pathway analyses of genes differentially expressed showed induction of flagellar assembly and aminobenzoate degradation, nitrogen and amino acid metabolisms. Interestingly, fatty acid degradation and CAMP resistance pathways were also induced, probably related to changes suffered in the cell wall after the action of Tse1 toxin. On the other hand, synthesis and degradation of ketone bodies pathway was mostly repressed.

Figure 2. KEGG pathway analyses of genes differentially expressed occurring in Bsub after treatment with Tse1.

Another methodological concern in this paper is the limited details provided for the calculation of the permeabilization rate (Figure 4, L359, L662-664). It is not clear how, or if, cell density was controlled for in these experiments.

We agree with the reviewer and we have explained with more detail how the permeabilization rate was calculated. Quote text: “N=3 for Bsub treated with Tse1 and N=3 for untreated Bsub. N refers to the number of CLSM fields analyzed to calculate the number of permeabilized cells of the total of cells in the field”

Finally, one weakness of the paper is the broad conclusions that they draw. The authors claim that the mechanism of sporulation activation is conserved across Bacilli when the authors only test one B. subtilis and one B. cereus strain. They further argue (lines 469+) that Tse1 requires a PAAR repeat for its targeting, but do not provide direct evidence for this possibility.

We have reduced the tone of the final conclusion in order to specify that the activation of sporulation is a mechanism that can be found in different Bacillus species such as Bsub and Bcer. Related with the second appreciation, we have included a further explanation for this argument. Quote text: “As shown in Figure 2B, a paar mutant has an active T6SS able to kill E. coli. However, as shown in Figure 2A, we noticed that a paar mutant (which encodes tse1) is not able to trigger B. subtilis sporulation to a similar level than Pchl WT strain. Given that paar deletion apparently abolishes Tse1 secretion, we suggest that Tse1 is a PAAR-associated effector that requires a PAAR repeat domain protein to be targeted for secretion, thereby increasing Bacillus sporulation during contact with Pseudomonas cells (Cianfanelli et al., 2016; Hachani et al., 2014; Whitney et al., 2014)”.

Author Response

Reviewer #1 (Public Review):

In this manuscript, Elkind et al. use a deep learning segmentation algorithm trained on detecting putative cell nuclei in mouse brains to count cells in the Allen Mouse Brain Connectivity Atlas. The Allen Mouse Brain Connectivity Atlas is a dataset compromising hundreds of mice brains. The authors use this increased statistical power for detecting differences in volume, cell count, and cell density between strains (C57BL/6J and FVB.CD1) as well as sex differences.

Both volume, cell count, and cell density are regularly used in neuroanatomy to normalize or benchmark results so having a large available dataset for others to compare their data would be a useful resource. The trained segmentation algorithm might also find utility in assays where investigators for one reason or another can't dedicate an entire labeled channel to count cell nuclei.

Nevertheless, because of technical reasons, I find the current work problematic.

We thank the Reviewer for acknowledging potential usefulness of our work, and the insightful, helpful comments. We believe this consideration has made our revised manuscript much stronger compared to the initial submission. We hope our revised version will also clear the Reviewer’s remaining doubts.

Major:

The authors make use of the "red" channel from the Allen Mouse Brain Connectivity Project (AMBCP). The AMBCP was acquired using two-photon tomography with the TissueCyte 1000 system (http://help.brain-map.org/download/attachments/2818171/Connectivity_Overview.pdf?version=2&modificationDate=1489022310670&api=v2). The sample is illuminated at 925 nm wavelength and the channel the authors describe as autofluorescence is collected through a 593/40 nm bandpass filter. The authors go on to describe their rationale for using this channel for quantifying cell nuclei:

"We noticed that the red (background) channel of STPT images, taken for the purpose of atlas alignment, typically features dark, round-like objects resembling cell nuclei. We had observed this phenomenon in our own imaging of mouse brains but found little more than anecdotal mentions of it in the literature8,9,10,11".

The authors here cite a Scientific Reports paper from 2021 with 11 citations, a Journal of Clinical Pathology paper from 2005 with 87 citations, and lastly a paper in Laboratory Investigation from 2016 with 41 citations. The authors completely fail to cite the work from Watt Webb's group (co-inventor of 2p microscopy) in PNAS from 2003 that entirely described the phenomena of native fluorescence by multiphoton- excitation (https://www.pnas.org/doi/10.1073/pnas.0832308100 ), citations so far: 1959 citations. This is either indicative of poor scholarship or an attempt to describe something as novel. Either way, the native fluorescence and second harmonic generation from multiphoton illumination are perfectly characterized by Webb and colleagues and they clearly show the differential effect on nucleosides, retinol, indoleamines, and collagen. This is also where the authors should have paid more attention to discrepancies in their own data when correlated to well-established cell nuclei markers (Murakami et al). The authors will note "black large spots" in the data at specific anatomical regions and structures, like the fornix and stria medullaris: https://connectivity.brain-map.org/projection/experiment/siv/263780729?imageId=263780960&imageType=TWO_PHOTON,SEGMENTATION&initImage=TWO_PHOTON&x=15702&y=18833&z=5

which is not reproduced in for example the Allen Reference Atlas H&E staining: http://atlas.brain-map.org/atlas?atlas=1&plate=100960284#atlas=1&plate=100960284&resolution=4.19&x=5507.4000244140625&y=5903.39990234375&zoom=-2

In connection here notice the poor signal in the 2p "autofluorescence" within the paraventricular nucleus: https://connectivity.brain-map.org/projection/experiment/siv/263780729?imageId=263780960&imageType=TWO_PHOTON,SEGMENTATION&initImage=TWO_PHOTON&x=15702&y=17833&z=6

and then compare it to the H&E staining: http://atlas.brain-map.org/atlas?atlas=1&plate=100960280#atlas=1&plate=100960276&resolution=1.50&x=5342.476283482143&y=5368.023856026786&zoom=0

These multiphoton-specific signals are especially pronounced in the pons and medulla which makes quantification especially dubious, which is even apparent simply from looking at Figure 1c in the manuscript.

We thank the Reviewer for the comments and sincerely apologize for missing the seminal work of Webb’s group. We included the former references for their specific mention or illustration of non-autofluorescent nuclei. We indeed entirely missed to address the underlying chemistry that Webb’s group beautifully characterized. We have added the following sentence in the Results section “Autofluorescence of STPT images displays cell nuclei” (red font for new sentence; Reference #15 corresponds to Zipfel et al.):

“We noticed that the red (background) channel of STPT images, taken for the purpose of atlas alignment, typically features dark, round-like objects resembling cell nuclei. This phenomenon was described in previous literature11,12,13,14. In particular, Zipfel et al. characterized the use of multiphoton-excited native florescence and second harmonic generation for the purpose of staining-free tissue imaging15.”

And mentioned the dependency of our method on the presence of intrinsically fluorescent molecules in the Discussion:

“The study has several limitations. First, the model is sensitive to the contrast between dark nuclei and autofluorescent surroundings, which can be limited by image quality and tissue composition. In particular, the staining-free approach depends on the presence of intrinsic molecular indicators such as NADH, retinol or collagen15, which may vary between cell or tissue components, even within the brain.”

We understand that more generally, the Reviewer’s major concern above was regarding the technical validity of our approach; that the segmentation based on small objects lacking autofluorescence, as evident in the STPT dataset, in fact corresponds to cells/nuclei.

In our initial Supplemental Figure 1 (in current version Figure 1—figure supplement 1) we provide technical validation of the method, by showing nuclear staining, and autofluorescence side-by-side, using epifluorescence microscopy. In our revision we now report appropriate statistical measures for this analysis (true positives, false positives, false negatives).

In addition, we performed the following two sets of validations –

(i) Technical validation of our staining-free quantification approach, by nuclear staining. We performed nuclear staining (Hoechst 33342) followed by STPT imaging of 9 female brains and trained a new deep neural network (DNN) to segment the resulting images (STPT was performed by TissueVision). Unfortunately, in STPT it is not technically possible to analyze nuclear staining and autofluorescence in the very same tissue. Therefore, we compared per-region density, cell count and volume of the nuclei-stained validation brains to our original DNN-based analysis of AMBCA brains. We show a correlation coefficient >0.99 for per-region cell count in AMBCA autofluorescence and our nuclear staining (and a similar correlation coefficient for volume). However, the number of cells in nuclear staining over the whole brain is 56% larger than in autofluorescence. Although we currently have no technically feasible way to prove this, one likely explanation for this discrepancy is the nature of the two signals the imaging detects; as positive (Hoechst fluorophore) or autofluorescence. Further, discrepancies between the two methods were notably higher in glial-rich tissues (e.g., CTX L1, midbrain, brainstem) – leading to the speculation that low-autofluorescent object-counts may be biased to detect neurons, rather than glia.

(ii) Independent validation of the biological findings – discussed further below. Regarding the specific concern of “black large spots” in the fornix and stria medullaris – we would like to emphasize that our DNN does not identify and segment dark regions like ventricles and tracks. We provide in the Author Response Image 1 three examples featuring “black large spots” of different shapes and size, with examples of the segmentation results as shown in Figures 1 and 2 of the manuscript. Note that colored circles, that appear as dots depending on magnification, are the objects that were detected and segmented by the DNN. In the Figure we demonstrate that (1) fiber tracts (incl. fornix, stria medullaris) are not segmented; (2) striatal patches (that are smaller still than the fiber tracts in question) are not segmented; and (3) putative blood vessels, appearing as elongated, black structures, are ignored by our DNN.

Author Response Image 1. How does the DNN deal with large black spots? Examples for fiber tracts, striatal patches, and blood vessels; adapted from Figures 1 and 2 in the manuscript. Note that dots/outlines represent segmented putative “nuclei” as detected by the model, colored by assigned region according to Allen Mouse Brain hierarchy. Example (1): fiber tracts (incl. fornix, stria medullaris) are not segmented. Example (2): Striasomes (patches in the striatum, that are smaller still than the fiber tracts in question) are not segmented, and the much smaller objects that are detected as putative nuclei are indicated by arrows. Example (3) putative blood vessels, appearing as elongated, black structures, are ignored by our DNN. Examples of the segmentation images were adapted from the manuscript’s Figure 1 to correspond to the STPT image featuring fiber tracts (and Striasomes/patches) was pointed out by the Reviewer.

Retrieved from: https://connectivity.brain-map.org/projection/experiment/siv/263780729?imageId=263780960&imageType=TWO_PHOTON,SEGMENTATION&initImage=TWO_PHOTON&x=15702&y=18833&z=5.

Regarding the claim of problematic counting in brain stem regions, we agree, and had addressed this limitation in the manuscript’s Discussion (see below). We believe that our counting is valuable even if in some regions there is a significant systematic error: Most of the analyses in this study compare brain regions across individuals and thus systematic error is less impactful. In the revision, we nevertheless took care to validate and quantify the size of this effect. Briefly, we compared counting based on nuclear staining (Hoechst) from 9 STPT imaged brains, to our quantifications of non-autofluorescent objects. As expected, the ratio between these counts depends on the brain region, and accuracy is better in regions with high brightness, which are not on the border of the section (Figure 2—figure supplement 2). As for pons and medulla, the densities in our Hoechst quantifications are 43% and 60% higher than in our AMBCA analysis, respectively, yet rank order is kept in both.

We have revised the relevant sentences in the Discussion:

Original sentences: The study has several limitations. … In the hindbrain (pons, medulla), contrast was exceedingly weak, and we expect our quantifications in this region to strongly underestimate real cell densities, to an extent we cannot quantify.

Revised sentences: The study has several limitations. … In the hindbrain (pons, medulla), contrast was exceedingly weak, and we expect our quantifications in this region to be 66% of the value estimated by nuclear staining (Figure 2—figure supplement 2).

The authors here use the correlation on log-log coordinates between their data and that of Murakami et al to argue that the method has validity. However, the variance explained here is R^2 = 0.74 which is very poor given the log-log coordinates. A more valid metric would use linear coordinates and computing the ICC and interpret it according to established guidelines (e.g. https://www.ncbi.nlm.nih.gov/pmc/articles/PMC4913118/).

As mentioned by the Reviewer, Figure 2D compares Murakami et al. cell counts and ours, across all brain regions. The value “r=0.869” represents the correlation coefficient between the two vectors in log scale and not the R^2. We also now display the correlation coefficient for the linear scale, in which case p=0.98. As suggested by the Reviewer, we added ICC values between the two vectors in linear scale. Using 6 different forms (ICC – 1-1;1-k;C-1;C-k;A-1;A-k), the ICC values were 0.98-0.99, thus corresponding to an excellent agreement (ICC values are mentioned in legend of Figure 2).

Author Response Image 2 displays the revised Figure 2D (left), and the log value of the ratio between the AMBCA-based cell count and the Murakami-based value (right), as a function of region volume. The mean value across regions is zero, corresponding to similar cell counts in both methods. Indeed, there exist outlier regions, that may be attributed to either registration errors, different experimental protocols or may stem from the fact that the Murakami values are based on 3 brains, compared to hundreds of AMBCA brains.

Author Response Image 2. Correlation with cell counts in Murakami et al. Left, revised Figure 2D; Right, ratio between AMBCA-based cell counts and Murakami et al. counts, as a function of region volume  

In addition to the above concern, the authors argue that the large sample size of the AMBCP is what would enable them to find statistically significant small effect sizes that might have gone undetected in the literature. However, this argument falls flat once we examine some of the main findings the authors report. Although the authors do not directly report measures of dispersion we can estimate it from the figures and then arrive at the sample size needed to find the reported effect size. For example, the effect that describes ORBvl2/3 volume is larger in female mice compared to males would only require n=13 mice at the desired power of 0.8. Likewise, the sample size needed to detect the increased BST volume in male mice looks to be roughly n=16 mice at the desired power of 0.8. Both of these estimates are well within what is a reasonable sample size to expect in an ordinary study. This begs the question: why did the authors simply not verify some of their main findings in an independent sample obtained through traditional ways to quantify volume and cell density since it is well within reach? Such validation would strengthen the arguments of the paper.

We thank the reviewer for this comment and apologize. In the revised version we do report dispersion.

We would like to emphasize that due to our restricted time and resources, we decided to focus our experimental validation on the technical comparison of nuclear staining vs. autofluorescence-based segmentation, outlined above.

We then verified the biological findings from the initial cohort using C57BL/6J volume data from an additional 663 males vs.166 females on AMBCA. This independent cohort showed similar sexual dimorphism in the volume of MEA, BST and ORBvl2/3, as depicted in the following figure (panels A-D and also as new Figure 4—figure supplement 1).

We fully acknowledge the interesting issue raised on sample sizes required to detect our reported effect sizes. Therefore, we here also present the average p-value for sexual dimorphism in volumes of MEA, BST and ORBvl2/3, as a function of the sample size (panel E in Figure 4—figure supplement 1 of the revised manuscript). The Reviewer will note that the regions with largest effect size (MEA, BST) can be detected within more ordinary sample sizes, and indeed, MEA and BST dimorphism is evident in the literature. ORB dimorphism required much greater sample size; and our analysis (Figure 4) systematically detected many more dimorphic regions, in volume, density and count.

Reviewer #2 (Public Review):

This report describes a large-scale analysis of cell counts in mouse brains. The authors found that the Allen Mouse Connectivity project has a rich dataset for cell counting that is yet to be analyzed, and they developed methods to quantify cells in different nuclei. They go on to compare males vs females and two different strains. From this analysis, they found specific differences between male versus female brains, left versus right hemispheres, and C57BL/6 versus FVB.CD1 mice, especially with regard to cell counts and density.

Overall, the methodology is sound and the quality of the data seems high. In fact, this study uses >100 brains for the statistics, and this is one of the major strengths of this study. For researchers who are interested in interrogating the differences at the macroscopic level in brain structures, this study will be a great resource. For example, the manuscript contains an interesting finding that for most brain areas, females have larger volumes but fewer cell numbers.

We thank the Reviewer for these comments. We would like to mention that the revised version of the manuscript does not include a statement regarding BL6 female volume. We found a batch effect in the AMBCA experiments, mostly affecting the volume in their first batch (Figure 2—figure supplement 1B). That batch included mostly males, and had, for some reason, lower volume compared to all later experiments, which caused the volume differences. We emphasize that (1) the total number of cells did not show any batch effect (Figure 2—figure supplement 1C); (2) We normalized the volume and repeated the analysis. Aside the finding that females did not in fact have larger volumes, other main findings remained unchanged.

Reviewer #3 (Public Review):

Elkind et al. have devised a strategy to detect cells in whole brain samples of the large, publicly accessible Allen Mouse Brain Connectivity database. They put together an analysis pipeline to quantify cell numbers and -density as well as volumes for all annotated brain areas in these samples. This allowed them to make several important discoveries such as (1) strain-, sex- and hemisphere-specific differences in cell densities, (2) a large interindividual variability in cell numbers, and (3) an absence of linear scaling of cell count with volume, among others. The key strength of this work lies in its comprehensive analysis, the large sample size that the authors have drawn from (making their conclusions particularly robust), and the fact that they have made their analysis tools accessible. A weakness of the current manuscript is the dense layout and overplotting of several of the figures, and the lack of necessary information to understand them more easily. Another, conceptual weakness of using the autofluorescence channel for cell detection is that the identity (neuronal vs non-neuronal) of the underlying cells remains unresolved. Overall, however, I believe that this study has the potential to serve as a valuable reference point, and I would expect this work to have a lasting impact on quantitative studies of mouse brain cytoarchitecture.

We thank the Reviewer for these valuable comments. We have tried to minimize overplotting of figures and hopefully added all necessary information. For example, the revised manuscript presents more pared-down figures, with data labels omitted if they crowded the graphic. Instead, we provide the full data in Supplemental tables, and our online accessible GUI. We hope the reader will feel encouraged to both zoom the presented data, more deeply explore additional tables, and our online tool.

Regarding the question of cell types, we were unfortunately not able to provide a definitive answer, but our validation experiments provided some potential clues. For example, nuclear staining (Hoechst) uniformly detected 65% more cells than AMBCA autofluorescence quantification. And, in neuron-rich regions, the correspondence between nuclear staining and AMBCA autofluorescence was notably better than in glia-rich regions (e.g., CTX L1, midbrain, medulla). These discrepancies between the techniques may therefore point to an underlying difference in cell types composition – such that counting low-autofluorescent nuclei is biased to neurons.

In addition, however, the methods differ in their native physical properties; in that one detects presence of a fluorescent signal (e.g., the nuclear stain is detected beyond its focal plane), compared to the detection of the absence of a signal (which, in turn, is dependent on the presence of surrounding intrinsic fluorescent molecules). It is technically non-trivial to assess the extent to which these factors apply. We have added a clarification along these lines in the Discussion (below). We would further like to emphasize the nature of our study as a comparative, systematic analysis within this interesting cohort, rather than providing definitive cell counts – that we found to be greatly variable across the population.

“We further attempted to estimate the region-specific accuracy of our cell counting by comparing autofluorescence STPT with brain-wide imaging of nuclear-stained STPT. However, this comparison is technically nontrivial because of the native physical properties of direct staining vs. autofluorescence. For example, stained nuclei located off the focal plane may appear in the image, yet remain undetected by autofluorescence. In addition, tissue composition (e.g., cell types, extracellular matrix) may affect the imaged region. Indeed, in regions rich with non-neuronal cells the error of autofluorescent-based counting was larger compared to nuclear staining. Hence, one may speculate that autofluorescent-based detection is biased for neurons”

Author Response:

Reviewer #1 (Public Review):

Chakrabarti et al study inner hair cell synapses using electron tomography of tissue rapidly frozen after optogenetic stimulation. Surprisingly, they find a nearly complete absence of docked vesicles at rest and after stimulation, but upon stimulation vesicles rapidly associate with the ribbon. Interestingly, no changes in vesicle size were found along or near the ribbon. This would have indicated a process of compound fusion prior to plasma membrane fusion, as proposed for retinal bipolar cell ribbons. This lack of compound fusion is used to argue against MVR at the IHC synapse. However, that is only one form of MVR. Another form, coordinated and rapid fusion of multiple docked vesicles at the bottom of the ribbon, is not ruled out. Therefore, I agree that the data set provides good evidence for rapid replenishment of the ribbon-associated vesicles, but I do not find the evidence against MVR convincing. The work provides fundamental insight into the mechanisms of sensory synapses.

We thank the reviewer for the appreciation of our work and the constructive comments. As pointed out below, we now included this discussion (from line 679 onwards).

We wrote:

“This might reflect spontaneous univesicular release (UVR) via a dynamic fusion pore (i.e. ‘kiss and run’, (Ceccarelli et al., 1979), which was suggested previously for IHC ribbon synapses (Chapochnikov et al., 2014; Grabner and Moser, 2018; Huang and Moser, 2018; Takago et al., 2019) and/or and rapid undocking of vesicles (e.g. Dinkelacker et al., 2000; He et al., 2017; Nagy et al., 2004; Smith et al., 1998). In the UVR framework, stimulation by ensuing Ca2+ influx triggers the statistically independent release of several SVs. Coordinated multivesicular release (MVR) has been indicated to occur at hair cell synapses (Glowatzki and Fuchs, 2002; Goutman and Glowatzki, 2007; Li et al., 2009) and retinal ribbon synapses (Hays et al., 2020; Mehta et al., 2013; Singer et al., 2004) during both spontaneous and evoked release. We could not observe structures which might hint towards compound or cumulative fusion, neither at the ribbon nor at the AZ membrane under our experimental conditions. Upon short and long stimulation, RA-SVs as well as docked SVs even showed a slightly reduced size compared to controls. However, since some AZs harbored more than one docked SV per AZ in stimulated conditions, we cannot fully exclude the possibility of coordinated release of few SVs upon depolarization.”

Reviewer #2 (Public Review):

Chakrabarti et al. aimed to investigate exocytosis from ribbon synapses of cochlear inner hair cells with high-resolution electron microscopy with tomography. Current methods to capture the ultrastructure of the dynamics of synaptic vesicle release in IHCs rely on the application of potassium for stimulation, which constrains temporal resolution to minutes rather than the millisecond resolution required to analyse synaptic transmission. Here the authors implemented a high-pressure freezing method relying on optogenetics for stimulation (Opto-HPF), granting them both high spatial and temporal resolutions. They provide an extremely well-detailed and rigorously controlled description of the method, falling in line with previously use of such "Opto-HPF" studies. They successfully applied Opto-HPF to IHCs and had several findings at this highly specialised ribbon synapse. They observed a stimulation-dependent accumulation of docked synaptic vesicles at IHC active-zones, and a stimulation-dependent reduction in the distance of non-docked vesicles to the active zone membrane; while the total number of ribbon-associated vesicles remained unchanged. Finally, they did not observe increases in diameter of synaptic vesicles proximal to the active zone, or other potential correlates to compound fusion - a potential mode of multivesicular release. The conclusions of the paper are mostly well supported by data, but some aspects of their findings and pitfalls of the methods should be better discussed.

We thank the reviewer for the appreciation of our work and the constructive comments.

Strengths:

While now a few different groups have used "Opto-HPF" methods (also referred to as "Flash and Freeze) in different ways and synapses, the current study implemented the method with rigorous controls in a novel way to specifically apply to cochlear IHCs - a different sample preparation than neuronal cultures, brain slices or C. elegans, the sample preparations used so far. The analysis of exocytosis dynamics of IHCs with electron microscopy with stimulation has been limited to being done with the application of potassium, which is not physiological. While much has been learned from these methods, they lacked time resolution. With Opto-HPF the authors were successfully able to investigate synaptic transmission with millisecond precision, with electron tomography analysis of active zones. I have no overall questions regarding the methodology as they were very thoroughly described. The authors also employed electrophysiology with optogenetics to characterise the optical simulation parameters and provided a well described analysis of the results with different pulse durations and irradiance - which is crucial for Opto-HPF.

Thank you very much.

Further, the authors did a superb job in providing several tables with data and information across all mouse lines used, experimental conditions, and statistical tests, including source code for the diverse analysis performed. The figures are overall clear and the manuscript was well written. Such a clear representation of data makes it easier to review the manuscript.

Thank you very much.

Weaknesses:

There are two main points that I think need to be better discussed by the authors.

The first refers to the pitfalls of using optogenetics to analyse synaptic transmission. While ChR2 provides better time resolution than potassium application, one cannot discard the possibility that calcium influx through ChR2 alters neurotransmitter release. This important limitation of the technique should be properly acknowledged by the authors and the consequences discussed, specifically in the context in which they applied it: a single sustained pulse of light of ~20ms (ShortStim) and of ~50ms (LongStim). While longer, sustained stimulation is characteristic for IHCs, these are quite long pulses as far as optogenetics and potential consequences to intrinsic or synaptic properties.

We thank the reviewer for pointing this out. We would like to mention that upon 15 min high potassium depolarization, the number of docked SVs only slightly increased as shown in Chakrabarti et al., 2018, EMBO rep and Kroll et al. 2020 JCS, but it was not statistically significant. In the current study, we report a similar phenomenon, but here light induced depolarization resulted in a more robust increase in the number of docked SVs.

To compare the data from the previous studies with the current study, we included an additional table 3 (line 676) now in the discussion with all total counts (and average per AZ) of docked SVs.

Furthermore, in response to the reviewers’ concern, we now discuss the Ca2+ permeability of ChR2 in addition to the above comparison to our previous studies that demonstrated very few docked SVs in the absence of K+ channel blockers and ChR2 expression in IHCs. We are not entirely certain, if the reviewer refers to potential dark currents of ChR2 (e.g. as an explanation for a depletion of docked vesicles under non-stimulated conditions) or to photocurrents, the influx of Ca2+ through ChR2 itself, and their contribution to Ca2+ concentration at the active zone.

However, regardless this, we consider it unlikely that a potential contribution of Ca2+ influx via ChR2 evokes SV fusion at the hair cell active zone.

First of all, we note that the Ca2+ affinity of IHC exocytosis is very low. As first shown in Beutner et al., 2001 and confirmed thereafter (e.g. Pangrsic et al., 2010), there is little if any IHC exocytosis for Ca2+ concentrations at the release sites below 10 µM. Two studies using CatCh (a ChR2 mutant with higher Ca2+ permeability than wildtype ChR2 (Kleinlogel et al., 2011; Mager et al., 2017) estimated a max intracellular Ca2+ increase below 10 µM, even at very negative potentials that promote Ca2+ influx along the electrochemical gradient or at high extracellular Ca2+ concentrations of 90 mM. In our experiments, IHCs were depolarized, instead, to values for which extrapolation of the data of Mager et al., 2017 indicate a submicromolar Ca2+ concentration. In addition, we and others have demonstrated powerful Ca2+ buffering and extrusion in hair cells (e.g. Tucker and Fettiplace, 1995; Issa and Hudspeth., 1996; Frank et al., 2009 Pangrsic et al., 2015). As a result, the hair cells efficiently clear even massive synaptic Ca2+ influx and establish a low bulk cytosolic Ca2+ concentration (Beutner and Moser, 2001; Frank et al., 2009). We reason that these clearance mechanisms efficiently counter any Ca2+ influx through ChR2. This will likely limit potential effects of ChR2 mediated Ca2+ influx on Ca2+ dependent replenishment of synaptic vesicles during ongoing stimulation.

We have now added the following in the discussion (starting in line 620):

“We note that ChR2, in addition to monovalent cations, also permeates Ca2+ ions and poses the question whether optogenetic stimulation of IHCs could trigger release due to direct Ca2+ influx via the ChR2. We do not consider such Ca2+ influx to trigger exocytosis of synaptic vesicles in IHCs. Optogenetic stimulation of HEK293 cells overexpressing ChR2 (wildtype version) only raises the intracellular Ca2+ concentration up to 90 nM even with an extracellular Ca2+ concentration of 90 mM (Kleinlogel et al., 2011). IHC exocytosis shows a low Ca2+ affinity (~70 µM, Beutner et al., 2001) and there is little if any IHC exocytosis for Ca2+ concentrations below 10 µM, which is far beyond what could be achieved even by the highly Ca2+ permeable ChR2 mutant (CatCh: Ca2+ translocating channelrhodopsin, Mager et al., 2017). In addition, we reason that the powerful Ca2+ buffering and extrusion by hair cells (e.g., Frank et al., 2009; Issa and Hudspeth, 1996; Pangršič et al., 2015; Tucker and Fettiplace, 1995) will efficiently counter Ca2+ influx through ChR2 and, thereby limit potential effects on Ca2+ dependent replenishment of synaptic vesicles during ongoing stimulation. “

The second refers to the finding that the authors did not observe evidence of compound fusion (or homotypic fusion) in their data. This is an interesting finding in the context of multivesicular release in general, as well as specifically for IHCs. While the authors discussed the potential for "kiss-and-run" and/or "kiss-and-stay", it would be valuable if they could discuss their findings further in the context of the field for multivesicular release. For example, the evidence in support of the potential of multiple independent release events. Further, as far as such function-structure optical-quick-freezing methods, it is not unusual to not capture fusion events (so-called omega-shapes or vesicles with fusion pores); this is largely because these are very fast events (less than 10 ms), and not easily captured with optical stimulation.

We agree with the reviewer that the discussion on MVR and UVR should be extended. We now added the following paragraph to the discussion from line 679 on:

“This might reflect spontaneous univesicular release (UVR) via a dynamic fusion pore (i.e. ‘kiss and run’, (Ceccarelli et al., 1979), which was suggested previously for IHC ribbon synapses (Chapochnikov et al., 2014; Grabner and Moser, 2018; Huang and Moser, 2018; Takago et al., 2019) and/or and rapid undocking of vesicles (e.g. Dinkelacker et al., 2000; He et al., 2017; Nagy et al., 2004; Smith et al., 1998). In the UVR framework, stimulation by ensuing Ca2+ influx triggers the statistically independent release of several SVs. Coordinated multivesicular release (MVR) has been indicated to occur at hair cell synapses (Glowatzki and Fuchs, 2002; Goutman and Glowatzki, 2007; Li et al., 2009) and retinal ribbon synapses (Hays et al., 2020; Mehta et al., 2013; Singer et al., 2004) during both spontaneous and evoked release. We could not observe structures which might hint towards compound or cumulative fusion, neither at the ribbon nor at the AZ membrane under our experimental conditions. Upon short and long stimulation, RA-SVs as well as docked SVs even showed a slightly reduced size compared to controls. However, since some AZs harbored more than one docked SV per AZ in stimulated conditions, we cannot fully exclude the possibility of coordinated release of few SVs upon depolarization.”

Reviewer #3 (Public Review):

Precise methods were developed to validate the expression of channelrhodopsin in inner hair cells of the Organ of Corti, to quantify the relationship between blue light irradiance and auditory nerve fiber depolarization, to control light stimulation within the chamber of a high-pressure freezing device, and to measure with good precision the delay between stimulation and freezing of the specimen. These methods represent a clear advance over previous experimental designs used to study this synaptic system and are an initial application of rapid high-pressure freezing with freeze substitution, followed by high-resolution electron tomography (ET), to sensory cells that operate via graded potentials.

Short-duration stimuli were used to assess the redistribution of vesicles among pools at hair cell ribbon synapses. The number of vesicles linked to the synaptic ribbon did not change, but vesicles redistributed within the membrane-proximal pool to docked locations. No evidence was found for vesicle-to-vesicle fusion prior to vesicle fusion to the membrane, which is an important, ongoing question for this synapse type. The data for quantifying numbers of vesicles in membrane-tethered, non-tethered, and docked vesicle pools are compelling and important.

We thank the reviewer for the appreciation of our work and the constructive comments.

These quantifications would benefit from additional presentation of raw images so that the reader can better assess their generality and variability across synaptic sites.

The images shown for each of the two control and two experimental (stimulated) preparation classes should be more representative. Variation in synaptic cleft dimensions and numbers of ribbon-associated and membrane-proximal vesicles do not track the averaged data. Since the preparation has novel stimulus features, additional images (as the authors employed in previous publications) exhibiting tethered vesicles, non-tethered vesicles, docked vesicles, several sections through individual ribbons, and the segmentation of these structures, will provide greater confidence that the data reflect the images.

Thank you very much for pointing this out. We now included more details in supplemental figures and in the text.

Precisely, we added:

• More details about the morphological sub-pools (analysis and images):

  -We now show a sequence of images with different tethering states of membrane proximal SVs together with examples for docked and non-tethered SVs as we did in Chakrabarti et al., 2018 for each condition (Fig. 6-figure supplement 2, line 438). Moreover, we included for each condition additional information, we selected further tomograms, one per condition, and depict two additional virtual sections: Fig. 6-figure supplement 2.

  -Moreover, we present a more detailed quantification for the different morphological sub-pools: For the MP-SV pool, we analyzed the SV diameters and the distances to the AZ membrane and PD of different SV sub-pools separately, we now included this information in Fig. 7 For the RA-SVs, we analyzed in addition the morphological sub-pools and the SV diameters in the distal and the proximal ribbon part as done in Chakrabarti et al. 2018. We now added a new supplement figure (Fig. 7-figure supplement 2, line 558 and a supplementary file 2).

• We replaced the virtual section in panel 6D: In the old version, it appeared that the ribbon was contacting the membrane and we realized that this virtual section was not representative: actually, the ribbon was not directly contacting the AZ membrane, a presynaptic density was still visible adjacent to the docked SVs. To avoid potential confusion, we selected a different virtual section of the same tomogram and now indicated the presynaptic density also as graphical aid in Fig. 6.

The introduction raises questions about the length of membrane tethers in relation to vesicle movement toward the active zone, but this topic was not addressed in the manuscript.

We apologize for not stating it sufficiently clear, we now rephrased this sentence. We now wrote:

“…and seem to be organized in sub-pools based on the number of tethers and to which structure these tethers are connected. “

Seemingly quantification of this metric, and the number of tethers especially for vesicles near the membrane, is straightforward. The topic of EPSC amplitude as representing unitary events due to variation in vesicle volume, size of the fusion pore, or vesicle-vesicle fusion was partially addressed. Membrane fusion events were not evident in the few images shown, but these presumably occurred and could be quantified. Likewise, sites of membrane retrieval could also be marked. These analyses will broaden the scope of the presentation, but also contribute to a more complete story.

Regarding the presence/absence of membrane fusion events we agree with the reviewer that this should be clearly addressed in the MS. We would like to point out that we

(i) did not observe any omega shapes at the AZ membrane, which we also mention in the MS. We can also report that we could not see them in data sets from previous publications (Vogl et al., 2015, JCS; Jung et al., 2015, PNAS).

(ii) To be clear on our observations on potential SV-SV fusion events we now point out in the discussion from line 688ff:

“We could not observe structures which might hint towards compound or cumulative fusion, neither at the ribbon nor at the AZ membrane under our experimental conditions. Upon short and long stimulation, RA-SVs as well as docked SVs even showed a slightly reduced size compared to controls. However, since some AZs harbored more than one docked SV per AZ in stimulated conditions, we cannot fully exclude the possibility of coordinated release of few SVs upon depolarization.”

Furthermore, we agree with the reviewer that a complete presentation of endo-exocytosis structural correlates is very important. However, we focused our study on exocytosis events and therefore mainly analyzed membrane proximal SVs at active zones.

Nonetheless, in response to the reviewer’s comment, we now included a quantification of clathrin-coated (CC) structures. We determined the appearance of CC vesicles (V) and CC invaginations within 0-500 nm away from the PD. We measured the diameter of the CCV, and their distance to the membrane and the PD. We only found very few CC structures in our tomograms (now added in a table to the result section (Supplementary file 1). Sites for endocytic membrane retrieval likely are in the peri-active zone area or even beyond. We did not observe obvious bulk endocytosis events that were connected to the AZ membrane. However, we do observe large endosomal like vesicles that we did not quantify in this study. More details were presented in two of our previous studies: Kroll et al., 2019 and 2020, however, under different stimulation conditions.

Overall, the methodology forms the basis for future studies by this group and others to investigate rapid changes in synaptic vesicle distribution at this synapse.

Reviewer #4 (Public Review):

This manuscript investigates the process of neurotransmitter release from hair cell synapses using electron microscopy of tissue rapidly frozen after optogenetic stimulation. The primary finding is that in the absence of a stimulus very few vesicles appear docked at the membrane, but upon stimulation vesicles rapidly associate with the membrane. In contrast, the number of vesicles associated with the ribbon and within 50 nm of the membrane remains unchanged. Additionally, the authors find no changes in vesicle size that might be predicted if vesicles fuse to one-another prior to fusing with the membrane. The paper claims that these findings argue for rapid replenishment and against a mechanism of multi-vesicular release, but neither argument is that convincing. Nonetheless, the work is of high quality, the results are intriguing, and will be of interest to the field.

We thank the reviewer for the appreciation of our work and the constructive comments.

1) The abstract states that their results "argue against synchronized multiquantal release". While I might agree that the lack of larger structures is suggestive that homotypic fusion may not be common, this is far from an argument against any mechanisms of multi-quantal release. At least one definition of synchronized multiquantal release posits that multiple vesicles are fusing at the same time through some coordinated mechanism. Given that they do not report evidence of fusion itself, I fail to see how these results inform us one way or the other.

We agree with the reviewer that the discussion on MVR and UVR should be extended. It is important to point out that we do not claim that the evoked release is mediated by one single SV. As discussed in the paper (line 672), we consider that our optogenetic stimulation of IHCs triggers the release of more than 10 SVs per AZ. This falls in line with the previous reports of several SVs fusing upon stimulation. This type of evoked MVR is probably mediated by the opening of Ca2+ channels in close proximity to each SV Ca2+ sensor. We indeed sometimes observed more than one docked SV per AZ upon long optogenetic stimulation. This could reflect that possibility. However, given the absence of large structures directly at the ribbon or the AZ membrane that could suggest the compound fusion of several SVs prior or during fusion, we argue against compound MVR release at IHCs. As mentioned above, we added to the discussion (from line 679 onwards).

We wrote:

“This might reflect spontaneous univesicular release (UVR) via a dynamic fusion pore (i.e. ‘kiss and run’, (Ceccarelli et al., 1979), which was suggested previously for IHC ribbon synapses (Chapochnikov et al., 2014; Grabner and Moser, 2018; Huang and Moser, 2018; Takago et al., 2019) and/or and rapid undocking of vesicles (e.g. Dinkelacker et al., 2000; He et al., 2017; Nagy et al., 2004; Smith et al., 1998). In the UVR framework, stimulation by ensuing Ca2+ influx triggers the statistically independent release of several SVs. Coordinated multivesicular release (MVR) has been indicated to occur at hair cell synapses (Glowatzki and Fuchs, 2002; Goutman and Glowatzki, 2007; Li et al., 2009) and retinal ribbon synapses (Hays et al., 2020; Mehta et al., 2013; Singer et al., 2004) during both spontaneous and evoked release. We could not observe structures which might hint towards compound or cumulative fusion, neither at the ribbon nor at the AZ membrane under our experimental conditions. Upon short and long stimulation, RA-SVs as well as docked SVs even showed a slightly reduced size compared to controls. However, since some AZs harbored more than one docked SV per AZ in stimulated conditions, we cannot fully exclude the possibility of coordinated release of few SVs upon depolarization.”

2) The complete lack of docked vesicles in the absence of a stimulus followed by their appearance with a stimulus is a fascinating result. However, since there are no docked vesicles prior to a stimulus, it is really unclear what these docked vesicles represent - clearly not the RRP. Are these vesicles that are fusing or recently fused or are they ones preparing to fuse? It is fine that it is unknown, but it complicates their interpretation that the vesicles are "rapidly replenished". How does one replenish a pool of docked vesicles that didn't exist prior to the stimulus?

In response to the reviewers’ comment, we would like to note that we indeed reported very few docked SVs in wild type IHCs at resting conditions without K+ channel blockers in Chakrabarti et al. EMBO Rep 2018 and in Kroll et al., 2020, JCS. In both studies, a solution without TEA and Cs was used for the experiments (resting solution Chakrabarti: 5 mM KCl, 136.5 mM NaCl, 1 mM MgCl2, 1.3 mM CaCl2, 10 mM HEPES, pH 7.2, 290 mOsmol; control solution Kroll: 5.36 mM KCl, 139.7 mM NaCl, 2 mM CaCl2, 1 mM MgCl2, 0.5 mM MgSO4, 10 mM HEPES, 3.4 mM L-glutamine, and 6.9 mM D-glucose, pH 7.4). Similarly, our current study shows very few docked SVs in the resting condition even in the presence of TEA and Cs. Based on the results presented in ‘Response to reviewers Figure 1’, we assume that the scarcity of docked SVs under control conditions is not due to depolarization induced by a solution containing 20 mM TEA and 1 mM Cs but is rather representative for the physiological resting state of IHC ribbon synapses. Upon 15 min high potassium depolarization, the number of docked SVs only slightly increased as shown in Chakrabarti et al., 2018 and Kroll et al. 2020, but it was not statistically significant. In the current study, we report a similar phenomenon, but here depolarization resulted in a more robust increase in the number of docked SVs.

To compare the data from the previous studies with the current study, we included an additional table 3 (line 676) now in the discussion with all total counts (and average per AZ) of docked SVs.

Author Response

eLife assessment:

This study addresses whether the composition of the microbiota influences the intestinal colonization of encapsulated vs unencapsulated Bacteroides thetaiotaomicron, a resident micro-organism of the colon. This is an important question because factors determining the colonization of gut bacteria remain a critical barrier in translating microbiome research into new bacterial cell-based therapies. To answer the question, the authors develop an innovative method to quantify B. theta population bottlenecks during intestinal colonization in the setting of different microbiota. Their main finding that the colonization defect of an acapsular mutant is dependent on the composition of the microbiota is valuable and this observation suggests that interactions between gut bacteria explains why the mutant has a colonization defect. The evidence supporting this claim is currently insufficient. Additionally, some of the analyses and claims are compromised because the authors do not fully explain their data and the number of animals is sometimes very small.

Thank you for this frank evaluation. Based on the Reviewers’ comments, the points raised have been addressed by improving the writing (apologies for insufficient clarity), and by the addition of data that to a large extent already existed or could be rapidly generated. In particularly the following data has been added:

1. Increase to n>=7 for all fecal time-course experiments

2. Microbiota composition analysis for all mouse lines used

3. Data elucidating mechanisms of SPF microbiome/ host immune mechanisms restriction of acapsular B. theta

4. Short- versus long-term recolonization of germ-free mice with a complete SPF microbiota and assessment of the effect on B. theta colonization probability.

5. Challenge of B. theta monocolonized mice with avirulent Salmonella to disentangle effects of the host inflammatory response from other potential explanations of the observations.

6. Details of all inocula used

7. Resequencing of all barcoded strains

Additionally, we have improved the clarity of the text, particularly the methods section describing mathematical modeling in the main text. Major changes in the text and particularly those replying to reviewers comment have been highlighted here and in the manuscript.

Reviewer #1 (Public Review):

The study addresses an important question - how the composition of the microbiota influences the intestinal colonization of encapsulated vs unencapsulated B. theta, an important commensal organism. To answer the question, the authors develop a refurbished WITS with extended mathematical modeling to quantify B. theta population bottlenecks during intestinal colonization in the setting of different microbiota. Interestingly, they show that the colonization defect of an acapsular mutant is dependent on the composition of the microbiota, suggesting (but not proving) that interactions between gut bacteria, rather than with host immune mechanisms, explains why the mutant has a colonization defect. However, it is fairly difficult to evaluate some of the claims because experimental details are not easy to find and the number of animals is very small. Furthermore, some of the analyses and claims are compromised because the authors do not fully explain their data; for example, leaving out the zero values in Fig. 3 and not integrating the effect of bottlenecks into the resulting model, undermines the claim that the acapsular mutant has a longer in vivo lag phase.

We thank the reviewer for taking time to give this details critique of our work, and apologies that the experimental details were insufficiently explained. This criticism is well taken. Exact inoculum details for experiment are now present in each figure (or as a supplement when multiple inocula are included). Exact microbiome composition analysis for OligoMM12, LCM and SPF microbiota is now included in Figure 2 – Figure supplement 1.

Of course, the models could be expanded to include more factors, but I think this comment is rather based on the data being insufficiently clearly explained by us. There are no “zero values missing” from Fig. 3 – this is visible in the submitted raw data table (excel file Source Data 1), but the points are fully overlapped in the graph shown and therefore not easily discernable from one another. Time-points where no CFU were recovered were plotted at a detection limit of CFU (50 CFU/g) and are included in the curve-fitting. However, on re-examination we noticed that the curve fit was carried out on the raw-data and not the log-normalized data which resulted in over-weighting of the higher values. Re-fitting this data does not change the conclusions but provides a better fit. These experiments have now been repeated such that we now have >=7 animals in each group. This new data is presented in Fig. 3C and D and Fig. 3 Supplement 2.

Limitations:

1) The experiments do not allow clear separation of effects derived from the microbiota composition and those that occur secondary to host development without a microbiota or with a different microbiota. Furthermore, the measured bottlenecks are very similar in LCM and Oligo mice, even though these microbiotas differ in complexity. Oligo-MM12 was originally developed and described to confer resistance to Salmonella colonization, suggesting that it should tighten the bottleneck. Overall, an add-back experiment demonstrating that conventionalizing germ-free mice imparts a similar bottleneck to SPF would strengthen the conclusions.

These are excellent suggestions and have been followed. Additional data is now presented in Figure 2 – figure supplement 8 showing short, versus long-term recolonization of germ-free mice with an SPF microbiota and recovering very similar values of beta, to our standard SPF mouse colony. These data demonstrate a larger total niche size for B. theta at 2 days post-colonization which normalizes by 2 weeks post-colonization. Independent of this, the colonization probability, is already equivalent to that observed in our SPF colony at day 2 post-colonization. Therefore, the mechanisms causing early clonal loss are very rapidly established on colonization of a germ-free mouse with an SPF microbiota. We have additionally demonstrated that SPF mice do not have detectable intestinal antibody titers specific for acapsular B. theta. (Figure 2 – figure supplement 7), such that this is unlikely to be part of the reason why acapsular B. theta struggles to colonize at all in the context of an SPF microbiota. Experiments were also carried to detect bacteriophage capable of inducing lysis of B. theta and acapsular B. theta from SPF mouse cecal content (Figure 2 – figure supplement 7). No lytic phage plaques were observed. However, plaque assays are not sensitive for detection of weakly lytic phage, or phage that may require expression of surface structures that are not induced in vitro. We can therefore conclude that the restrictive activity of the SPF microbiota is a) reconstituted very fast in germ-free mice, b) is very likely not related to the activity of intestinal IgA and c) cannot be attributed to a high abundance of strongly lytic bacteriophage. The simplest explanation is that a large fraction of the restriction is due to metabolic competition with a complex microbiota, but we cannot formally exclude other factors such as antimicrobial peptides or changes in intestinal physiology.

2) It is often difficult to evaluate results because important parameters are not always given. Dose is a critical variable in bottleneck experiments, but it is not clear if total dose changes in Figure 2 or just the WITS dose? Total dose as well as n0 should be depicted in all figures.

We apologized for the lack of clarity in the figures. Have added panels depicting the exact inoculum for each figure legend (or a supplementary figure where many inocula were used). Additionally, the methods section describing how barcoded CFU were calculated has been rewritten and is hopefully now clearer.

3) This is in part a methods paper but the method is not described clearly in the results, with important bits only found in a very difficult supplement. Is there a difference between colonization probability (beta) and inoculum size at which tags start to disappear? Can there be some culture-based validation of "colonization probability" as explained in the mathematics? Can the authors contrast the advantages/disadvantages of this system with other methods (e.g. sequencing-based approaches)? It seems like the numerator in the colonization probability equation has a very limited range (from 0.18-1.8), potentially limiting the sensitivity of this approach.

We apologized for the lack of clarity in the methods. This criticism is well taken, and we have re-written large sections of the methods in the main text to include all relevant detail currently buried in the extensive supplement.

On the question of the colonization probability and the inoculum size, we kept the inoculum size at 107 CFU/ mouse in all experiments (except those in Fig.4, where this is explicitly stated); only changing the fraction of spiked barcoded strains. We verified the accuracy of our barcode recovery rate by serial dilution over 5 logs (new figure added: Figure 1 – figure supplement 1). “The CFU of barcoded strains in the inoculum at which tags start to disappear” is by definition closely related to the colonization probability, as this value (n0) appears in the calculation. Note that this is not the total inoculum size – this is (unless otherwise stated in Fig. 4) kept constant at 107 CFU by diluting the barcoded B. theta with untagged B. theta. Again, this is now better explained in all figure legends and the main text.

We have added an experiment using peak-to-trough ratios in metagenomic sequencing to estimate the B. theta growth rate. This could be usefully employed for wildtype B. theta at a relatively early timepoint post-colonization where growth was rapid. However, this is a metagenomics-based technique that requires the examined strain to be present at an abundance of over 0.1-1% for accurate quantification such that we could not analyze the acapsular B. theta strain in cecum content at the same timepoint. These data have been added (Figure 3 – figure supplement 3). Note that the information gleaned from these techniques is different. PTR reveals relative growth rates at a specific time (if your strain is abundant enough), whereas neutral tagging reveals average population values over quite large time-windows. We believe that both approaches are valuable. A few sentences comparing the approaches have been added to the discussion.

The actual numerator is the fraction of lost tags, which is obtained from the total number of tags used across the experiment (number of mice times the number of tags lost) over the total number of tags (number of mice times the number of tags used). Very low tag recovery (less than one per mouse) starts to stray into very noisy data, while close to zero loss is also associated with a low-information-to-noise ratio. Therefore, the size of this numerator is necessarily constrained by us setting up the experiments to have close to optimal information recovery from the WITS abundance. Robustness of these analyses is provided by the high “n” of between 10 and 17 mice per group.

4) Figure 3 and the associated model is confusing and does not support the idea that a longer lag-phase contributes to the fitness defect of acapsular B.theta in competitive colonization. Figure 3B clearly indicates that in competition acapsular B. theta experiences a restrictive bottleneck, i.e., in competition, less of the initial B. theta population is contributed by the acapsular inoculum. There is no need to appeal to lag-phase defects to explain the role of the capsule in vivo. The model in Figure 3D should depict the acapsular population with less cells after the bottleneck. In fact, the data in Figure 3E-F can be explained by the tighter bottleneck experienced by the acapsular mutant resulting in a smaller acapsular founding population. This idea can be seen in the data: the acapsular mutant shedding actually dips in the first 12-hours. This cannot be discerned in Figure 3E because mice with zero shedding were excluded from the analysis, leaving the data (and conclusion) of this experiment to be extrapolated from a single mouse.

We of course completely agree that this would be a correct conclusion if only the competitive colonization data is taken into account. However, we are also trying to understand the mechanisms at play generating this bottleneck and have investigated a range of hypotheses to explain the results, taking into account all of our data.

Hypothesis 1) Competition is due to increased killing prior to reaching the cecum and commencing growth: Note that the probability of colonization for single B. theta clones is very similar for OligoMM12 mouse single-colonization by the wildtype and acapsular strains. For this hypothesis to be the reason for outcompetition of the acapsular strain, it would be necessary that the presence of wildtype would increase the killing of acapsular B. theta in the stomach or small intestine. The bacteria are at low density at this stage and stomach acid/small intestinal secretions should be similar in all animals. Therefore, this explanation seems highly unlikely

Hypothesis 2) Competition between wildtype and acapsular B. theta occurs at the point of niche competition before commencing growth in the cecum (similar to the proposal of the reviewer). It is possible that the wildtype strain has a competitive advantage in colonizing physical niches (for example proximity to bacteria producing colicins). On the basis of the data, we cannot exclude this hypothesis completely and it is challenging to measure directly. However, from our in vivo growth-curve data we observe a similar delay in CFU arrival in the feces for acapsular B. theta on single colonization as in competition, suggesting that the presence of wildtype (i.e., initial niche competition) is not the cause of this delay. Rather it is an intrinsic property of the acapsular strain in vivo,

Hypothesis 3) Competition between wildtype and acapsular B. theta is mainly attributable to differences in growth kinetics in the gut lumen. To investigate growth kinetics, we carried our time-courses of fecal collection from OligoMM12 mice single-colonized with wildtype or acapsular B. theta, i.e., in a situation where we observe identical colonization probabilities for the two strains. These date, shown now in Figure 3 C and D and Figure 3 – figure supplement 2, show that also without competition, the CFU of acapsular B. theta appear later and with a lower net growth rate than the wildtype. As these single-colonizations do not show a measurable difference between the colonization probability for the two strains, it is not likely that the delayed appearance of acapsular B. theta in feces is due to increased killing (this would be clearly visible in the barcode loss for the single-colonizations). Rather the simplest explanation for this observation is a bona fide lag phase before growth commences in the cecum. Interestingly, using only the lower net growth rate (assumed to be a similar growth rate but increased clearance rate) produces a good fit for our data on both competitive index and colonization probability in competition (Figure 3, figure supplement 5). This is slightly improved by adding in the observed lag-phase (Figure 3). It is very difficult to experimentally manipulate the lag phase in order to directly test how much of an effect this has on our hypothesis and the contribution is therefore carefully described in the new text.

Please note that all data was plotted and used in fitting in Fig 3E, but “zero-shedding” is plotted at a detection limit and overlayed, making it look like only one point was present when in fact several were used. This was clear in the submitted raw data tables. To sure-up these observations we have repeated all time-courses and now have n>=7 mice per group.

5) The conclusions from Figure 4 rely on assumptions not well-supported by the data. In the high fat diet experiment, a lower dose of WITS is required to conclude that the diet has no effect. Furthermore, the authors conclude that Salmonella restricts the B. theta population by causing inflammation, but do not demonstrate inflammation at their timepoint or disprove that the Salmonella population could cause the same effect in the absence of inflammation (through non-inflammatory direct or indirect interactions).

We of course agree that we would expect to see some loss of B. theta in HFD. However, for these experiments the inoculum was ~109 CFUs/100μL dose of untagged strain spiked with approximately 30 CFU of each tagged strain. Decreasing the number of each WITS below 30 CFU leads to very high variation in the starting inocula from mouse-to-mouse which massively complicates the analysis. To clarify this point, we have added in a detection-limit calculation showing that the neutral tagging technique is not very sensitive to population contractions of less than 10-fold, which is likely in line with what would be expected for a high-fat diet feeding in monocolonized mice for a short time-span.

This is a very good observation regarding our Salmonella infection data. We have now added the fecal lipocalin 2 values, as well as a group infected with a ssaV/invG double mutant of S. Typhimurium that does not cause clinical grade inflammation (“avirulent”). This shows 1) that the attenuated S. Typhimurium is causing intestinal inflammation in B. theta colonized mice and 2) that a major fraction of the population bottleneck can be attributed to inflammation. Interestingly, we do observe a slight bottleneck in the group infected with avirulent Salmonella which could be attributable either to direct toxicity/competition of Salmonella with B. theta or to mildly increased intestinal inflammation caused by this strain. As we cannot distinguish these effects, this is carefully discussed in the manuscript.

6) Several of the experiments rely on very few mice/groups.

We have increased the n to over 5 per group in all experiments (most critically those shown in Fig 3, Supplement 5). See figure legends for specific number of mice per experiment.

Reviewer #2 (Public Review):

The goal of this study was to understand population bottlenecks during colonization in the context of different microbial communities. Capsular polysaccharide mutants, diet, and enteric infection were also used paired to short-term monitoring of overall colonization and the levels of specific strains. The major strength of this study is the innovative approach and the significance of the overall research area.

The first major limitation is the lack of clear and novel insight into the biology of B. theta or other gut bacterial species. The title is provocative, but the experiments as is do not definitively show that the microbiota controls the relative fitness of acapsular and wild-type strains or provide any mechanistic insights into why that would be the case. The data on diet and infection seem preliminary. Furthermore, many of the experiments conflict with prior literature (i.e., lack of fitness difference between acapsular and wild-type strain and lack of impact of diet) but satisfying explanations are not provided for the lack of reproducibility.

In line with suggestions from Reviewer 1, the paper has undergone quite extensive re-writing to better explain the data presented and its consequences. Additionally, we now explicitly comment on apparent discrepancies between our reported data and the literature – for example the colonization defect of acapsular B. theta is only published for competitive colonizations, where we also observe a fitness defect so there is no actual conflict. Additionally, we have calculated detection limits for the effect of high-fat diet and demonstrate that a 10-fold reduction in the effective population size would not be robustly detected with the neutral tagging technique such that we are probably just underpowered to detect small effects, and we believe it is important to point out the numerical limits of the technique we present here. Additionally for the Figure 4 experiments, we have added data on colonization/competition with an avirulent Salmonella challenge giving some mechanistic data on the role of inflammation in the B. theta bottleneck.

Another major limitation is the lack of data on the various background gut microbiotas used. eLife is a journal for a broad readership. As such, describing what microbes are in LCM, OligoMM, or SPF groups is important. The authors seem to assume that the gut microbiota will reflect prior studies without measuring it themselves.

All gnotobiotic lines are bred as gnotobiotic colonies in our isolator facility. This is now better explained in the methods section. Additionally, 16S sequencing of all microbiotas used in the paper has been added as Figure 2 – figure supplement 1.

I also did not follow the logic of concluding that any differences between SPF and the two other groups are due to microbial diversity, which is presumably just one of many differences. For example, the authors acknowledge that host immunity may be distinct. It is essential to profile the gut microbiota by 16S rRNA amplicon sequencing in all these experiments and to design experiments that more explicitly test the diversity hypotheses vs. alternatives like differences in the membership of each community or other host phenotypes.

This is an important point. We have carried out a number of experiments to potentially address some issues here.

1) We carried out B. theta colonization experiments in germ-free mice that had been colonized by gavage of SPF feces either 1 day prior to colonization of 2 weeks prior to colonization. While the shorter pre-colonization allowed B. theta to colonize to a higher population density in the cecum, the colonization probability was already reduced to levels observed in our SPF colony in the short pre-colonization. Therefore, the factors limiting B. theta establishment in the cecum are already established 1-2 days post-colonization with an SPF microbiota (Figure 2 - figure supplement 8). 2) We checked for the presence of secretory IgA capable of binding to the surface of live B. theta, compared to a positive control of a mouse orally vaccinated against B. theta. (Fig. 2, Supplement 7) and could find no evidence of specific IgA targeting B. theta in the intestinal lavages of our SPF mouse colony. 3) We isolated bacteriophage from the intestine of SPF mice and used this to infect lawns of B. theta wildtype and acapsular in vitro. We could not detect and plaque-forming phage coming from the intestine of SPF mice (Figure 2 – figure supplement 7).

We can therefore exclude strongly lytic phage and host IgA as dominant driving mechanisms restricting B. theta colonization. It remains possible that rapidly upregulated host factors such as antimicrobial peptide secretion could play a role, but metabolic competition from the microbiota is also a very strong candidate hypothesis. The text regarding these experiments has been slightly rewritten to point out that colonization probability inversely correlates with microbiota complexity, and the mechanisms involved may involve both direct microbe-microbe interactions as well as host factors.

Given the prior work on the importance of capsule for phage, I was surprised that no efforts are taken to monitor phage levels in these experiments. Could B. theta phage be present in SPF mice, explaining the results? Alternatively, is the mucus layer distinct? Both could be readily monitored using established molecular/imaging methods.

See above: no plaque-forming phage could be recovered from the SPF mouse cecum content. The main replicative site that we have studied here, in mice, is the cecum which does not have true mucus layers in the same way as the distal colon and is upstream of the colon so is unlikely to be affected by colon geography. Rather mucus is well mixed with the cecum content and may behave as a dispersed nutrient source. There is for sure a higher availability of mucus in the gnotobiotic mice due to less competition for mucus degradation by other strains. However, this would be challenging to directly link to the B. theta colonization phenotype as Muc2-deficient mice develop intestinal inflammation.

The conclusion that the acapsular strain loses out due to a difference of lag phase seems highly speculative. More work would be needed to ensure that there is no difference in the initial bottleneck; for example, by monitoring the level of this strain in the proximal gut immediately after oral gavage.

This is an excellent suggestion and has been carried out. At 8h post-colonization with a high inoculum (allowing easy detection) there were identical low levels of B. theta in the upper and lower small intestine, but more B. theta wildtype than B. theta acapsular in the cecum and colon, consistent with commencement of growth for B. theta wildtype but not the acapsular strain at this timepoint. We have additionally repeated the single-colonization time-courses using our standard inoculum and can clearly see the delayed detection of acapsular B. theta in feces even in the single-colonization state when no increased bottleneck is observed. This can only be reasonably explained by a bona fide lag-phase extension for acapsular B. theta in vivo. These data also reveal and decreased net growth rate of acapsular B. theta. Interestingly, our model can be quite well-fitted to the data obtained both for competitive index and for colonization probability using only the difference in net growth rate. Adding the (clearly observed) extended lag-phase generates a model that is still consistent with our observations.

Another major limitation of this paper is the reliance on short timepoints (2-3 days post colonization). Data for B. theta levels over 2 weeks or longer is essential to put these values in context. For example, I was surprised that B. theta could invade the gut microbiota of SPF mice at all and wonder if the early time points reflect transient colonization.

It should be noted that “SPF” defines microbiota only on missing pathogens and not on absolute composition. Therefore, the rather efficient B. theta colonization in our SPF colony is likely due to a permissive composition and this is likely to be not at all reproducible between different SPF colonies (a major confounder in reproducibility of mouse experiments between institutions. In contrast the gnotobiotic colonies are highly reproducible). We do consistently see colonization of our SPF colony by wildtype B. theta out to at least 10 days post-inoculation (latest time-point tested) at similar loads to the ones observed in this work, indicating that this is not just transient “flow-through” colonization. Data included below:

For this paper we were very specifically quantifying the early stages of colonization, also because the longer we run the experiments for, the more confounding features of our “neutrality” assumptions appear (e.g., host immunity selecting for evolved/phase-varied clones, within-host evolution of individual clones etc.). For this reason, we have used timepoints of a maximum of 2-3 days.

Finally, the number of mice/group is very low, especially given the novelty of these types of studies and uncertainty about reproducibility. Key experiments should be replicated at least once, ideally with more than n=3/group.

For all barcode quantification experiments we have between 10 and 17 mice per group. Experiments for the in vivo time-courses of colonization have been expanded to an “n” of at least 7 per group.

Author Response

Reviewer #1 (Public Review):

This is a well-executed study using cutting-edge proteomics analysis to characterize muscle tissue from a genetically diverse mouse population. The use of only females in the study is a serious limitation that the authors acknowledge. The statistical methods, including protein quantification, QTL mapping, and trait correlation analysis are appropriate and include corrections for multiple testing. One concern is that missense variants, if they occur in peptides used to quantify proteins, could lead to false-positive signatures of low abundance (see lines 123-127). The experimental validation and deep dive into UFMylation provide some confidence in the reliability of other associations that can be mined from these data. The authors have provided a web-based tool for exploring the data.

We thank the reviewer for these very positive comments and for reviewing the manuscript.

We agree the quantification of peptides containing missense variants could confound quantification at the protein level. This is an important consideration when there are only a few peptides identified for a specific protein. However, in our data the average number of peptides used to quantify the 14 proteins containing missense-associated pQTLs was ~68 peptides/protein (lowest was 5 peptides for FGB and highest 703 peptides for NEB).

In the case of EPHX1, we quantified 15 peptides (Figure R1A). We identified a peptide adjacent to R338 spanning amino acids 339-347. As such, mutation of R338C would prevent trypsin from cleavage resulting in the missense peptide not being identified and may lead to false-positive signatures of low abundance as suggested by the reviewer. To investigate this, we re-quantified EPHX1 relative protein abundance with or without the peptide spanning 339-347 for each genotype (Figure R1B). This made little difference to protein quantification and EPHX1 abundance was still significantly lower following mutation of R338C (AA genotype). In fact, quantification at the peptide-level revealed 12 out of the remaining 14 peptides were also significantly lower in AA genotype (data not shown).

Although we agree this a very important consideration, we are mindful of the length of the article and feel including these data would not significantly improve the manuscript. We therefore request to not include these data as it would detract from the main findings of the paper focused on phenotypic associations and validation of UFMylation as a regulator of muscle function.

Figure 1R. (A) Identified peptides from EPHX1 mapped onto primary amino acid sequence highlighting the missense mutation induced by SNP rs32746574 that was associated to EPHX1 protein levels by pQTL analysis. (B) Relative quantification of EPHX1 between the two genotypes of SNP rs32746574 with and without the peptide neighboring the missense mutation (amino acids 339-347) (**p<0.001, students t-test)

Author Response

Reviewer #1 (Public Review):

Building upon the previous evidence of activation of auditory cortex VIP interneurons in response to non-classical stimuli like reward and punishment, Szadai et al., extended the investigation to multiple cortical regions. Use of three-dimensional acousto-optical two-photon microscopy along with the 3D chessboard scanning method allowed high-speed signal acquisition from numerous VIP interneurons in a large brain volume. Additionally, activity of VIP interneurons in deep cortical regions was obtained using fiber photometry. With the help of these two imaging methods authors were able to extract and analyze the VIP cell signal from different cortical regions. Study of VIP interneuron activity during an auditory go-no-go task revealed that more than half of recorded cortical VIP interneurons were responding to both reward and punishment with high reliability. Fiber photometry data revealed similar observations; however, the temporal dynamics of reinforcement stimuli-related response in mPFC was slower than in the auditory cortex. The authors performed detailed analysis of individual cell activity dynamics, which revealed five categories of VIP cells based on their temporal profiles. Further, animals with higher performance on the discrimination task showed stronger VIP responses to 'go trials' possibly suggesting the role of VIP interneurons in discrimination learning. Authors found that reinforcement related response of VIP interneurons in visual cortex was not correlated with their sensory tuning, unveiling an interesting idea that VIP interneurons take part in both local as well as global processing. These observations bring attention to the possible involvement of VIP interneurons in reinforcement stimuli-associated global signaling that would regulate local connectivity and information processing leading to learning.

The state-of-the-art imaging technique allowed authors to succeed in imaging VIP interneurons from several cortical regions. Advanced analyses revealed the nuances, similarities and differences in the VIP activity trend in various regions. The conclusions about reinforcement stimuli related activity of VIP interneurons made by the authors are well supported by the results obtained, however some claims and interpretations require more attention and clarification.

We thank Reviewer #1 for the positive general comments.

Reviewer #2 (Public Review):

In recent years the activity of cortical VIP+ interneurons in relation to learning and sensory processing has raised great interest and has been intensely investigated. The ability of VIP+ interneurons in the auditory cortex to respond to both reward and punishment was already reported a few years ago by some of the authors (Pi et al., 2013, Nature). However, this work importantly adds to their previous study demonstrating a largely similar and synchronous response of a large fraction of these interneurons across the neocortex to salient stimuli of different valence during the performance of an auditory discrimination task.

An additional strength of this study is the analysis and identification of the general pattern of VIP+ interneuron responses associated to specific behaviors in the different layers of the neocortex depth.

Interestingly, the authors also identified using cluster analysis 5 different classes of VIP+ interneurons, based on the dynamic of their responses, that were unequally distributed in distinct cortical areas.

This is a well performed study that took advantage of a cutting-edge imaging approach with high recording speed and good signal-to-noise ratio. Experiments are well performed and the data are properly analyzed and nicely illustrated. However, one shortcoming of this paper, in my opinion, is the "case report" structure of the data. Essentially for each neocortical area the activity of VIP+ interneurons was analyzed only in one animal. This limits the assessment of the stability of the response/recruitment of these interneurons. I appreciate the high number of recorded VIP+ interneurons per area/animal and I do understand that it would be excessively laborious to perform 3D random-access two-photon microscopy in several mice for each cortical area. On the other hand, it would be important to have some knowledge of the general variability of the responses of these neurons among animals.

In conclusion, despite the findings described in this manuscript being generally sound, additional experiments are recommended to further substantiate the conclusions.

Thank you for pointing out this potential misunderstanding. Although we mentioned the number of animals the recordings were obtained from (n=22 total), we repeated this multiple times to alleviate the potential confusion. The data recorded with the 2-photon microscope are from 16 animals, and fiber photometry was performed on a separate 6 animals. Each animal was recorded in one (14 mice) or two areas (8 mice, 2 AOD, 6 photometry). We aimed to acquire data from at least 3 recordings per area (4 in the primary somatosensory cortex, 6 in the primary and secondary motor cortices, 4 in the lateral and medial parietal cortices, 3 in the primary visual cortices, 6 in the auditory and medial prefrontal cortices). In the revised manuscript this information can be found at the beginning of the results section and in the figure legends:

“To probe the behavioral function of VIP interneurons, we trained head-fixed mice (n=22 in total, n=16 for 2-photon microscopy and n=6 for fiber photometry) on a simple auditory discrimination task (Figure 1A).”

“Among the 811 neurons imaged in 18 imaging sessions from 16 mice,”

“Ca2+ responses of individual VIP interneurons recorded separately from 18 different cortical regions from 16 mice using fast 3D AO imaging were averaged for Hit (thick green), FA (thick red), Miss (dark blue), and CR (light blue). Fiber photometry data were recorded simultaneously from mPFC and ACx regions and are shown in gray boxes. Functional map (Kirkcaldie, 2012) used with the permission of the author. Speaker symbols represent the average time of tone onset, and gray triangles mark the reinforcement onset for Hit and FA. Averages of Miss and CR trials were aligned according to the expected reinforcement delivery calculated on the basis of the average reaction time. mPFC: medial prefrontal cortex (n=6 mice), ACx: auditory cortex (n=6), S1Hl/S1Tr/S1Bf/S1Sh: primary somatosensory cortex, hindlimb/trunk/barrel field/shoulder region (n=4), M1/M2: primary/secondary motor cortex (n=6), Mpta/Lpta: medial/lateral parietal cortex (n=4), V1: primary visual cortex (n=3).”

“This approach allowed us to simultaneously measure bulk calcium-dependent signals from VIP interneurons located in the right medial prefrontal (mPFC) and left auditory cortices (ACx) by implanting two 400 µm optical fibers at these locations (n=6 sessions from n=6 mice, Figure 1–figure supplement 1C).”

“Raster plot of the trial-to-trial activation of the responsive VIP neurons in Hit and FA trials during the two-photon imaging sessions (n=18 sessions, n=16 mice, n=746 cells).”

Subregional labels, for example on Figure 2, should be considered as additional information to orient the readers, even if they were very precisely defined on the basis of the coordinates. All analyses considering regional differences were conducted on the level of the main functional areas of the dorsal cortex (motor, somatosensory, parietal, and visual). Despite some location-dependent heterogeneity in the late response phase (Figures 2G and H), even these main dorsal cortical regions were all similar from the perspective of responsiveness to reinforcers and auditory cues.

Reviewer #3 (Public Review):

In this study Szadai et al. show reliable, relatively synchronous activation of VIP neurons across different areas of dorsal cortex in response to reward and punishment of mice performing an auditory discrimination task. The authors use both a relatively fast 2 photon imaging, as well as fiber photometry for some deeper areas. They cluster neurons according to their temporal response profiles and show that these profiles differ across areas and cortical depths. Task performance, running behavior and arousal are all related to VIP response magnitude, as has been previously shown.

Methodologically, this paper is strong: the described imaging technique allows for fairly fast sampling rates, they sample VIP cells from many different areas and the analyses are sophisticated and touch on the most relevant points. The figures are of high quality.

However, as the manuscript is now, the presentation could be clearer, the methods more complete and it is not clear whether their conclusions are entirely supported by the data.

The main issue is that reinforcement and arousal are hard to distinguish in this study. It is well known that VIP activity is correlated with arousal. And it is fairly clear that the reinforcement they use in this study - air puffs to the eye, as well as water rewards - cause arousal. It is possible that the reinforcer responses they observe in VIP neurons throughout all areas merely reflect the increases in arousal caused by these behaviorally salient events. They do discuss this caveat (albeit not fully convincingly) and in their abstract even state that the arousal state was not predictive of reinforcer responses. However their data clearly shows the tight relationship of the VIP reinforcer responses to both arousal (as measured by pupil diameter), as well as running speed of the animal. Both of these variables are well known to be tightly coupled to VIP activity.

Although barely mentioned, the authors do appear to sometimes present uncued reward (Figure S2F). If responses were noticeably different from the same events in the task context (as actual reinforcers) this could at least hint towards the reinforcement signal being distinct from mere arousal. However, this data is only mentioned in one supplementary figure in a different context (comparison with PV cells) and neither directly compared to cued reward, nor is this discussed at all. Were uncued air puffs also presented? How do the responses compare to cued air puffs/punishment?

Our original approach to distinguish between reinforcement- and arousal-related responses aimed:

1) to show that VIP cells with both low and high correlation coefficients with arousal produce large signals upon reinforcement presentation (Figure 3B),

2) the high differences of low and high arousal changes were reflected in a limited way in the VIP activity (Figures 3C and D): as highlighted in Figure R1, where we also added bars to show ∆P/P in high and low pupil change conditions, the difference in ∆P/P is ~5-fold, while it is only ~1.5-fold for ∆F/F. This disproportionality suggests that a large part of the signal below the dashed blue line is independent of arousal. We have added these modifications to the new version of Figure 3 for clarity.

Figure R1 = Figure 3C-D with modification. Comparison of pupil changes and corresponding calcium averages.

We collected further evidence to support our claims. In Figure 3–figure supplement 2 we depicted Hit and FA trials in which the reinforcement didn’t elevate the arousal level any further. Many of these trials were associated with locomotion prior to the reinforcement, but it was also common that the animals remained still during the whole trial. Trials with increased locomotion upon reinforcement presentation were excluded. Reinforcement-related calcium signals were still present under these conditions, indicating that these signals are not simple reflections of arousal. Moreover, we estimate the distinct contributions of arousal, locomotion, and reinforcers in Figure 3–figure supplement 2D in a systematic way with a generalized linear model. This model also confirmed our view about the reinforcement-related coding.

We now say in the results:

“Finally, to assess the motor- and reinforcement-related contributions to VIP interneuronal activity, we built a generalized linear model using the behavior and imaging data of the SS and Mtr recordings (Figure 3–figure supplement 2D, n=3 mice). This model was able to explain 18.8 ± 11.1% of the variance of the VIP population calcium signal, and highlighted that arousal was the best predictor, followed by reward, punishment, locomotion velocity, and auditory cue (weights = 0.055, 0.031, 0.028, 0.020, 0.018 respectively; all predictors, except the auditory cue in the case of one animal, contributed significantly, p<0.001). These observations indicate that running and arousal changes alone cannot fully explain the recruitment of VIP interneurons by reinforcers.”

We apologize for not describing the rational and the result from the uncued reward experiments. Briefly, while recording reinforcement related signals in auditory cortex in our task, we realized that the cue delivery, and the resulting purely sensory response could alter the measurement of the reward-related responses. Hence, in order to disentangle the reward and sensory-related responses, we presented the animals with simple, uncued reward and observed a similar and robust recruitment of VIP interneurons. Based on the same rational, we made similar measurement for PV neurons.

We now say in the results:

“We did not further analyze the FA responses in auditory cortex as those responses also had a sensory component linked to the white noise-like sound created by the air puff delivery. Because the cue delivery could prove as a confound to measure reward-mediated responses from VIP interneurons in auditory cortex (see also methods), we delivered random reward in separate sessions. Water droplets delivery recruited VIP interneurons in both auditory and medial prefrontal cortex in a similar fashion as water delivery during the discrimination task (Figure 2–figure supplement 1G). Like our single cell results, PV-expressing neuronal population in ACx did not show any significant change in activity upon similar random reward delivery (Figure 2–figure supplement 1G).”

Regarding the difference between cued and uncued responses, we definitely agree with the reviewer that it is an important point. The goal of this manuscript is however to study how reward and punishment are being represented by VIP interneurons in cortex.

The imaging method appears well suited for their task, however the improvements listed in table S1 make the method appear far superior to existing methods in many aspects. Published or preprinted papers with 2 photon imaging of VIP populations (eg. from Scanziani lab (Keller et al.), Carandini lab (Dipoppa et al.), deVries lab (Millman et al.), Adesnik lab (Mossing et al.), which use the much more common resonant scanning, seem to be able to image 4-7 layers at 4-8Hz with a good enough SNR and potentially bigger neuronal yield of approximately 100-200 VIP cells, depending on the field of view. While not every single cell in a volume would be captured by these studies, the only main advantage of the here-used technique appears to be the superior temporal resolution.

We thank the reviewer for the positive comment and we agree that interpretation must be improved. We agree that the imaging methods in the papers listed above have good SNR and were proper to address the scientific questions that had arisen. As the reviewer points out, 3D-AOD imaging allows fast 3D measurement that cannot be achieved otherwise. We used these advantages to address the critical question of layer specificity in the response of VIP interneurons to reinforcer presentation (Figure 2–figure supplement 1F, but see also the new Figure 1–figure supplement 1B). Regarding the comparison and quantification of the factual advantages of AOD microscopy over other imaging methods, the reviewer and readers can refer to the methods section (3D AO microscopy), Table S1 and Szalay et al., 2016. We agree with the reviewer that one of the main advantages is the superior temporal resolution. The second main advantage is the improved SNR. This originates from the fact that the entire measurement time is spent on regions of interest; measurement of unnecessary background areas is not required. More specifically, SNR is improved even in the case of 2D imaging by the factor of:

((area of the entire frame )/(area of the recorded VIP cells))^0.5

which is about (100)0.5=10 as VIP interneurons represent about 1% of the brain. We used this second advantage of AO scanning when we determined the activation ratio (e.g., see Figure 2D).

As the resolution of single or a few action potentials is challenging in behaving mice labelled with the GCaMP6 sensor, any improvement in SNR will improve the detection threshold. The higher SNR achieved here improved the detection threshold, which also explains the relatively high activation ratio in our work.

In the case of asynchronous activity patterns, there is negligible contribution of individual small neuropil structures to somatic activities because of the relatively high volume-ratio of a soma and a given small neuropil structure: this minimizes the error during ∆F/F calculation of somatic responses. However, reinforcement, arousal, and running can generate highly synchronous neuronal activities which can synchronize neuropil activity around a given soma and, therefore, effectively and systematically modulating the somatic ∆F/F responses. To avoid this error, we used a high NA objective with proper neuropil resolution and combined it with motion correction. The use of the high NA also decreased the total scanning volume to about 689 µm × 639 µm × 580 µm and, therefore, it limited the maximum number of VIP cells which could be recorded. It is also possible to use a low-NA objective with a much higher FOV and scanning volume and record over 1000 VIP cells, but the extension of the PSF along the z dimension is inversely and quadratically proportional to the NA of the objective, therefore neuropil resolution will be at least partially lost. In summary, using the high-NA Olympus objective we maximized the 2P resolution which, in combination with off-line motion artifact elimination, allowed precise recording of somatic signals without any neuropil contamination: this provided correct activation ratio values.

Even though this is not mentioned at all, it certainly appears possible, that the accousto-optical scanning emits audible noise. In this case it would be good to know the frequency range and level of this background noise, whether there are auditory responses to the scanning itself and if it interferes with the performance of the animals in the auditory task in any way. If this is not the case, this should probably simply be mentioned for non-experts.

While the name of the acousto-optical deflectors seems to refer to “acoustic noise”, these devices are driven in the range of 55-120 MHz, which is 3 orders of magnitude higher frequency than the hearing threshold of animals: mice don’t hear them. Moreover, we developed water-cooled AODs ten years ago which means that ventilators are also not required, therefore AOD-based scanning can be used with zero noise emission. In contrast, galvo, resonant, and piezo scanning work in the kHz frequency range, which is in the middle of the hearing range of mice. Moreover, these technologies can’t be used in a vacuum and the scanner is just a few tens of centimeters away from the mice, which means that acoustic noise can’t be canceled but can only be partially suppressed with white noise. We thank the reviewer for the helpful comment and have added one sentence about the absence of acoustic noise during acousto-optical scanning:

“The deflectors are driven in the 55-120 MHz frequency range, therefore the noise emitted does not interfere with the auditory cues, as mice can’t hear it. This, in combination with the water cooling of the deflectors, makes the AOD-based scanning the quietest technology for in-vivo imaging.”

The authors show a strong correlation between task performance (hit rate) and the response to the auditory cue on hit trials. Was there any other significant correlations of VIP cells' responses to other trial types? Was reinforcer response correlated to behavioral variables at all?

We have not found any remarkable correlations between VIP cell activity and behavioral variables except the one mentioned above.

For example, we tested discrimination rate (hit rate/FA rate) correlation with ∆F/Ftone in Hit trials, but this was not significant (R2=0.03, F=0.49, p=0.69), just like Hit rate vs. ∆F/Ftone in FA trials (R2=0.19, F=3.8, p=0.07), and discrimination rate vs. ∆F/Ftone in FA trials (R2=0.07, F=1.1, p=0.31).

Author Response

Reviewer #1 (Public Review):

This study used GWAS and RNAseq data of TCGA to show a link between telomere length and lung cancer. Authors identified novel susceptibility loci that are associated with lung adenocarcinoma risk. They showed that longer telomeres were associated with being a female nonsmoker and early-stage cancer with a signature of cell proliferation, genome stability, and telomerase activity.

Major comments:

1) It is not clear how are the signatures captured by PC2 specific for lung adenocarcinoma compared to other lung subtypes. In other words, why is the association between long telomeres specific to lung adenocarcinoma?

We thank the reviewer for raising this point (similarly mentioned by reviewer #2). Indeed, it is unclear why genetically predicted LTL appears more relevant to lung adenocarcinoma. We have used LASSO approach to select important features of PC2 in lung adenocarcinoma and inferred PC2 in lung squamous cell carcinomas tumours to better explore the differences between histological subtypes. The new results are presented in Figure 5, as well as being described in the methods and results sections. In addition, we have expanded upon this point in the discussion with the following paragraph (page 11, lines 229-248):

‘An explanation for why long LTL was associated with increased risk of lung cancer might be that individuals with longer telomeres have lower rates of telomere attrition compared to individuals with shorter telomeres. Given a very large population of histologically normal cells, even a very small difference in telomere attrition would change the probability that a given cell is able to escape the telomere-mediated cell death pathways (24). Such inter-individual differences could suffice to explain the modest lung cancer risk observed in our MR analyses. However, it is not clear why longer TL would be more relevant to lung adenocarcinoma compared to other lung cancer subtypes. A suggestion may come from our observation that longer LTL is related to genomic stable lung tumours (such as lung adenocarcinomas in never smokers and tumours with lower proliferation rates) but not genomic unstable lung tumours (such as heavy smoking related, highly proliferating lung squamous carcinomas). One possible hypothesis is that histologic normal cells exposed to highly genotoxic compounds, such as tobacco smoking, might require an intrinsic activation of telomere length maintenance at early steps of carcinogenesis that would allow them to survival, and therefore, genetic differences in telomere length are less relevant in these cells. By contrast, in more genomic stable lung tumours, where TL attrition rate is more modest, the hypothesis related to differences in TL length may be more relevant and potentially explaining the heterogeneity in genetic effects between lung tumours (Figure 2). Alternately, we also note that the cell of origin may also differ, with lung adenocarcinoma is postulated to be mostly derived from alveolar type 2 cells, the squamous cell carcinoma is from bronchiolar epithelium cells (19), possibly suggesting that LTL might be more relevant to the former.

2) The manuscript is lacking specific comparisons of gene expression changes across lung cancer subtypes for identified genes such as telomerase etc since all the data is presented as associations embedded within PCs.

The genes associated with telomere maintenance such as TERT and TERC are very low expressed in these tumours (Barthel et al NG 2017). In this context, no sample has more than 5 normalised read counts by RNA-sequencing for TERT within TCGA lung cohorts (TCGA-LUSC, TCGA-LUAD). As such we have not explored the difference by individual telomere related genes. Nevertheless, we have explored an inferred telomerase activity gene signature, developed by Barthel et al and we did explore this in the context of lung adenocarcinoma tumours. We have added a note in the result section to inform the reader regarding why we did not directly test TERT/TERC expression (page 9, lines 184-187).

3) It is not clear how novel are the findings given that most of these observations have been made previously i.e. the genetic component of the association between telomere length and cancer.

Others, including ourselves, have studied TL and lung cancer. We have built on that on the most updated TL genetic instrument and the largest lung cancer study available. In addition, we provided insights into the possible mechanisms in which telomere length might affect lung adenocarcinoma development. Using colocalisation analyses, we reported novel shared genetic loci between telomere length and lung adenocarcinoma (MPHOSPH6, PRPF6, and POLI), such genes/loci that have not previously linked to lung adenocarcinoma susceptibility. For MPHOSPH6 locus, we showed that the risk allele of rs2303262 (missense variant annotated for MPHOSPH6 gene) colocalized with increased lung adenocarcinoma risk, lower lung function (FEV1 and FVC), and increased MPHOSPH6 gene expression in lung, as highlighted in the discussion section of the revised manuscript.

In addition, we have used a PRS analysis to identify a gene expression component associated with genetically predicted telomere length in lung adenocarcinoma but not in squamous cell carcinoma subtype. The aspect of this gene expression component associated with longer telomere length are also associated with molecular characteristics related to genome stability (lower accumulation of DNA damage, copy number alterations, and lower proliferation rates), being female, early-stage tumours, and never smokers, which is an interesting but not completely understood lung cancer strata. As far as we are aware, this is the first time an association between a PRS related to an etiological factor, such as telomere length and a particular expression component in the tumour.

We have adjusted the discussion further highlight the novel aspects in the discussion section of the revised manuscript.

Reviewer #2 (Public Review):

The manuscript of Penha et al performs genetic correlation, Mendelian randomization (MR), and colocalization studies to determine the role of genetically determined leukocyte telomere length (LTL) and susceptibility to lung cancer. They develop an instrument from the most recent published association of LTL (Codd et al), which here is based on n=144 genetic variants, and the largest association study of lung cancer (including ~29K cases and ~56K controls). They observed no significant genetic correlation between LTL and lung cancer, in MR they observed a strong association that persisted after accounting for smoking status. They performed colocalization to identify a subset of loci where LTL and lung cancer risk coincided, mainly around TERT but also other loci. They also utilized RNA-Seq data from TCGA lung cancer adenocarcinoma, noting that a particular gene expression profile (identified by a PC analysis) seemed to correlate with LTL. This expression component was associated with some additional patient characteristics, genome stability, and telomerase activity.

In general, most of the MR analysis was performed reasonably (with some suggestions and comments below), it seems that most of this has been performed, and the major observations were made in previous work. That said, the instrument is better powered and some sub-analyses are performed, so adds further robustness to this observation. While perhaps beyond the scope here, the mechanism of why longer LTL is associated with (lung) cancer seems like one of the key observations and mechanistically interesting but nothing is added to the discussion on this point to clarify or refute previous speculations listed in the discussion mentioned here (or in other work they cite).

Some broad comments:

1) The observations that lung adenocarcinoma carries the lion's share of risk from LTL (relative to other cancer subtypes) could be interesting but is not particularly highlighted. This could potentially be explored or discussed in more detail. Are there specific aspects of the biology of the substrata that could explain this (or lead to testable hypotheses?)

We thank the reviewer for these comments. A similar point was raised by reviewer #1. Please see our response above, as well as the additional analysis described in Figure 5 that considers the differences by histological subtype.

2) Given that LTL is genetically correlated (and MR evidence suggests also possibly causal evidence in some cases) across a range of traits (e.g., adiposity) that may also associate with lung cancer, a larger genetic correlation analysis might be in order, followed by a larger set of multivariable MR (MVMR) beyond smoking as a risk factor. Basically, can the observed relationship be explained by another trait (beyond smoking)? For example, there is previous MR literature on adiposity measures, for example (BMI, WHR, or WHRadjBMI) and telomere length, plus literature on adiposity with lung cancer; furthermore, smoking with BMI. A bit more comprehensive set of MVMR analyses within this space would elevate the significance and interpretation compared to previous literature.

Indeed, there are important effects related to BMI and lung cancer (Zhou et al., 2021. Doi:10.1002/ijc.33292; Mariosa et al., 2022. Doi: 10.1093/jnci/djac061). We have tested the potential for influence on our finding using MVMR, modelling LTL and BMI using a BMI genetic instrument of 755 SNPs obtained from UKBB (feature code: ukb-b-19953). This multivariate approach did not result any meaningful changes in the associations between LTL and lung cancer risk.

3) In the initial LTL paper, the authors constructed an IV for MR analyses, which appears different than what the authors selected here. For example, Codd et al. proposed an n=130 SNP instrument from their n=193 sentinel variants, after filtering for LD (n=193 >>> n=147) and then for multi-trait association (n=147 >> n=130). I don't think this will fundamentally change the author's result, but the authors may want to confirm robustness to slightly different instrument selection procedures or explain why they favor their approach over the previous one.

We appreciate the reviewer’s suggestion. Our study is designed for a Mendelian Randomization framework and chose to be conservative in the construction of our instrumental variable (IV). We therefore applied more stringent filters to the LTL variants relative to Codd et al’s approach. We applied a wider LD window (10MB vs. 1MB) centered around the LTL variants that were significant at genome-wide level (p<5e-08) and we restricted our analyses to biallelic common SNPs (MAF>1% and r2<0.01 in European population from 1000 genomes). Nevertheless, the LTL genetic instrument based on our study (144 LTL variants) is highly correlated with the PRS based on the 130 variants described by Codd et al. (correlation estimate=0.78, p<2.2e-16). The MR analyses based on the 130 LTL instrument described by Codd et al showed similar results to our study.

4) Colocalization analysis suggests that a /subset/ of LTL signals map onto lung cancer signals. Does this mean that the MR relationships are driven entirely by this small subset, or is there evidence (polygenic) from other loci? Rather than do a "leave one out" the authors could stratify their instrument into "coloc +ve / coloc -ve" and redo the MR analyses.

Mainly here, the goal is to interpret if the subset of signals at the top (looks like n=14, the bump of non-trivial PP4 > 0.6, say) which map predominantly to TERT, TERC, and OBFC1 explain the observed effect here. I.e., it is biology around these specific mechanisms or generally LTL (polygenicity) but exemplified by extreme examples (TERT, etc.). I appreciate that statistical power is a consideration to keep in mind with interpretation.

We appreciate the reviewer’s comment and, indeed, we considered this idea. However, the analytical approach used the lung cancer GWAS to identify variants that colocalise. To validate this hypothesis that a subset of colocalised variants would be driving all the MR associations, we would need an independent lung cancer case control study to act as an out-of-sample validation set. This is not available to us at this point. Nevertheless, we slightly re-worded the discussion to highlight that the colocalised loci tend to be near genes related to telomere length biology and are also exploring the colocalisation approach to select variants for PRS analysis elsewhere.

Author Response

Reviewer #1 (Public Review):

The authors examine the role of the K700E mutation in the Sf3B1 splicing factor in PDAC and report that this Sf3B1 mutation promotes PDAC by decreasing sensitivity to TGF-b resulting in decreased EMT and decreased apoptosis as a result. They propose that the Sf3b1 K700E mutant causes decreased expression of Map3K7, a known mediator of TGF-β signaling and also known to be alternately spliced in other systems by the Sf3b1 K700E mutation. The role of splicing defects in cancer is relatively understudied and could identify novel targets for therapeutic intervention so this work is of potential significance. However, the data is over-interpreted in many instances and it is not clear the authors can make the claims they do based on the data shown. In particular, the data showing that decreased Map3k7 underlies the effects of the Sf3b1K700E mutant is very weak. Does over-expression of Map3k7 promote the EMT signature and induce apoptosis? Do the Map3k7 expressing organoids form tumors more effectively when transplanted into mice? Also, the novelty of the work is a concern since aberrant Map3k7 splicing due to SF3B1 mutation was seen previously in other systems. The authors also do not address the apparent conundrum of Sf3b1 K700E mutation promoting tumorigenesis despite there being less EMT which is also required for progression to metastasis in PDAC.

Major Concerns.

1) The analysis of the effect of Sf3b1K700E expression on normal pancreas and on PanINs in KC mice and PDAC in KPC mice is superficial and could be enhanced by staining for amylase, cytokeratin-19 and insulin. In particular, the data quantified in figure 1L should be accompanied by staining for CK19, Mucin5AC or some other marker of ductal transformation. Also, are any effects seen at older ages in normal mice?

We performed staining of normal and cancerous mouse pancreata using Ck19, MUC5AC and b-amylase antibodies. In line with our hypothesis that Sf3b1K700E mainly plays a role in early stages of PDAC formation, we observed significant differences in CK19 (increase), MUC5AC (increase) and b-amylase (decrease) expression in early stage KPC-Sf3b1K700E vs. KPC tumors (Fig. 1G-J), but not in late stage tumors (see Figure 1-figure supplement 1F-I). In addition, no differences were observed in normal mice. We added these data to the revised manuscript (see Figure 1-figure supplement 1D, E).

2) The invasion assays used are limited and should be complemented by more routine quantification of cell migration and invasion including such assays as a scratch assay, Boyden chamber assays and use of the IncuCyte system to quantify. As it stands the image in Figure 3B is difficult to interpret since it is very poorly described in the figure legend. Additional evidence is needed to make the claims made by the authors.

During the revisions we performed wound healing/scratch assays using PANC-1 cells with inducible SF3B1 WT/K700E overexpression. We observed a significant difference in migratory capacity between SF3B1 WT- and SF3B1 K700E overexpressing cells stimulated with TGF-β. We added this data to the revised manuscript (Fig. 2I, J). We also describe the abovementioned figure 3B in more detail (revised manuscript Fig. 2G, H; line 759-767).

3) The authors should show the actual CC3 staining quantified in Suppl. Figure 2G.

We added a representative image of CC3 staining (see Figure 3-figure supplement 1A) for the quantified data (see Figure 3-figure supplement 1B in the revised manuscript).

4) The graph in Figure 3L should show WT and Sf3b1K700E expressing organoids number both with and without TGF-b.

Since without TGF-b supplementation organoids have to be split in a 1:3 ratio every 5 days, we could not follow the same passaging regimen as in experiments with TGF-b supplementation (split in a 1:2 ratio every 20 days, Fig. 3I). However, we assessed the organoid number grown in control medium without TGF-b for 4 passages (20 days) in a 1:3 ratio, and observe no difference in organoid number in WT and Sf3b1K700E expressing organoids (Author response image 1). In the revised manuscript we show with a highly quantitative read-out (CellTiterGlo) that Sf3b1K700E expressing organoids do not grow faster than Sf3b1 WT expressing organoids in absence of TGF-β (see Figure 3-figure supplement 1E). Taken together, we can exclude that Sf3b1K700E organoids outgrow Sf3b1 WT organoids in medium with TGF-β supplementation because they generally have a growth advantage.

Author response image 1.

Author response image 1. WT and Sf3b1K700E expressing organoids were cultured without TGF-β supplementation. Organoids were split in a 1:3 ratio every 5 days. Data points show organoid number before splitting, assessed for 4 passages.

Reviewer #2 (Public Review):

The manuscript has several areas of strength; it functionally explores a mutant that is detected in a portion of pancreatic cancers; it conducts mechanistic investigation and it uses human cell lines to validate the findings based on mouse models. Some areas for improvement are described below.

1) TGF-b is known to act as a tumor suppressor early in carcinogenesis, and as a tumor promoter later. The authors should extend their analysis of mouse models to determine whether the effect of SF3B1K700E is specific to promoting initiation (e.g. more, early acinar ductal metaplasia) or faster progression of PanINs following their formation. Another way to address this could be acinar cultures, to determine whether an increased propensity to ADM exists.

To further detangle the effect KPC-Sf3b1K700E with respect to tumor progression, we analyzed our autochthonous model at an early and late stage of tumor progression: Histological examination at 5 weeks revealed increased propensity to ADM (see Figure 1-figure supplement 1J, K), PanIN formation (shown by Muc5a1 and CK19 IF stainings, Fig. 1G, I, J) and a concomitant decrease of acinar cells (shown by b-amylase staining) in KPC-Sf3b1K700E vs. KPC tumors (Fig. 1G, H). Analyzing tumors at 9 weeks of age did not show differences in CK19 staining and fibrosis. We added these data to the revised manuscript (see Figure 1-figure supplement 1F-I).

2) Given that the effect of SF3B1K700E expression is more prominent in KC mice, rather than in KPC mice, the authors should explain the rationale for using the latter for RNA sequencing.

In KC mice, pre-invasive PanIN lesions only infrequently progress to PDAC (spontaneous progression, see Gabriel et al., Pancreatology, 2020 ). Therefore, it would have been difficult to collect enough material for cell sorting and downstream RNA sequencing of tumor cells. The KPC mouse model develops PDAC with a 100% penetrance, allowing the collection of sufficient material.

3) Given that this mutation is found in about 3% of human pancreatic cancer, it would be interesting to know whether these tumors have any unique feature, and specifically any characteristic that could be harnessed therapeutically.

Unfortunately, the size of published datasets is too small for a meaningful differential gene expression analysis of SF3B1-WT vs. SF3B1-K700E PDAC tumors (due to the low occurrence of SF3B1-K700E PDAC). However, harnessing the K700E mutation therapeutically by increasing missplicing through splicing inhibitors has previously been suggested, and it was shown that SF3B1-K700E mutated cancer cells are more prone to apoptosis when splicing is chemically targeted than SF3B1-WT cells. We tested a similar approach in murine pre-cancerous organoids, demonstrating that Sf3b1-WT organoids show higher survival than Sf3b1K700E expressing organoids when treated with the splicing-inhibitor Pladienolide B (Author response image 2). However, since this concept is not novel and not within the topic of our manuscript, we would prefer to not integrate this data into our manuscript.

Author response image 2.

Author response image 2. 33 nM of the splicing inhibitor Pladienolide B was added to the cell culture medium for 48 hours and the viability was assessed by normalizing organoid numbers to untreated control organoids. The line indicates WT and Sf3b1K700E organoids assessed in the same replicate.

4) It would be interesting to know whether this mutation mutually exclusive to other mutations affecting response to TGF-b. Further, while the data might not be widely available, it would be interesting to know whether in human patients the mutation occurs in precursor lesions (PanIN might be difficult to assess, but IPMN might be doable) or at later stages.

We performed a mutual exclusivity analysis in PDAC samples available at www.cbioportal.org, but did not find mutual exclusivity of SF3B1-K700E to genes of the TGF-β-pathway. Of note, the value of the analysis is limited by the small sample size of SF3B1-K700E PDAC (n=7) Moreover, to our knowledge there is no public tissue biobank for PDAC which would allow us to assess the stage of SF3B1-K700E mutated PDAC tumors. Thus, unfortunately we cannot histologically assess if the mutations already occur in early stages of human tumor development.

Author response table 1.

Author response table 1: Mutual exclusivity analysis of public PDAC databases (ICGC, CPTAC, QCMG, TCGA, UTSW), including 910 patients. Mutation frequency is 25% for SMAD4, 5% for TGF-ΒR2, 3% for SMAD2, 2.6% for TGF-ΒR1, 1.4% for SMAD3, 0.7% for SF3B1-K700E, 0.7% for TGF-ΒR3, 0.4% for SMAD1. Analysis was performed on cbioportal.org.

Reviewer #3 (Public Review):

Alternative splicing as a result of mutations in different components of the splicing machinery has been associated with a variety of cancer types, including hematological malignancies where this has been most extensively studied but also for solid tumors such as breast and pancreatic ductal adenocarcinoma (PDAC). Here the authors analyze genome sequencing data in human PDAC samples and identify a recurring mutation in the SF3B1 subunit that substitutes lysine for glutamate at residue 700 (SF3B1K700E) in PDACs. This mutation has been identified and its' molecular role in disease progression in other diseases has been studied, but the mechanism for promoting disease progression in pancreatic cancer has not been as well characterized.

To study how SF3B1K700E contributes to PDAC pathology, the authors generate a novel genetically modified mouse model of a pancreas specific SF3B1K700E mutation and explore its oncogenicity and tumor promoting potential. The authors find that SF3B1K700E is not oncogenic, but potentiates the oncogenic potential of Kras and p53 (KP) driver mutations commonly found in PDAC tumors. The authors then proceed to characterize the molecular mechanisms that might drive this phenotype. By transcriptomic analysis, the authors find KP-SF3B1K700E tumors have downregulation of epithelial-to-mesenchymal transition (EMT) genes compared to KP tumors. The cytokine TGFβ has previously been found to limit PDAC initiation and progression by causing lethal EMT in PDAC and PDAC precursor cells. Thus, the authors propose SF3B1K700E inhibition of EMT blocks the tumor suppressive activity of TGFβ and this underpins the tumor promoting role of SF3B1K700E mutation in PDAC. Consistent with this finding, SF3B1K700E mutation blocks TGFβ-induced toxicity in a variety of cell culture models of PDAC and PDAC precursor models.

Lastly, the authors seek to identify how altered splicing reduces EMT activity in PDAC cells. The authors identify misspliced genes consistent in both KP and human SF3B1K700E mutant cancer samples and find Map3k7 as one of 11 consistently misspliced genes. MAP3K7 has previously been identified as a positive regulator of EMT. Thus the authors speculated Map3k7 missplicing would lead to reduced MAP3K7 activity and a reduction EMT and that this underpins the TGFβ in SF3B1K700E mutant PDAC cells. Consistent with this, the authors find inhibition of MAP3K7 reduces TGFβ toxicity in SF3B1K700E WT cells and overexpression of MAP3K7 in SF3B1K700E mutant PDAC cells induces TGFβ toxicity. Altogether, this suggests activity of Map3k7 is responsible for altered EMT activity and TGFβ sensitivity in SF3B1K700E mutant PDAC.

Altogether, the authors generate a valuable model to study the role of a recurring splicing mutation in PDAC and provide compelling evidence that this mutation is accelerates disease. The authors then perform both: (1) an open-ended investigation of how this mutation alters PDAC cell biology where they identify altered EMT activity and (2) rigorous mechanistic studies showing suppressed EMT provides PDAC cells with resistance to TGFβ, which has previously been shown to be tumor suppressive in PDAC, suggesting a possible mechanism by which SF3B1K700E mutation is oncogenic in PDAC that future animal studies can confirm. This work generates valuable models and datasets to advance the understanding of how mutations in the splicing machinery can promote PDAC progression and suggests alternative splicing of MAP3K7 is one such possible mechanism that altered splicing promotes PDAC progression in vivo.

• One major concern about the manuscript is that the proposed mechanism by which SF3B1K700E mutation accelerates PDAC progression (MAP3K7 inhibition -> EMT inhibition -> reduced TGF-β toxicity) is only tested in ex vivo culture models and there is very limited and correlative data to suggest that this is the operative mechanism by which SF3B1K700E mutant tumors are accelerated. This is especially important because of recent findings that IFN-α signaling, which the authors also found to be high in SF3B1K700E mutant tumors, also promotes PDAC progression (https://www.biorxiv.org/content/10.1101/2022.06.29.497540v1). Thus, while thoroughly convinced by the rigorous ex vivo work that SF3B1K700E does lead to MAP3K7 inhibition -> EMT inhibition -> reduced TGF-β toxicity, further experiments to confirm this mechanism is critical in vivo would be needed to convince me that this mechanism is critical to tumor progression in vivo. For example, would forced expression of MAP3K7 slow orthotopic KP-SF3B1K700E tumor growth while leaving IFN-α signaling unperturbed?

We thank the reviewer for raising these important points. To first test if the upregulation of IFN-α signaling, seen in our RNA-seq data of sorted KPC-Sf3b1K700E cells, was directly caused by the Sf3b1-K700E mutation, we assessed the 5 most deregulated genes of the IFN-α signature in in-vitro activated KPC and KPC-Sf3b1K700E organoids (analogous to the experiments on the EMT gene signature in see Figure 2-figure supplement 1D). However, in contrast to EMT marker genes, INFa signature genes were not differently expressed in KPC-Sf3b1K700E vs. KPC organoids (Author response image 3). Thus, increased IFN-α signaling in KPC-Sf3b1K700E tumors in mice is likely an indirect consequence of further progressed cancers rather than an effect directly caused by Sf3b1K700E mediated missplicing.

Author response image 3.

Author response image 3. Expression of the 5 most deregulated genes of the IFN-α gene set identified in sorted KPC-Sf3b1K700E cells in in-vitro activated KPC-Sf3b1K700E and KPC organoids. 4 biological replicates were performed. For analysis, Ct-values of the indicated genes were normalized to Actb and a two-tailed unpaired t-test was used to compute the indicated p-values.

To next examine the effect of Map3k7 on tumors in vivo, we established orthotopic transplantation models with KPC and KPC-Sf3b1K700E cells, with overexpression or knockdown of Map3k7 (Author response image 4). However, in contrast to the autochthonous mouse model, already orthotopically transplanted KPC vs. KPC-Sf3b1K700E cells did not show differences in tumor size (see Figure 1-figure supplement 1M, N). These data support our hypothesis that Sf3b1-K700E rather plays an important role during early stages of PDAC (KPC cells are isolated from fully developed PDAC tumors and orthotopic KPC transplantation thus represents a late-stage PDAC model).

Unfortunately, these data also demonstrate that orthotopic transplantation of KPC cells is not a suitable model for studying the impact of Map3k7 in PDAC development, and as expected, neither Map3k7 overexpression in transplanted KPC-Sf3b1K700E cells nor shRNA mediated knockdown of Map3k7 (shMap3k7) in transplanted KPC cells led to differences in growth compared to their control groups (Author response image 4). In line with these results, the EMT genes that were found to be differentially expressed in our autochthonous mouse model (KPC vs. KPC-Sf3b1K700E) were expressed at similar levels upon Map3K7 downregulation or overexpression.

Since establishment of an autochthonous KPC PDAC mouse model with a knock-down of MAP3K7 is out of scope for a revision, in the revised manuscript we discuss the limitation of our study that the molecular link between Sf3b1K700E, Map3k7 and Tgfb resistance has only been studied in vitro in organoids and cell lines. We also adapted the abstract and the title of the manuscript accordingly (formerly “Mutant SF3B1 promotes PDAC malignancy through TGF-β resistance”, now “Mutant SF3B1 promotes malignancy in PDAC”).

Author response image 4.

Author response image 4. (A) Relative gene expression of Map3k7 in KPC cells transduced with shRNA targeting Map3k7 (shMap3k7), normalized to KPC cells transduced with scrambled control shRNA (shCtrl). 3 biological replicates are shown. (B) Weight of tumors derived by orthotopical transplantation of shMap3k7 and shCtrl KPC cells. 5 biological replicates are shown. (C) Relative gene expression of EMT genes in tumors derived by orthotopic transplantation of shCtrl and shMap3k7 cells. 4 biological replicates are shown. (D) Relative gene expression of Map3k7 in KPC-Sf3b1K700E cells transduced with an overexpression vector of Map3k7 (OE Map3k7), normalized to control KPC cells without Map3k7 overexpression. 3 biological replicates are shown, a two-sided student’s t-test was used to calculate significance. (E) Weight of tumors derived by orthotopical transplantation of Map3k7 overexpressing KPC-Sf3b1K700E cells (n=5) and control KPC-Sf3b1K700E cells (n=4). (F) Relative gene expression of EMT genes in tumors derived by orthotopic transplantation of KPC-Sf3b1K700E cells with- and without overexpression of Map3k7. 4 biological replicates are shown. A two-sided student’s t-test was used to calculate significance in Fig. 2A-F.

Author Respones

Reviewer #1 (Public Review):

The manuscript by Hekselman et al presents analyses linking cell-types to monogenic disorders using over-expression of monogenic disease genes as the signal. The manuscript analyses data from 6 tissues (bone marrow, lung, muscle, spleen, tongue and trachea) together with ~1,000 rare diseases from OMIM (with ~2,000 associated genes) to identify cell-type of interest for specific disease of choice. The signal used by the approach is the relative expression of OMIM-genes in a particular cell type relative to the expression of the gene in the tissue of interest identifying celltype-disease pairs that are then investigated through literature review and recapitulated using mouse expression. A potentially interesting finding is that disease genes manifesting in multiple tissues seem to hit same cell-types. Overall this important study combines multiple data analyses to quantify the connection between cell types and human disorders. However whereas some of the analyses are compelling, the statistical analyses are incomplete as they don't provide full treatment of type I error.

Statistical analyses were changed to include permutation testing and a different threshold (Results, page 6, 1st paragraph; Methods, page 21-22, ‘PrEDiCT score calculation and significance assessment’; Figure 1–figure supplement 2). Assessments of type I error were based on literature text-mining and expert curation, and showed that false-positive rates were low in both (0.01 and 0.07, respectively; Figure 1F and Figure 1–figure supplement 4A).

Reviewer #2 (Public Review):

This study identifies 110 disease-affected cell types for 714 Mendelian diseases, based on preferential expression of known disease-associated genes in single-cell data. It is likely that many or most of the results are real, and the results are biologically interesting and provide a valuable resource. However, updates to the method are needed to ensure that inference of statistical significance is appropriately stringent and rigorous.

Strengths: a systematic evaluation of disease-affected cell types across Mendelian diseases is a valuable addition to the literature, complementing systematic evaluations of common disease and targeted analyses of individual Mendelian diseases. The validation via excess overlap with diseasecell type pairs from literature co-appearance provides compelling evidence that many or most of the results are real. In addition, many of the results are biologically interesting. In particular, it is interesting that diseases with multiple affected tissues tend to affect similar cell types in the respective tissues.

Limitations: the main limitation of the study is that, although many or most of the results are likely to be real, the criteria for statistical significance is probably not stringent enough, and is not welljustified. For diseases with only 1 disease-associated gene, the threshold is a z-score>2 for preferential expression in the cell type, but this threshold is likely to be often exceeded by chance. (For diseases with many disease-associated genes, the threshold is a median (across genes) zscore>2 for preferential expression in the cell type, which is less likely to occur by chance but still an arbitrary threshold.) Thus, there is a good chance that a sizable proportion of the reported disease-affected cell types might be false positives. The best solution would be to assess statistical significance via empirical comparison with results for non-disease-associated control genes, and assess the statistical significance of the resulting P-values using FDR.

We thank the reviewer for the valuable insights and suggestions. We revised the method to assess statistical significance by using empirical comparison followed by FDR correction, as suggested by the reviewer (Results, page 6, 1st paragraph; Methods, page 21-22, ‘PrEDiCT score calculation and significance assessment’; Figure 1–figure supplement 2).

The re-analysis using mouse single-cell data adds an interesting additional dimension to the study, with the small caveat that mouse single-cell data does not provide statistically independent information across genes (for the same reason that adding data from independent human individuals would not provide statistically independent information across genes, given that human and mouse expression are partially correlated).

We acknowledge this caveat in the text (Discussion, page 17, 2nd paragraph, lines 8-11).

Reviewer #3 (Public Review):

The authors describe the method, PrEDiCT, which helps identify disease affected cell types based on gene sets. As I understand it, the method is based on finding which "disease genes" (from an annotation) are relatively highly expressed. The idea is nice, however, I have concerns about how "significance" is assessed and the relative controls.

Overall, I find the idea interesting, but the execution raises some concerns.

1) From a causal perspective, there is an association of high expression of these genes within these cell types, but without also assessing individuals with those specific diseases, I do not it is fair to say "disease affected" cell types. It is possible that these genes might behave completely fine but are highly expressed in those cell types while being affected another in other cell types.

We agree with the reviewer. We changed the terminology to "likely disease-affected cell types” and added this caveat to the Discussion, page 16, 2nd paragraph.

2) It is unclear to me what the "null" comparison is in the method and if there is one. For example, by chance, would I expect this gene to be highly expressed because other genes are also highly expressed in this cell type? Some way to assess "significance" or "enrichment" beyond simply using ranks and thresholds would be helpful in deciding whether these associations are robust.

We revised the procedure for assessing statistical significance to include permutation tests. Specifically, given a disease D with n disease-associated genes, the null hypothesis was that the PrEDiCT score of these genes is not significantly different from the PrEDiCT score of a random set of n genes. To test this, we randomly selected n genes expressed in any cell type, and computed the PrEDiCT score for this random gene set in each cell type of the disease-affected tissue (referred to as ‘random score’). We repeated this procedure 1,000 times, resulting in 1,000 random scores per disease and cell type. The p-value of the PrEDiCT score of disease D in cell type c was set to the fraction of random scores in c that were at least as high as the original PrEDiCT score of D in c. The acquired p-values were adjusted for multiple hypothesis testing per disease using the Benjamini-Hochberg procedure. To increase stringency, we treated only statistically significant disease–cell-type pairs with PrEDiCT score≥1 as 'likely affected'. The procedure is detailed in Results, page 6, 1st paragraph; Methods, page 21-22, ‘PrEDiCT score calculation and significance assessment’; Figure 1–figure supplement 2. Additionally, we estimated type I error by using literature text-mining or expert curation (Results, page 7, 2nd paragraph; Methods, page 22, ‘Textmining of PubMed records’, and page 23, ‘Expert curation and assessment of disease-affected cell types’; Figure 1F and Figure 1–figure supplement 4A).

3) Additionally, it is unclear to me, but I suspect that there are unequal cell numbers in the scores computed as well as between relevant tissues. This is related to point (2) above, but as a result, the estimates of the scores will inherently have different variances, thus making comparisons between them difficult/unreliable unless accounted for. If I understand correctly, the score is first the average expression within a tissue, then, the Z-score? If so, my comment applies.

To clarify, the PrEDiCT score of a disease D in cell type c was set to the median preferential expression P of its disease genes (Equation 1 below). The preferential expression of each gene in c was computed as a Z-score, by comparing the average expression of the gene in c to its average expression in all cell types of the tissue, divided by the standard deviation (SD, Equation 2 below). Tissues indeed had unequal numbers of cell types, however, the distribution of PrEDiCT scores were similar between tissues (now in Supplementary File 13). We revised this part of Methods and added Equations 1 and 2 (Methods, page 21-22, ‘PrEDiCT score calculation and significance assessment’) and Supplementary File 13.

4) There is a large set of work done in gene enrichment sets which appears to not be mentioned (e.g. GSEA and other works by the Price group). It would be helpful for the authors to summarize these methods and how their method differs.

We added work done in gene enrichment sets (including two relevant and recent studies from the Price group) and summarized these methods in the Introduction (page 2-3).

5) Additionally, it should be noted that a caveat of this analysis is that the comparisons are all done only relative to the cell types sampled and the diseases which have Mendelian genes associated with them. I would expect these results to change, possibly drastically, if the sampled cell types and diseases were to be changed.

We agree with the reviewer and now discuss the generalizability of our results, relating to the extent of the sampled cell types (Discussion, page 18, 1st paragraph).

6) Finally, I would appreciate a more detailed explanation in the methods of how the score is computed. Some equations and the data they are calculated from would be helpful here.

We now provide a detailed explanation of how the score and its statistical significance were computed and added Equations 1 and 2 (Methods, page 21-22, ‘PrEDiCT score calculation and significance assessment’).

In summary, the general idea is an interesting one, but I do think the issues above should be addressed to make the results convincing.

We thank the reviewer for the important feedback which helped us strengthen our analyses.

Author Response

Reviewer #2 (Public Review):

I believe the authors succeeded in finding neural evidence of reactivation during REM sleep. This is their main claim, and I applaud them for that. I also applaud their efforts to explore their data beyond this claim, and I think they included appropriate controls in their experimental design. However, I found other aspects of the paper to be unclear or lacking in support. I include major and medium-level comments:

Major comments, grouped by theme with specifics below:

Theta.

Overall assessment: the theta effects are either over-emphasized or unclear. Please either remove the high/low theta effects or provide a better justification for why they are insightful.

Lines ~ 115-121: Please include the statistics for low-theta power trials. Also, without a significant difference between high- and low-theta power trials, it is unclear why this analysis is being featured. Does theta actually matter for classification accuracy?

Lines 123-128: What ARE the important bands for classification? I understand the point about it overlapping in time with the classification window without being discriminative between the conditions, but it still is not clear why theta is being featured given the non-significant differences between high/low theta and the lack of its involvement in classification. REM sleep is high in theta, but other than that, I do not understand the focus given this lack of empirical support for its relevance.

Line 232-233: "8). In our data, trials with higher theta power show greater evidence of memory reactivation." Please do not use this language without a difference between high and low theta trials. You can say there was significance using high theta power and not with low theta power, but without the contrast, you cannot say this.

Thank you, we have taken this point onboard. We thought the differences observed between classification in high and low theta power trials were interesting, but we can see why the reviewer feels there is a need for a stronger hypothesis here before reporting them. We have therefore removed this approach from the manuscript, and no longer split trials into high and low theta power.

Physiology / Figure 2.

Overall assessment: It would be helpful to include more physiological data.

It would be nice, either in Figure 2 or in the supplement, to see the raw EEG traces in these conditions. These would be especially instructive because, with NREM TMR, the ERPs seem to take a stereotypical pattern that begins with a clear influence of slow oscillations (e.g., in Cairney et al., 2018), and it would be helpful to show the contrast here in REM.

We thank the reviewer for these comments. We have now performed ERP and time-frequency analyses following a similar approach to that of (Cairney et al., 2018). We have added a section in the results for these analyses as follows:

“Elicited response pattern after TMR cues

We looked at the TMR-elicited response in both time-frequency and ERP analyses using a method similar to the one used in (Cairney et al., 2018), see methods. As shown in Figure 2a, the EEG response showed a rapid increase in theta band followed by an increase in beta band starting about one second after TMR onset. REM sleep is dominated by theta activity, which is thought to support the consolidation process (Diekelmann & Born, 2010), and increased theta power has previously been shown to occur after successful cueing during sleep (Schreiner & Rasch, 2015). We therefore analysed the TMR-elicited theta in more detail. Focussing on the first second post-TMR-onset, we found that theta was significantly higher here than in the baseline period, prior to the cue [-300 -100] ms, for both adaptation (Wilcoxon signed rank test, n = 14, p < 0.001) and experimental nights (Wilcoxon signed rank test, n = 14, p < 0.001). The absence of any difference in theta power between experimental and adaptation conditions (Wilcoxon signed rank test, n = 14, p = 0.68), suggests that this response is related to processing of the sound cue itself, not to memory reactivation. Turning to the ERP analysis, we found a small increase in ERP amplitude immediately after TMR onset, followed by a decrease in amplitude 500ms after the cue. Comparison of ERPs from experimental and adaptation nights showed no significant difference, (n= 14, p > 0.1). Similar to the time-frequency result, this suggests that the ERPs observed here relate to the processing of the sound cues rather than any associated memory.“

And we have updated Figure 2.

Also, please expand the classification window beyond 1 s for wake and 1.4 s for sleep. It seems the wake axis stops at 1 s and it would be instructive to know how long that lasts beyond 1 s. The sleep signal should also go longer. I suggest plotting it for at least 5 seconds, considering prior investigations (Cairney et al., 2018; Schreiner et al., 2018; Wang et al., 2019) found evidence of reactivation lasting beyond 1.4 s.

Regarding the classification window, this is an interesting point. TMR cues in sleep were spaced 1.5 s apart and that is why we included only this window in our classification. Extending our window beyond 1.5 s would mean that we considered the time when the next TMR cue was presented. Similarly, in wake the duration of trials was 1.1 s thus at 1.1 s the next tone was presented.

Following the reviewer’s comment, we have extended our window as requested even though this means encroaching on the next trial. We do this because it could be possible that there is a transitional period between trials. Thus, when we extended the timing in wake and looked at reactivation in the range 0.5 s to 1.6 s we found that the effect continued to ~1.2 s vs adaptation and chance, e.g. it continued 100 ms after the trial. Results are shown in the figures below.

Temporal compression/dilation.

Overall assessment: This could be cut from the paper. If the authors disagree, I am curious how they think it adds novel insight.

Line 179 section: In my opinion, this does not show evidence for compression or dilation. If anything, it argues that reactivation unfolds on a similar scale, as the numbers are clustered around 1. I suggest the authors scrap this analysis, as I do not believe it supports any main point of their paper. If they do decide to keep it, they should expand the window of dilation beyond 1.4 in Figure 3B (why cut off the graph at a data point that is still significant?). And they should later emphasize that the main conclusion, if any, is that the scales are similar.

Line 207 section on the temporal structure of reactivation, 1st paragraph: Once again, in my opinion, this whole concept is not worth mentioning here, as there is not really any relevant data in the paper that speaks to this concept.

We thank the reviewer for these frank comments. On consideration, we have now removed the compression/dilation analysis.

Behavioral effects.

Overall assessment: Please provide additional analyses and discussion.

Lines 171-178: Nice correlation! Was there any correlation between reactivation evidence and pre-sleep performance? If so, could the authors show those data, and also test whether this relationship holds while covarying our pre-sleep performance? The logic is that intact reactivation may rely on intact pre-sleep performance; conversely, there could be an inverse relationship if sleep reactivation is greater for initially weaker traces, as some have argued (e.g., Schapiro et al., 2018). This analysis will either strengthen their conclusion or change it -- either outcome is good.

Thanks for these interesting points. We have now performed a new analysis to check if there was a correlation between classification performance and pre-sleep performance, but we found no significant correlation (n = 14, r = -0.39, p = 0.17). We have included this in the results section as follows:

“Finally, we wanted to know whether the extent to which participants learned the sequence during training might predict the extent to which we could identify reactivation during subsequent sleep. We therefore checked for a correlation between classification performance and pre-sleep performance to determine whether the degree of pre-sleep learning predicted the extent of reactivation, this showed no significant correlation (n = 14, r = -0.39, p = 0.17). “

Note that we calculated the behavioural improvement while subtracting pre-sleep performance and then normalising by it for both the cued and un-cued sequences as follows:

[(random blocks after sleep - the best 4 blocks after sleep) – (random blocks pre-sleep – the best 4 blocks pre-sleep)] / (random blocks pre-sleep – the best 4 blocks pre-sleep).

Unlike Schönauer et al. (2017), they found a strong correspondence between REM reactivation and memory improvement across sleep; however, there was no benefit of TMR cues overall. These two results in tandem are puzzling. Could the authors discuss this more? What does it mean to have the correlation without the overall effect? Or else, is there anything else that may drive the individual differences they allude to in the Discussion?

We have now added a discussion of this point as follows:

“We are at a very early phase in understanding what TMR does in REM sleep, however we do know that the connection between hippocampus and neocortex is inhibited by the high levels of Acetylcholine that are present in REM (Hasselmo, 1999). This means that the reactivation which we observe in the cortex is unlikely to be linked to corresponding hippocampal reactivation, so any consolidation which occurs as a result of this is also unlikely to be linked to the hippocampus. The SRTT is a sequencing task which relies heavily on the hippocampus, and our primary behavioural measure (Sequence Specific Skill) specifically examines the sequencing element of the task. Our own neuroimaging work has shown that TMR in non-REM sleep leads to extensive plasticity in the medial temporal lobe (Cousins et al., 2016). However, if TMR in REM sleep has no impact on the hippocampus then it is quite possible that it elicits cortical reactivation and leads to cortical plasticity but provides no measurable benefit to Sequence Specific Skill. Alternatively, because we only measured behavioural improvement right after sleep it is possible that we may have missed behavioural improvements that would have emerged several days later, as we know can occur in this task (Rakowska et al., 2021).”

Medium-level comments

Lines 63-65: "We used two sequences and replayed only one of them in sleep. For control, we also included an adaptation night in which participants slept in the lab, and the same tones that would later be played during the experimental night were played."

I believe the authors could make a stronger point here: their design allowed them to show that they are not simply decoding SOUNDS but actual memories. The null finding on the adaptation night is definitely helpful in ruling this possibility out.

We agree and would like to thank the reviewer for this point. We have now included this in the text as follows: “This provided an important control, as a null finding from this adaptation night would ensure that we are decoding actual memories, not just sounds. “

Lines 129-141: Does reactivation evidence go down (like in their prior study, Belal et al., 2018)? All they report is theta activity rather than classification evidence. Also, I am unclear why the Wilcoxon comparison was performed rather than a simple correlation in theta activity across TMR cues (though again, it makes more sense to me to investigate reactivation evidence across TMR cues instead).

Thanks a lot for the interesting point. In our prior study (Belal et. al. 2018), the classification model was trained on wake data and then tested on sleep data, which enabled us to examine its performance at different timepoints in sleep. However in the current study the classifier was trained on sleep and tested on wake, so we can only test for differential replay at different times during the night by dividing the training data. We fear that dividing sleep trials into smaller blocks in this way will lead to weakly trained classifiers with inaccurate weight estimation due to the few training trials, and that these will not be generalisable to testing data. Nevertheless, following your comment, we tried this, by dividing our sleep trials into two blocks, e.g. the first half of stimulation during the night and the second half of stimulation during the night. When we ran the analysis on these blocks separately, no clusters were found for either the first or second halves of stimulation compared to adaptation, probably due to the reasons cited above. Hence the differences in design between the two studies mean that the current study does not lend itself to this analysis.

Line 201: It seems unclear whether they should call this "wake-like activity" when the classifier involved training on sleep first and then showing it could decode wake rather than vice versa. I agree with the author's logic that wake signals that are specific to wake will be unhelpful during sleep, but I am not sure "wake-like" fits here. I'm not going to belabor this point, but I do encourage the authors to think deeply about whether this is truly the term that fits.

We agree that a better terminology is needed, and have now changed this: “In this paper we demonstrated that memory reactivation after TMR cues in human REM sleep can be decoded using EEG classifiers. Such reactivation appears to be most prominent about one second after the sound cue onset. ”

Reviewer #3 (Public Review):

The authors investigated whether reactivation of wake EEG patterns associated with left- and right-hand motor responses occurs in response to sound cues presented during REM sleep.

The question of whether reactivation occurs during REM is of substantial practical and theoretical importance. While some rodent studies have found reactivation during REM, it has generally been more difficult to observe reactivation during REM than during NREM sleep in humans (with a few notable exceptions, e.g., Schonauer et al., 2017), and the nature and function of memory reactivation in REM sleep is much less well understood than the nature and function of reactivation in NREM sleep. Finding a procedure that yields clear reactivation in REM in response to sound cues would give researchers a new tool to explore these crucial questions.

The main strength of the paper is that the core reactivation finding appears to be sound. This is an important contribution to the literature, for the reasons noted above.

The main weakness of the paper is that the ancillary claims (about the nature of reactivation) may not be supported by the data.

The claim that reactivation was mediated by high theta activity requires a significant difference in reactivation between trials with high theta power and trials with low theta, but this is not what the authors found (rather, they have a "difference of significances", where results were significant for high theta but not low theta). So, at present, the claim that theta activity is relevant is not adequately supported by the data.

The authors claim that sleep replay was sometimes temporally compressed and sometimes dilated compared to wakeful experience, but I am not sure that the data show compression and dilation. Part of the issue is that the methods are not clear. For the compression/dilation analysis, what are the features that are going into the analysis? Are the feature vectors patterns of power coefficients across electrodes (or within single electrodes?) at a single time point? or raw data from multiple electrodes at a single time point? If the feature vectors are patterns of activity at a single time point, then I don't think it's possible to conclude anything about compression/dilation in time (in this case, the observed results could simply reflect autocorrelation in the time-point-specific feature vectors - if you have a pattern that is relatively stationary in time, then compressing or dilating it in the time dimension won't change it much). If the feature vectors are spatiotemporal patterns (i.e., the patterns being fed into the classifier reflect samples from multiple frequencies/electrodes / AND time points) then it might in principle be possible to look at compression, but here I just could not figure out what is going on.

Thank you. We have removed the analysis of temporal compression and dilation from the manuscript. However, we wanted to answer anyway. In this analysis, raw data were smoothed and used as time domain features. The data was then organized as trials x channels x timepoints then we segmented each trial in time based on the compression factor we are using. For instance, if we test if sleep is 2x faster than wake we look at the trial lengths in wake which was 1.1 sec. and we take half of this value which is 0.55 sec. we then take a different window in time from sleep data such that each sleep trial will have multiple smaller segments each of 0.55 sec., we then add those segments as new trials and label them with the respective trial label. Afterwards, we resize those segments temporally to match the length of wake trials. We now reshape our data from trials x channels x timepoints to trials x channels_timepoints so we aggregate channels and timepoints into one dimension. We then feed this to PCA to reduce the dimensionality of channels_timepoints into principal components. We then feed the resultant features to a LDA classifier for classification. This whole process is repeated for every scaling factor and it is done within participant in the same fashion the main classification was done and the error bars were the standard errors. We compared the results from the experimental night to those of the adaptation night.

For the analyses relating to classification performance and behavior, the authors presently show that there is a significant correlation for the cued sequence but not for the other sequence. This is a "difference of significances" but not a significant difference. To justify the claim that the correlation is sequence-specific, the authors would have to run an analysis that directly compares the two sequences.

Thanks a lot. We have now followed this suggestion by examining the sequence specific improvement after removing the effect of the un-cued sequence from the cued sequence. This was done by subtracting the improvement of the un-cued sequence from the improvement for the cued sequence, and then normalising the result by the improvement of the un-cued sequence. The resulting values, which we term ‘cued sequence improvement’ showed a significant correlation with classification performance (n = 14, r = 0.56, p = 0.04). We have therefore amended this section of the manuscript as follows: We have updated the text as follows: “We therefore set out to determine whether there was a relationship between the extent to which we could classify reactivation and overnight improvement on the cued sequence. This revealed a positive correlation (n = 14, r = 0.56, p = 0.04), Figure 3b.”

Author response:

Reviewer #1 (Public Review):

In this study, Girardello et al. use proteomics to reveal the membrane tension sensitive caveolin-1 interactome in migrating cells. The authors use EM and surface rendering to demonstrate that caveolae formed at the rear of migrating cells are complex membrane-linked multilobed structures, and they devise a robust strategy to identify caveolin-1 associated proteins using APEX2-mediated proximity biotinylation. This important dataset is further validated using proximity ligation assays to confirm key interactions, and follows up with an interrogation of a surprising relationship between caveolae and RhoGTPase signalling, where caveolin-1 recruits ROCK1 under high membrane tension conditions, and ROCK1 activity is required to reform caveolae upon reversion to isotonic solution. However, caveolin-1 recruits the RhoA inactivator ARHGAP29 when membrane tension is low and ARHGAP29 overexpression leads to disassembly of caveolae and reduced cell motility. This study builds on previous findings linking caveolae to positive feedback regulation of RhoA signalling, and provides further evidence that caveolae serve to drive rear retraction in migration but also possess an intrinsic brake to limit RhoA activation, leading the authors to suggest that cycles of caveolae assembly and disassembly could thereby be central to establish a stable cell rear for persistent cell migration

A major strength of the manuscript is the robust proteomic dataset. The experimental set up is well defined and mostly well controlled, and there is good internal validation in that the high abundance of core caveolar proteins in low membrane tension (isotonic) conditions, and absence under high membrane tension (brief hypo-osmotic shock) conditions, correlating very well with previous finding. The data could however be better presented to show where statically robust changes occur, and supplementary information should include a table of showing abundance. It's very good to see a link to PRIDE, providing a useful resource for the community.

We thank the reviewer for the positive feedback. We have included the outputs from the search engine in Supplementary File 1.

The authors detail several known interactions and their mechanosensitivty, but also report new interactors of caveolin-1. Several mechanosensitive interactions of caveolin-1 take place at the cell rear, but others are more diffuse across the cell looking at the PLA data (e.g FLN1, CTTN, HSPB1; Figure 4A-F and Figure 4 supplement 1). It is interesting to speculate that those at the cell rear are involved in caveolae, whilst others are linked specifically to caveolin-1 (e.g. dolines). PLA or localisation analysis with Cavin1/PTRF may be able to resolve this and further specify caveolae versus non-caveolae mechanosensitive interactions.

We thank the reviewer for this interesting idea. It is true that many if not most proteins we identified to be associated with Cav1 are not restricted to the cell rear. To analyse to what extent the identified proteins interact with Cav1 at the rear we reanalysed our PLA data for some of the antibody combinations we looked at. This new analysis is now shown in Fig 5G. As expected, for Cav1/PTRF and Cav1/EHD2 most PLA dots (70-80%) were found at the rear. This rear bias is also evident from the representative images we show in the Figure panels 5A and 5E. On the contrary, much fewer PLA dots (~40%) were rear-localised for Cav1/CTTN and Cav1/FLNA antibody combinations. This reflects the much broader cellular distribution of these proteins compared to the core caveolae proteins, and might suggest that there are generally few links between caveolae and cortical actin. However, it is also possible that such links/interactions are more difficult to detect using PLA (because of the extended distance between caveolae and the actin cortex, or because of steric constraints).

The Cav1/ARHGAP29 influence on YAP signalling is interesting, but appear to be quite isolated from the rest of the manuscript. Does overexpression of ARHGAP29 influence YAP signalling and/or caveolar protein expression/Cav1pY14?

Our data and published work originally prompted us to speculate that there is a potential functional link between Cav1, YAP, and ARHGAP29. In an attempt to address this we have performed several Western blots on cell lysates from cells overexpressing ARHGAP29. We did not see major changes in Cav1 Y14 phosphorylation levels in cells overexpressing ARHGAP29, and YAP and pYAP levels also remained unchanged (not shown). In addition, based on previous literature 1,2 we expected to see an effect on ARHGAP29 mRNA levels and YAP target gene transcripts in Cav1 siRNA transfected cells. To our surprise, the mRNA levels of three independent YAP target genes and ARHGAP29 were unchanged in Cav1 siRNA treated cells (this is now shown in Figure 6 Figure Supplement 1). Our data therefore suggest that in RPE1 cells, the connection between Cav1 and ARHGAP29 is independent of YAP signalling, and that the increase in ARHGAP29 protein levels observed in Cav1 siRNA cells is due to some unknown post-translational mechanism.

ARHGAP29 and RhoA/ROCK1 related observations are very interesting and potentially really important. However, the link between ARHGAP29 and caveolae is not well established (other than in proteomic data). PLA or FRET could help establish this.

We agree that the physical and functional link between caveolae (or Cav1) and ARHGAP29 was not well worked out in the original manuscript. In an attempt to address this we have performed PLA assays in GFP-ARHGAP29 transfected cells (as we did not find a suitable ARHGAP29 antibody that works reliably in IF) using anti-Cav1 and anti-GFP antibodies. The PLA signal we obtained for Cav1 and ARHGAP29 was not significantly different to control PLA experiments. There was very little PLA signal to start with. This is not surprising given that ARHGAP29 localisation is mostly diffuse in the cytoplasm, whilst Cav1 is concentrated at the rear. In addition, in cases where we do see ARHGAP29 localisation at the cell cortex, Cav1 tends to be absent (this is now shown in Figure 6 – Figure Supplement 2E). In other words, with the tools we have available, we see little colocalization between Cav1 and ARHGAP29 at steady state. Altogether we speculate that ARHGAP29, through its negative effect on RhoA, flattens caveolae at the membrane or interferes with caveolae assembly at these sites.

This of course prompts the question why ARHGAP29 was identified in the Cav1 proteome with such specificity and reproducibility in the first place? This can be explained by the way APEX2 labeling works. Proximity biotinylation with APEX2 is extremely sensitive and restricted to a labelling radius of ~20 nm 3. The labeling reaction is conducted on live and intact cells at room temperature for 1 min. Although 1 min appears short, dynamic cellular processes occur at the time scale of seconds and are ongoing during the labelling reaction. It is conceivable that within this 1 min time frame, ARHGAP29 cycles on and off the rear membrane (kiss and run). This allows ARHGAP29 to be biotinylated by Cav1-APEX2, resulting in its identification by MS. We have included this in the discussion section.

The relationship between ARHGAP29 and RhoA signalling is not well defined. Is GAP activity important in determining the effect on migration and caveolae formation? What is the effect on RhoA activity? Alternatively, the authors could investigate YAP dependent transcriptional regulation downstream of overexpression.

We have addressed this point using overexpression and siRNA transfections. We overexpressed ARHGAP29 or ARHGAP29 lacking its GAP domain and performed WB analysis against pMLC (which is a commonly used and reliable readout for RhoA and myosin-II activity). Much to our surprise, overexpression of ARHGAP29 increased (rather than decreased) pMLC levels, partially in a GAP-dependent manner (see Author response image 1). This is puzzling, as ARHGAP29 is expected to reduce RhoA-GTP levels, which in turn is expected to reduce ROCK activity and hence pMLC levels. In addition, and also surprisingly, siRNA-mediated silencing of ARHGAP29 did not significantly change pMLC levels. By contrast, pMLC levels were strongly reduced in Cav1 siRNA treated cells (this is shown in Fig. 6A and 6B in the revised manuscript). These new data underscore the important role of caveolae in the control of myosin-II activity, but do not allow us to draw any firm conclusions about the role of ARHGAP29 at the cell rear.

Author response image 1.

Overexpression of ARHGAP29 reduces, rather than increases pMLC in RPE1 cells.

We are uncertain as to how to interpret the ARHGAP29 overexpression data presented in Author response image 1 and therefore decided not to include it in the manuscript. One possibility is that inactivation of RhoA below a certain critical threshold causes other mechanisms to compensate. For instance, the activity of alternative MLC kinases such as MLCK could be enhanced under these conditions. Another possibility is that ARHGAP29 controls MLC phosphorylation indirectly. For instance, it has been shown that ARHGAP29 promotes actin destabilization through inactivating LIMK/cofilin signalling 1. In agreement with this, we find that overexpression of ARHGAP29 reduces p-cofilin (serine 3) levels (see Author response image 2). Since cofilin and MLC crosstalk 4, it is possible that increased pMLC levels are the result of a feedback loop that compensates for the effect of actin depolymerisation. This is now discussed in the discussion section. Whichever the case, we hope the reviewers understand that deeper mechanistic insight into the intricate mechanisms of Rho signalling at the cell rear are beyond the scope of this manuscript.

Author response image 2.

Overexpression of ARHGAP29 reduces p-cofilin levels in RPE1.

Reviewer #2 (Public Review):

Girardello et al investigated the composition of the molecular machinery of caveolae governing their mechano-regulation in migrating cells. Using live cell imaging and RPE1 cells, the authors provide a spatio-temporal analysis of cavin-3 distribution during cell migration and reveal that caveolae are preferentially localized at the rear of the cell in a stable manner. They further characterize these structures using electron tomography and reveal an organization into clusters connected to the cell surface. By performing a proteomic approach, they address the interactome of caveolin-1 proteins upon mechanical stimulation by exposing RPE1 cells to hypo-osmotic shock (which aims to increase cell membrane tension) or not as a control condition. The authors identify over 300 proteins, notably proteins related to actin cytoskeleton and cell adhesion. These results were further validated in cellulo by interrogating protein-protein interactions using proximity ligation assays and hypo-osmotic shock. These experiments confirmed previous data showing that high membrane tension induces caveolae disassembly in a reversible manner. Eventually, based on literature and on the results collected by the proteomic analysis, authors investigated more deeply the molecular signaling pathway controlling caveolae assembly upon mechanical stimuli. First, they confirm the targeting of ROCK1 with Caveolin-1 and the implication of the kinase activity for caveolae formation (at the rear of the cell). Then, they show that RhoGAP ARHGAP29, a factor newly identified by the proteomic analysis, is also implicated in caveolae mechano-regulation likely through YAP protein and found that overexpression of RhoGAP ARHGAP29 affects cell motility. Overall, this paper interrogated the role of membrane tension in caveolae located at the rear of the cell and identified a new pathway controlling cell motility.

Strengths:

Using a proximity-based proteomic assay, the authors reveal the protein network interacting with caveolae upon mechanical stimuli. This approach is elegant and allows to identify a substantial new set of factors involved in the mechano-regulation of caveolin-1, some of which have been verified directly in the cell by PLA. This study provides a compelling set of data on the interactions between caveolae and its cortical network which was so far ill-characterized.

We thank the reviewer for this positive feedback.

Weaknesses:

The methodology demonstrating an impact of membrane tension is not precise enough to directly assess a direct role on caveolae at a subcellular scale, that is between the front and the rear of the cell. First, a better characterization of the "front-rear" cellular model is encouraged.

We agree with the reviewer that a quantitative analysis of the caveolae front-rear polarity would strengthen our conclusions. To address this, we have analysed the localisation of Cav1 and cavins in detail and in a large pool of cells, both in fixed and live cells. Our quantification clearly shows that Cav1 and cavins are enriched at the cell rear. This is now shown in Figure 1 and Figure 1 - Figure Supplement 1. To demonstrate that Cav1/cavins are truly rear-localised we analysed live migrating cells expressing tagged Cav1 or cavins. This analysis, which was performed on several individual time lapse movies, showed that caveolae rear localisation is remarkably stable (e.g. Figure 1C and 1D). We also present novel data panels and movies showing caveolae dynamics during rear retractions, in dividing cells, and in cells that polarise de novo. This new data is now described in the first paragraph of the results section.

Secondly, authors frequently present osmotic shock as "high membrane tension" stimuli. While osmotic shock is widely used in the field, this study is focused only on caveolae localized at the rear of cell and it remains unclear how the level of a global mechanical stimuli triggered by an osmotic shock could mimic a local stimuli.

We agree with the reviewer that osmotic shock will cause a global increase in membrane tension and therefore is only of limited value to understand how membrane tension is regulated at the rear, and how caveolae respond to such a local stimulus. It was not our aim nor is it our expertise to address such questions. To answer this sophisticated optogenetic approaches or localised membrane tension measurements (e.g. through the use of the Flipper-TR probe) are needed. It is beyond the scope of this manuscript to perform such experiments. However, given the strong enrichment of caveolae at the cell rear, we believe it is justified to propose that the changes we observe in the proteome do (mostly) reflect changes in caveolae at the rear. We have now included several quantifications on fixed cells, live cells, and PLA assays to support that caveolae are highly enriched at the rear. In addition, and importantly, a recent preprint by the Roux lab shows that membrane tension gradients indeed exist in many migrating and non-migrating cells 5. Using very similar hypotonic shock assays, the Caswell lab also showed that low membrane tension at the rear is required for caveolae formation 6. We have included a section in the discussion in which we elaborate on how membrane tension is controlled in migrating cells, and how it might regulate caveolae rear localisation.

In the present case, it remains unknown the extent to which this mechanical stress is physiologically relevant to mimic mechanical forces applied at the rear of a migrating cell.

This is true. Our study does not address the nature of mechanical forces at the cell rear. This a complex subject that is technically challenging to address, and therefore is beyond the scope of this manuscript.

Some images are not satisfying to fully support the conclusions of the article.

We agree that some of the images, in particular the ones presented for the PLA assays, do not always show a clear rear localisation of caveolae. We have explained above why this is the case. We hope that our new quantitative measurements, movies and figure panels, addresses the reviewer’s concern.

At this stage, the lack of an unbiased quantitative analysis of the spatio-temporal analysis of caveolae upon well-defined mechanical stimuli is also needed.

These are all very good points that were previously addressed beautifully by the Caswell group 6. To address this in part in our RPE1 cell system, we imaged RPE1 cells exposed to the ROCK inhibitor Y27632 (see Author response image 3). The data shows that cell rear retraction is impeded in response to ROCK inhibition, which is in line with several previous reports. Cavin-1 remained mostly associated with the cell rear, although the distribution appeared more diffuse. We believe this data does not add much new insight into how caveolae function at the rear, and hence was not included in the manuscript.

Author response image 3.

Effect of ROCK inhibition on cavin1 rear localisation and rear retraction. Cells were imaged one hour after the addition of Y27632.

Cells on images, in particular Figure 1, are difficult to see. Signal-to noise ratio in different cell area could generate a biased. Since there is inconsistency between caveolae density and localization between Figures, more solid illustrations are needed along quantitative analysis.

As mentioned above, we have carefully analysed the localisation of caveolae in fixed cells (using Cav1 and cavin1 antibodies as well as Cav1 and cavin fusion proteins) and in live cells transfected with various different caveolae proteins. The analysis clearly demonstrates an enrichment of caveolae at the rear (Figure 1 and Figure 1 – Figure Supplement 1). Our tomography and TEM data supports this as well (Figure 2).

References:

1. Qiao Y, Chen J, Lim YB, et al. YAP Regulates Actin Dynamics through ARHGAP29 and Promotes Metastasis. Cell reports. 2017;19(8):1495-1502.

2. Rausch V, Bostrom JR, Park J, et al. The Hippo Pathway Regulates Caveolae Expression and Mediates Flow Response via Caveolae. Curr Biol. 2019;29(2):242-255 e246.

3. Hung V, Udeshi ND, Lam SS, et al. Spatially resolved proteomic mapping in living cells with the engineered peroxidase APEX2. Nat Protoc. 2016;11(3):456-475.

4. Wiggan O, Shaw AE, DeLuca JG, Bamburg JR. ADF/cofilin regulates actomyosin assembly through competitive inhibition of myosin II binding to F-actin. Dev Cell. 2012;22(3):530-543.

5. Juan Manuel García-Arcos AM, Julissa Sánchez Velázquez, Pau Guillamat, Caterina Tomba, Laura Houzet, Laura Capolupo, Giovanni D’Angelo, Adai Colom, Elizabeth Hinde, Charlotte Aumeier, Aurélien Roux. Actin dynamics sustains spatial gradients of membrane tension in adherent cells. bioRxiv 20240715603517. 2024.

6. Hetmanski JHR, de Belly H, Busnelli I, et al. Membrane Tension Orchestrates Rear Retraction in Matrix-Directed Cell Migration. Dev Cell. 2019;51(4):460-475 e410.

7. Tsai TY, Collins SR, Chan CK, et al. Efficient Front-Rear Coupling in Neutrophil Chemotaxis by Dynamic Myosin II Localization. Dev Cell. 2019;49(2):189-205 e186.

8. Mueller J, Szep G, Nemethova M, et al. Load Adaptation of Lamellipodial Actin Networks. Cell. 2017;171(1):188-200 e116.

9. De Belly H, Yan S, Borja da Rocha H, et al. Cell protrusions and contractions generate long-range membrane tension propagation. Cell. 2023.

10. Matthaeus C, Sochacki KA, Dickey AM, et al. The molecular organization of differentially curved caveolae indicates bendable structural units at the plasma membrane. Nat Commun. 2022;13(1):7234.

11. Sinha B, Koster D, Ruez R, et al. Cells respond to mechanical stress by rapid disassembly of caveolae. Cell. 2011;144(3):402-413.

12. Lieber AD, Schweitzer Y, Kozlov MM, Keren K. Front-to-rear membrane tension gradient in rapidly moving cells. Biophysical journal. 2015;108(7):1599-1603.

13. Shi Z, Graber ZT, Baumgart T, Stone HA, Cohen AE. Cell Membranes Resist Flow. Cell. 2018;175(7):1769-1779 e1713.

14. Grande-Garcia A, Echarri A, de Rooij J, et al. Caveolin-1 regulates cell polarization and directional migration through Src kinase and Rho GTPases. The Journal of cell biology. 2007;177(4):683-694.

15. Grande-Garcia A, del Pozo MA. Caveolin-1 in cell polarization and directional migration. Eur J Cell Biol. 2008;87(8-9):641-647.

16. Ludwig A, Howard G, Mendoza-Topaz C, et al. Molecular composition and ultrastructure of the caveolar coat complex. PLoS biology. 2013;11(8):e1001640.

Author Response

Reviewer #1 (Public Review):

The study presented by AL Seufert et al. follows the trajectory of trained immunity research in the context of sterile inflammatory diseases such as gout, cardiovascular disease and obesity. Previous studies in mice have shown that a 4 week Western-type diet is sufficient to induce systemic trained immunity, with gross reorganization of the bone marrow to support a potentiated inflammatory response [PMID: 29328911]. The current study demonstrates that mice on a Western-type diet (WD) and the more extreme Ketogenic diet (KD; where carbohydrates are essentially eliminated from the diet) for 2 weeks results in a state of increased monocyte-driven immune responsiveness when compared to standard chow diets (SC). This increased immune responsiveness after high-fat diet resulted in a deadly hyper-inflammatory in the mice in response to endotoxin (LPS) challenge in vivo.

These initial findings as displayed in Figure 1 are made difficult to interpret because the authors use a mix of male and female mice coupled with very small sample sizes (n = 5 - 9). Male and female mice are shown to have dimorphic responses to LPS exposure in vivo, with males having elevated cytokine levels (TNF, IL-6, IL1β, and also interesting IL-10) increased rates severe outcomes to LPS challenge [PMID: 27631979]. As a reader it is impossible to discern from their methodological description what the proportion of the sexes were in each group, and therefore cannot determine if their data are skewed or biased due to sexual dimorphic responses to LPS rather than diet. Additionally due to the very small sample sizes, the authors can't perform a stratified analysis based on sex to determine whether the diets are having the greatest effects in accordance with LPS induce inflammation.

The Reviewer brings up an important point, all studies with endotoxemia in wild-type conventional mice were carried out in 6–8-week female BALB/c mice, as mentioned in the Methods section under “Ethical approval of animal studies” and “endotoxin-induced model of sepsis” sections. This is extremely important to mention more clearly in the results text, because the Reviewer 1 is correct, sexual dimorphism and age differences can have very large effects on LPS treatment outcome. This was not stated clearly enough in the results and now the age, sex, and background of mice have been explicitly stated in each Results and Figure Legend section for each experiment.

When comparing SC to the KD, the authors identify large changes in fatty acid distribution circulating in the blood. The majority of the fatty acids were shown to relate to saturated fatty acids (SFA). Although Lauric, Myristic, and Myristovaccenic acid where the most altered after KD, the authors focus their research on the more thoroughly studied palmitic acid (PA).

We followed up on multiple saturated fatty acids (SFAs; Myristic, Lauric, and Behenic acid) that were identified in the lipidomic data, and found no robust or repeatable phenotypes in vitro using physiologically relevant concentrations. The inability to reproduce some of the findings with these SFAs may be due to the instability of some of these fats in solution, and plan to troubleshoot these assays in order to understand the complexity of SFA-dependent control of inflammation in macrophages. Please see Fig. R1 in this document for data showing LPS-stimulated BMDMs pre-treated with Myristic (Fig R1 A-C), Lauric (Fig R1 D-F), or Behenic (Fig R1 G-I) fatty acids. The physiological concentrations used in these studies were referenced from Perreault et. al., 2014.

Figure R1. The effect of Myristic Acid, Lauric Acid, and Behenic Acid on the response to LPS in macrophages. Primary bone marrowderived macrophages (BMDMs) were isolated from aged-matched (6-8 wk) C57BL/6 female and male mice. BMDMs were plated at 1x106 cells/mL and treated with either ethanol (EtOH; media with 0.05% or 0.35% ethanol to match MA and LA solutions respectively), media (Ctrl), LPS (10 ng/mL) for 24 h, or myristic or lauric acid (MA, LA stock diluted in 0.05%, or 0.35% EtOH; conjugated to 2% BSA) for 24 h, with and without a secondary challenge with LPS (10 ng/mL). After indicated time points, RNA was isolated and expression of (A, B) tnf, (D, E) il- 6, and (G, H) il-1β was measured via qRT-PCR. RAW 264.7 macrophages were thawed and cultured for 3-5 days, pelleted and resuspended in DMEM containing 5% FBS and 2% BSA, and treated identical to BMDM treatments with behenic acid (BA stock diluted in 1.7% EtOH) used as the primary stimulus. (C) tnf, (F) il-6, and (I) il-1β was measured via qRT-PCR. For all plates, all treatments were performed in triplicate. For all panels, a student’s t-test was used for statistical significance. p< 0.05; p < 0.01; **p< 0.001. Error bars shown mean ± SD.

PA was shown to increase the expression of inflammatory cytokines gene expression and protein production of TNF, IL-6 and IL-1β in bone marrow derived macrophages (BMDMs). The authors tie these effects to ceramide synthesis through a pharmacological blockade as well as the use of oleic acid, which allegedly sequesters ceramide synthesis. The author's claim that oleic acid supplementation reverses the inflammatory signaling induced by PA is invalid, as oleic acid was shown to induce a high level of cytokines in their model. When PA was added along with oleic acid, the cytokine levels returned to the levels produced by BMDM's stimulated with PA alone (see Figure 4 panels D- F).

This was an unfortunate oversight in our revisions of this manuscript, original Figure 5A-C was mislabeled (though colored the correct colors) – OA-12h → LPS-24h should have been switched with PA-12h → LPS-24h. These data were labeled correctly in the source file: Source_data_Fig5 and have since been updated in Figure 5 of the manuscript with correct labels. The corrected graphs have been split up in the resubmission in light of new data collected. Please see Fig 3K-M and Fig 5A-C.

Finally the authors test whether injection of PA into mice can recapitulate the systemic inflammatory response seen by WD and KD feeding followed by LPS exposure. They were able to demonstrate that injecting 1 mM of PA, waiting for 12h, and then exposing the mice to LPS for 24h could similarly result in a hyper-inflammatory state resulting in greater mortality. The reviewer is skeptical that 1 mM of PA truly represents post-prandial PA levels as one would expect to see after a single fatty meal, and whether this injection is generally well tolerated by mice. Looking into the paper cited by Eguchi et al. to inform their methods, it's shown that the earlier study continuously infused an emulsified ethyl palmitate solution (which contained 600 mM) at a rate of 0.2 uL/min. As far as I can read by Eguchi, they only managed to reach a serum PA concentration of 0.5 mM. This is hardly the same thing as a single i.p. injection of 1 mM PA. and reflects a single bolus injection of double the serum concentration of PA achieved by Eguchi et al.

The reviewer brings up an important point, Eguchi et al. did use infusions. From their data (Fig 1A), we calculated that after 600mM of i.v. injection (total = 267uL within 14h; 0.2L/min) there was ~420uM absolute PA within the blood. They were using C57BL/6 mice that were 23g on average. Using these results, we extrapolated that one single 200uL injection of a 750mM PA solution within 6–8-week female BALB/c mice (~15-18g) would equate to ~500-1mM of PA within the blood. Considering obese healthy and unhealthy humans vary widely in total PA concentrations in the blood (0.3-4.1 mM) (1, 2), we moved forward with these calculations. Considering this, we thank the reviewer for this advice, and we agree that we have not definitively shown we are increasing systemic levels of PA. Thus, we ran a lipidomic analysis of serum from SC-fed mice with Veh or PA for 12 h. We show that a 750 mM i.p. injection of ethyl palmitate enhances free PA levels in the serum to 173-425 μM at 2 h post-injection, which is within the reported range for humans on high-fat diets (0.34.1mM). We have added this new data to Fig. S7A of the main manuscript.

Importantly, the concentration in the PA-treated mice is greater than that of the Veh-treated mice, however we believe the value shown is an underestimate of maximum serum PA levels enhanced by i.p. injection, because free PA is known to be packaged into chylomicrons within enterocytes and travel through the circulation with a half-life of less than an hour (3, 4). Thus, serum concentrations of free PA are only transiently enhanced by i.p. injection, and is quickly taken up by adipose tissue, skeletal muscle, heart, and liver tissue. These complex lipid transport processes make it difficult to determine maximum concentrations of free PA in the serum.

While all of the details concerning PA circulation following an i.p. injection are unknown, we suggest that this method of “force-feeding” is similar to dietary intake in that uptake of PA into the circulation occurs within the peritoneal space prior to traveling to the blood via the thoracic duct and right lymphatic duct (5).

PA is known to induce inflammation in monocytes and macrophages, therefore the findings certainly make sense in the context of previously published literature. However the authors have made some poor methodological decisions in their mouse studies, namely haphazardly switching between groups of young and old mice (4-6 weeks, 8-9 weeks, and 14-23 weeks), using different LPS injection protocols (6, 10, and 50 mg/ml of LPS), and including multiple sexes of mice. All of which are drastically alter the interpretation of the data, and preventing solid conclusions from being drawn.

We appreciate this review and suggest that:

1) For the LPS models, mice were all female and aged matched between 6-8 weeks. We are aware of sex differences in the endotoxemia model, which is why we specifically use female mice in our studies (6, 7). This is mentioned twice in the methods under the sections “Endotoxin-induced model of sepsis” and “Ethical approval of animal studies”. We have added these specifics of our model to all Results and Figure Legend sections for clarification.

2) For Germ-free models, it is notoriously difficult to breed C57BL/6 germ-free mice. It was inherently difficult to obtain enough mice within the same sex and age to carry out these experiments, however since we have published in this model before with mixed sex and age we were aware that our WD phenotype is robust enough in these backgrounds (7). Further, we believe that seeing our robust phenotype independent of age or sex within germ-free mice provides more evidence of the strength of this phenotype. It is important to note that we induce endotoxemia within Germ-free mice with 50mg/kg, instead of 6mg/kg which is used in conventional mice, because this is our reported LD50 for mixed sex Germ-free C57BL/6, as we have published previously in detail (7). This difference is due to the presence of the microbiota (8, 9) and also germ-free mice have an immature immune system that correlates with a hyporesponsiveness to microbial products (10-12). We agree with the reviewer that the ages of the C57BL/6 germ-free mice are significantly older than our conventional 6-8 week mice, thus we confirmed that WD- and KD-fed conventional C57BL/6 female mice aged 20 – 21 weeks old still show enhanced disease severity and mortality in an LPS-induced endotoxemia model, compared to mice fed SC (Fig. S1G-H).

Figure R2. PA treatment enhances survival in both female and male RAG-/- mice. Age-matched (8-9 wk) RAG-/- mice were injected i.v. with ethyl palmitate (PA, 750mM) or vehicle (Veh) solutions 12 h before C. albicans infection. Survival was monitored for 40h post-infection.

3) In our preliminary results, we stratified survival during C. albicans infection between male and female C57BL/6 and found no notable difference in survival at 40h post IP infection with Candida albicans (Fig R2 A-B). However, the data presented in the manuscript on CFU is female kidney burden and we do not have data on fungal burden within male mice. This is an important piece of data that we would like to collect for understanding sex differences in the PA-dependent enhanced resistance to systemic C. albicans. We are currently addressing this question within the lab as well as elucidating the cell type and mechanism of PA-dependent enhanced fungal resistance.

Author Response

Reviewer #1 (Public Review):

Esmaily and colleagues report two experimental studies in which participants make simple perceptual decisions, either in isolation or in the context of a joint decision-making procedure. In this "social" condition, participants are paired with a partner (in fact, a computer), they learn the decision and confidence of the partner after making their own decision, and the joint decision is made on the basis of the most confident decision between the participant and the partner. The authors found that participants' confidence, response times, pupil dilation, and CPP (i.e. the increase of centro-parietal EEG over time during the decision process) are all affected by the overall confidence of the partner, which was manipulated across blocks in the experiments. They describe a computational model in which decisions result from a competition between two accumulators, and in which the confidence of the partner would be an input to the activity of both accumulators. This model qualitatively produced the variation in confidence and RTs across blocks.

The major strength of this work is that it puts together many ingredients (behavioral data, pupil and EEG signals, computational analysis) to build a picture of how the confidence of a partner, in the context of joint decision-making, would influence our own decision process and confidence evaluations. Many of these effects are well described already in the literature, but putting them all together remains a challenge.

We are grateful for this positive assessment.

However, the construction is fragile in many places: the causal links between the different variables are not firmly established, and it is not clear how pupil and EEG signals mediate the effect of the partner's confidence on the participant's behavior.

We have modified the language of the manuscript to avoid the implication of a causal link.

Finally, one limitation of this setting is that the situation being studied is very specific, with a joint decision that is not the result of an agreement between partners, but the automatic selection of the most confident decisions. Thus, whether the phenomena of confidence matching also occurs outside of this very specific setting is unclear.

We have now acknowledged this caveat in the discussion in line 485 to 504. The final paragraph of the discussion now reads as follows:

“Finally, one limitation of our experimental setup is that the situation being studied is confined to the design choices made by the experimenters. These choices were made in order to operationalize the problem of social interaction within the psychophysics laboratory. For example, the joint decisions were not made through verbal agreement (Bahrami et al., 2010, 2012). Instead, following a number of previous works (Bang et al., 2017, 2020) joint decisions were automatically assigned to the most confident choice. In addition, the partner’s confidence and choice were random variables drawn from a distribution prespecified by the experimenter and therefore, by design, unresponsive to the participant’s behaviour. In this sense, one may argue that the interaction partner’s behaviour was not “natural” since they did not react to the participant's confidence communications (note however that the partner’s confidence and accuracy were not entirely random but matched carefully to the participant’s behavior prerecorded in the individual session). How much of the findings are specific to these experimental setting and whether the behavior observed here would transfer to real-life settings is an open question. For example, it is plausible that participants may show some behavioral reaction to a human partner’s response time variations since there is some evidence indicating that for binary choices such as those studied here, response times also systematically communicate uncertainty to others (Patel et al., 2012). Future studies could examine the degree to which the results might be paradigm-specific.”

Reviewer #2 (Public Review):

This study is impressive in several ways and will be of interest to behavioral and brain scientists working on diverse topics.

First, from a theoretical point of view, it very convincingly integrates several lines of research (confidence, interpersonal alignment, psychophysical, and neural evidence accumulation) into a mechanistic computational framework that explains the existing data and makes novel predictions that can inspire further research. It is impressive to read that the corresponding model can account for rather non-intuitive findings, such as that information about high confidence by your collaborators means people are faster but not more accurate in their judgements.

Second, from a methodical point of view, it combines several sophisticated approaches (psychophysical measurements, psychophysical and neural modelling, electrophysiological and pupil measurements) in a manner that draws on their complementary strengths and that is most compelling (but see further below for some open questions). The appeal of the study in that respect is that it combines these methods in creative ways that allow it to answer its specific questions in a much more convincing manner than if it had used just either of these approaches alone.

Third, from a computational point of view, it proposes several interesting ways by which biologically realistic models of perceptual decision-making can incorporate socially communicated information about other's confidence, to explain and predict the effects of such interpersonal alignment on behavior, confidence, and neural measurements of the processes related to both. It is nice to see that explicit model comparison favor one of these ways (top-down driving inputs to the competing accumulators) over others that may a priori have seemed more plausible but mechanistically less interesting and impactful (e.g., effects on response boundaries, no-decision times, or evidence accumulation).

Fourth, the manuscript is very well written and provides just the right amount of theoretical introduction and balanced discussion for the reader to understand the approach, the conclusions, and the strengths and limitations.

Finally, the manuscript takes open science practices seriously and employed preregistration, a replication sample, and data sharing in line with good scientific practice.

We are grateful to the reviewer for their positive assessment of our work.

Having said all these positive things, there are some points where the manuscript is unclear or leaves some open questions. While the conclusions of the manuscript are not overstated, there are unclarities in the conceptual interpretation, the descriptions of the methods, some procedures of the methods themselves, and the interpretation of the results that make the reader wonder just how reliable and trustworthy some of the many findings are that together provide this integrated perspective.

We hope that our modifications and revisions in response to the criticisms listed below will be satisfactory. To avoid redundancies, we have combined each numbered comment with the corresponding recommendation for the Authors.

First, the study employs rather small sample sizes of N=12 and N=15 and some of the effects are rather weak (e.g., the non-significant CPP effects in study 1). This is somewhat ameliorated by the fact that a replication sample was used, but the robustness of the findings and their replicability in larger samples can be questioned.

Our study brings together questions from two distinct fields of neuroscience: perceptual decision making and social neuroscience. Each of these two fields have their own traditions and practical common sense. Typically, studies in perceptual decision making employ a small number of extensively trained participants (approximately 6 to 10 individuals). Social neuroscience studies, on the other hand, recruit larger samples (often more than 20 participants) without extensive training protocols. We therefore needed to strike a balance in this trade-off between number of participants and number of data points (e.g. trials) obtained from each participant. Note, for example, that each of our participants underwent around 4000 training trials. Strikingly, our initial study (N=12) yielded robust results that showed the hypothesized effects nearly completely, supporting the adequacy of our power estimate. However, we decided to replicate the findings because, like the reviewer, we believe in the importance of adequate sampling. We increased our sample size to N=15 participants to enhance the reliability of our findings. However, we acknowledge the limitation of generalizing to larger samples, which we have now discussed in our revised manuscript and included a cautionary note regarding further generalizations.

To complement our results and add a measure of their reliability, here we provide the results of a power analysis that we applied on the data from study 1 (i.e. the discovery phase). These results demonstrate that the sample size of study 2 (i.e. replication) was adequate when conditioned on the results from study 1 (see table and graph pasted below). The results showed that N=13 would be an adequate sample size for 80% power for behavoural and eye-tracking measurements. Power analysis for the EEG measurements indicated that we needed N=17. Combining these power analyses. Our sample size of N=15 for Study 2 was therefore reasonably justified.

We have now added a section to the discussion (Lines 790-805) that communicates these issues as follows:

“Our study brings together questions from two distinct fields of neuroscience: perceptual decision making and social neuroscience. Each of these two fields have their own traditions and practical common sense. Typically, studies in perceptual decision making employ a small number of extensively trained participants (approximately 6 to 10 individuals). Social neuroscience studies, on the other hand, recruit larger samples (often more than 20 participants) without extensive training protocols. We therefore needed to strike a balance in this trade-off between number of participants and number of data points (e.g. trials) obtained from each participant. Note, for example, that each of our participants underwent around 4000 training trials. Importantly, our initial study (N=12) yielded robust results that showed the hypothesized effects nearly completely, supporting the adequacy of our power estimate. However, we decided to replicate the findings in a new sample with N=15 participants to enhance the reliability of our findings and examine our hypothesis in a stringent discovery-replication design. In Figure 4-figure supplement 5, we provide the results of a power analysis that we applied on the data from study 1 (i.e. the discovery phase). These results demonstrate that the sample size of study 2 (i.e. replication) was adequate when conditioned on the results from study 1.”

We conducted Monte Carlo simulations to determine the sample size required to achieve sufficient statistical power (80%) (Szucs & Ioannidis, 2017). In these simulations, we utilized the data from study 1. Within each sample size (N, x-axis), we randomly selected N participants from our 12 partpincats in study 1. We employed the with-replacement sampling method. Subsequently, we applied the same GLMM model used in the main text to assess the dependency of EEG signal slopes on social conditions (HCA vs LCA). To obtain an accurate estimate, we repeated the random sampling process 1000 times for each given sample size (N). Consequently, for a given sample size, we performed 1000 statistical tests using these randomly generated datasets. The proportion of statistically significant tests among these 1000 tests represents the statistical power (y-axis). We gradually increased the sample size until achieving an 80% power threshold, as illustrated in the figure.The the number indicated by the red circle on the x axis of this graph represents the designated sample size.

Second, the manuscript interprets the effects of low-confidence partners as an impact of the partner's communicated "beliefs about uncertainty". However, it appears that the experimental setup also leads to greater outcome uncertainty (because the trial outcome is determined by the joint performance of both partners, which is normally reduced for low-confidence partners) and response uncertainty (because subjects need to consider not only their own confidence but also how that will impact on the low-confidence partner). While none of these other possible effects is conceptually unrelated to communicated confidence and the basic conclusions of the manuscript are therefore valid, the reader would like to understand to what degree the reported effects relate to slightly different types of uncertainty that can be elicited by communicated low confidence in this setup.

We appreciate the reviewer’s advice to remain cautious about the possible sources of uncertainty in our experiment. In the Discussion (lines 790-801) we have now added the following paragraph.

“We have interpreted our findings to indicate that social information, i.e. partner’s confidence, impacts the participants beliefs about uncertainty. It is important to underscore here that, similar to real life, there are other sources of uncertainty in our experimental setup that could affect the participants' belief. For example, under joint conditions, the group choice is determined through the comparison of the choices and confidences of the partners. As a result, the participant has a more complex task of matching their response not only with their perceptual experience but also coordinating it with the partner to achieve the best possible outcome. For the same reason, there is greater outcome uncertainty under joint vs individual conditions. Of course, these other sources of uncertainty are conceptually related to communicated confidence but our experimental design aimed to remove them, as much as possible, by comparing the impact of social information under high vs low confidence of the partner.”

In addition to the above, we would like to clarify one point here with specific respect to the comment. Note that the computer-generated partner’s accuracy was identical under high and low confidence. In addition, our behavioral findings did not show any difference in accuracy under HCA and LCA conditions. As a consequence, the argument that “the trial outcome is determined by the joint performance of both partners, which is normally reduced for low-confidence partners)” is not valid because the low-confidence partner’s performance is identical to that of the high-confidence partner. It is possible, of course, that we have misunderstood the reviewer’s point here and we would be happy to discuss this further if necessary.

Third, the methods used for measurement, signal processing, and statistical inference in the pupil analysis are questionable. For a start, the methods do not give enough details as to how the stimuli were calibrated in terms of luminance etc so that the pupil signals are interpretable.

Here we provide in Author response image 1 the calibration plot for our eye tracking setup, describing the relationship between pupil size and display luminance. Luminance of the random dot motion stimuli (ie white dots on black background) was Cd/m2 and, importantly, identical across the two critical social conditions. We hope that this additional detail satisfies the reviewer’s concern. For the purpose of brevity, we have decided against adding this part to the manuscript and supplementary material.

Author response image 1.

Calibration plot for the experimental setup. Average pupil size (arbitrary units from eyelink device) is plotted against display luminance. The plot is obtained by presenting the participant with uniform full screen displays with 10 different luminance levels covering the entire range of the monitor RGB values (0 to 255) whose luminance was separately measured with a photometer. Each display lasted 10 seconds. Error bars are standard deviation between sessions.

Moreover, while the authors state that the traces were normalized to a value of 0 at the start of the ITI period, the data displayed in Figure 2 do not show this normalization but different non-zero values. Are these data not normalized, or was a different procedure used? Finally, the authors analyze the pupil signal averaged across a wide temporal ITI interval that may contain stimulus-locked responses (there is not enough information in the manuscript to clearly determine which temporal interval was chosen and averaged across, and how it was made sure that this signal was not contaminated by stimulus effects).

We have now added the following details to the Methods section in line 1106-1135.

“In both studies, the Eye movements were recorded by an EyeLink 1000 (SR- Research) device with a sampling rate of 1000Hz which was controlled by a dedicated host PC. The device was set in a desktop and pupil-corneal reflection mode while data from the left eye was recorded. At the beginning of each block, the system was recalibrated and then validated by 9-point schema presented on the screen. For one subject was, a 3-point schema was used due to repetitive calibration difficulty. Having reached a detection error of less than 0.5°, the participants proceeded to the main task. Acquired eye data for pupil size were used for further analysis. Data of one subject in the first study was removed from further analysis due to storage failure.

Pupil data were divided into separate epochs and data from Inter-Trials Interval (ITI) were selected for analysis. ITI interval was defined as the time between offset of trial (t) feedback screen and stimulus presentation of trial (t+1). Then, blinks and jitters were detected and removed using linear interpolation. Values of pupil size before and after the blink were used for this interpolation. Data was also mid-pass filtered using a Butterworth filter (second order,[0.01, 6] Hz)[50]. The pupil data was z-scored and then was baseline corrected by removing the average of signal in the period of [-1000 0] ms interval (before ITI onset). For the statistical analysis (GLMM) in Figure 2, we used the average of the pupil signal in the ITI period. Therefore, no pupil value is contaminated by the upcoming stimuli. Importantly, trials with ITI>3s were excluded from analysis (365 out of 8800 for study 1 and 128 out 6000 for study 2. Also see table S7 and Selection criteria for data analysis in Supplementary Materials)”

Fourth, while the EEG analysis in general provides interesting data, the link to the well-established CPP signal is not entirely convincing. CPP signals are usually identified and analyzed in a response-locked fashion, to distinguish them from other types of stimulus-locked potentials. One crucial feature here is that the CPPs in the different conditions reach a similar level just prior to the response. This is either not the case here, or the data are not shown in a format that allows the reader to identify these crucial features of the CPP. It is therefore questionable whether the reported signals indeed fully correspond to this decision-linked signal.

Fifth, the authors present some effective connectivity analysis to identify the neural mechanisms underlying the possible top-down drive due to communicated confidence. It is completely unclear how they select the "prefrontal cortex" signals here that are used for the transfer entropy estimations, and it is in fact even unclear whether the signals they employ originate in this brain structure. In the absence of clear methodical details about how these signals were identified and why the authors think they originate in the prefrontal cortex, these conclusions cannot be maintained based on the data that are presented.

Sixth, the description of the model fitting procedures and the parameter settings are missing, leaving it unclear for the reader how the models were "calibrated" to the data. Moreover, for many parameters of the biophysical model, the authors seem to employ fixed parameter values that may have been picked based on any criteria. This leaves the impression that the authors may even have manually changed parameter values until they found a set of values that produced the desired effects. The model would be even more convincing if the authors could for every parameter give the procedures that were used for fitting it to the data, or the exact criteria that were used to fix the parameter to a specific value.

Seventh, on a related note, the reader wonders about some of the decisions the authors took in the specification of their model. For example, why was it assumed that the parameters of interest in the three competing models could only be modulated by the partner's confidence in a linear fashion? A non-linear modulation appears highly plausible, so extreme values of confidence may have much more pronounced effects. Moreover, why were the confidence computations assumed to be finished at the end of the stimulus presentation, given that for trials with RTs longer than the stimulus presentation, the sensory information almost certainly reverberated in the brain network and continued to be accumulated (in line with the known timing lags in cortical areas relative to objective stimulus onset)? It would help if these model specification choices were better justified and possibly even backed up with robustness checks.

Eight, the fake interaction partners showed several properties that were highly unnatural (they did not react to the participant's confidence communications, and their response times were random and thus unrelated to confidence and accuracy). This questions how much the findings from this specific experimental setting would transfer to other real-life settings, and whether participants showed any behavioral reactions to the random response time variations as well (since several studies have shown that for binary choices like here, response times also systematically communicate uncertainty to others). Moreover, it is also unclear how the confidence convergence simulated in Figure 3d can conceptually apply to the data, given that the fake subjects did not react to the subject's communicated confidence as in the simulation.

Author Response

Reviewer #1 (Public Review):

This work by Shen et al. demonstrates a single molecule imaging method that can track the motions of individual protein molecules in dilute and condensed phases of protein solutions in vitro. The authors applied the method to determine the precise locations of individual molecules in 2D condensates, which show heterogeneity inside condensates. Using the time-series data, they could obtain the displacement distributions in both phases, and by assuming a two-state model of trapped and mobile states for the condensed phase, they could extract diffusion behaviors of both states. This approach was then applied to 3D condensate systems, and it was shown that the estimates from the model (i.e., mobile fraction and diffusion coefficients) are useful to quantitatively compare the motions inside condensates. The data can also be used to reconstruct the FRAP curves, which experimentally quantify the mobility of the protein solution.

This work introduces an experimental method to track single molecules in a protein solution and analyzes the data based on a simple model. The simplicity of the model helps a clear understanding of the situation in a test tube, and I think that the model is quite useful in analyzing the condensate behaviors and it will benefit the field greatly. However, the manuscript in its current form fails to situate the work in the right context; many previous works are omitted in this manuscript, exaggerating the novelty of the work. Also, the two- state model is simple and useful, but I am concerned about the limits of the model. They extract the parameters from the experimental data by assuming the model. It is also likely that the molecules have a continuum between fully trapped and fully mobile states, and that this continuum model can also explain the experimental data well.

We thank the reviewer for the warm overview of our work and the insightful comments on the areas that need to be improved. We are very encouraged by the reviewer’s general positive assessment of our approach. We have addressed these comments in the revised manuscript

Reviewer #2 (Public Review):

In this paper, Shen and co-workers report the results of experiments using single particle tracking and FRAP combined with modeling and simulation to study the diffusion of molecules in the dense and dilute phases of various kinds of condensates, including those with strong specific interactions as well as weak specific interactions (IDR-driven). Their central finding is that molecules in the dense phase of condensates with strong specific interactions tend to switch between a confined state with low diffusivity and a mobile state with a diffusivity that is comparable to that of molecules in the dilute phase. In doing so, the study provides experimental evidence for the effect of molecular percolation in biomolecular condensates.

Overall, the experiments are remarkably sophisticated and carefully performed, and the work will certainly be a valuable contribution to the literature. The authors' inquiry into single particle diffusivity is useful for understanding the dynamics and exchange of molecules and how they change when the specific interaction is weak or strong. However, there are several concerns regarding the analysis and interpretation of the results that need to be addressed, and some control experiments that are needed for appropriate interpretation of the results, as detailed further below.

We thank the reviewer for the warm support of our work (assessing that our work is “remarkably sophisticated and carefully performed” and “will certainly be a valuable contribution”) and for the constructive comments/critiques, which we have now addressed in the revised manuscript (please refer to our detailed responses below).

(1) The central finding that the molecules tend to experience transiently confined states in the condensed phase is remarkable and important. This finding is reminiscent of transient "caging"/"trapping" dynamics observed in diverse other crowded and confined systems. Given this, it is very surprising to see the authors interpret the single-molecule motion as being 'normal' diffusion (within the context of a two-state diffusion model), instead of analyzing their data within the context of continuous time random walks or anomalous diffusion, which is generally known to arise from transient trapping in crowded/confined systems. It is not clear that interpreting the results within the context of simple diffusion is appropriate, given their general finding of the two confined and mobile states. Such a process of transient trapping/confinement is known to lead to transient subdiffusion at short times and then diffusive behavior at sufficiently long times. There is a hint of this in the inset of Fig 3, but these data need to be shown on log-log axes to be clearly interpreted. I encourage the authors to think more carefully and critically about the nature of the diffusive model to be used to interpret their results.

We thank the reviewer for the insightful comments and suggestions, which have been very helpful for us to think deeper about the experimental data and the possible underlying mechanism of our findings. Indeed, the phase separated systems studied here resemble previously studied crowed and confined systems with transient caging/trapping dynamics in the literature ((Akimoto et al., 2011; Bhattacharjee and Datta, 2019; Wong et al., 2004) for examples)(references have been added in the revised manuscript). In our PSD system in Figure 3, The caging/trapping of NR2B in the condensed phase is likely due to its binding to the percolated PSD network. Thus, NR2B molecules in the condensed phase should undergo subdiffusive motions. Indeed, from our single molecule tracking data, the motion of NR2B fits well with the continuous time random walk (CTRW) model, as surmised by this reviewer. We have now fitted the MSD curve of all tracks of NR2B in the condensed phase with an anomalous diffusion model: MSD(t)=4Dtα (see Response Figure 1 below). The fitted α is 0.74±0.03, indicating that NR2B molecules in the condensed phase indeed undergo sub- diffusive motions. The fitted diffusion coefficient D is 0.014±0.001 μm2/s. We have now replaced the Brownian motion fitting in Figure 3E in the original manuscript with this sub- diffusive model fitting in the revised manuscript to highlight the complexity of NR2B diffusion in PSD condensed phase we observed.

Response Figure 1: Fitted the MSD curve (mean value as red dot with standard error as error bar) in condensed phase with an anomalous diffusion model (blue curve, MSD=4Dtα). The fitting gives D=0.014±0.001 μm2/s and α=0.74±0.03.

We find it useful to interpret the apparent diffusion coefficient (D=0.014±0.001 μm2/s) derived from this particular anomalous diffusion model as containing information of NR2B motions in a broadly construed mobile state (i.e., corresponding to the network unbound form) as well as in a broadly construed confined state (i.e., corresponding to NR2B molecules bound to percolated PSD networks). The global fitting using the sub-diffusive model does not pin down motion properties of NR2B in these different motion states. This is why we used, at least as a first approximation, the two-state motion switch model (HMM model) to analyse our data (please refer also to our detailed response to the comment #7 from reviewer 1 and corresponding additional analyses made during the revision as highlighted in Response Figure 4).

As described in our response to the comment points #4 and #7 from reviewer 1, the two- state model is most likely a simplification of NR2B motions in the condensed phase. Both the mobile state and the confined state in our simplified interpretative framework likely represent ensemble averages of their respective motion states. However, the tracking data available currently do not allow us to further distinguish the substates, but further analysis using more refined model in the future may provide more physical insight, as we now emphasize in the revised “Discussion” section: “With this in mind, the two motion states in our simple two-state model for condensed-phase dynamics should be understood to be consisting of multiple sub-states. For instance, one might envision that the percolated molecular network in the condensed phase is not uniform (e.g., existence of locally denser or looser local networks) and dynamic (i.e., local network breaking and forming). Therefore, individual proteins binding to different sub-regions of the network will have different motion properties/states. … In light of this basic understanding, the “confined state” and “mobile state” as well as the derived diffusion coefficients in this work should be understood as reflections of ensemble-averaged properties arising from such an underlying continuum of mobilities. Further development of experimental techniques in conjunction with more refined models of anomalous diffusion (Joo et al., 2020; Kuhn et al., 2021; Muñoz-Gil et al., 2021) will be necessary to characterize these more subtle dynamic properties and to ascertain their physical origins” (p.23 of the revised manuscript).

A practical reason for using the two-state motion switch HMM model to analyse our tracking data in the condensed phase is that the lifetime of the putative mobile state (when the per-frame molecular displacements are relatively large) is very short and such relatively faster short trajectories are interspersed by long confined states (see Response Figure 4C for an example). Statistically, ascertaining a particular anomalous diffusion model by fitting to such short tracks is likely not reliable. Therefore, here we opted for a semi-quantitative interpretative framework by using fitted diffusion coefficients in a two-state HMM as well as the new correlation-based approach for demarcating a low-mobility state and a high- mobility state (see our detailed response to reviewer 1’s point #7) in the present manuscript (which is quite an extensive study already) while leaving refinements of our computational modelling to future effort.

Even in the context of the 'normal' two-state diffusion model they present, if they wish to stick with that-although it seems inappropriate to do so-can the authors provide some physical intuition for what exactly sets the diffusivities they extract from their data. (0.17 and 0.013 microns squared per second for the mobile and confined states). Can these be understood using e.g., the Stoke-Einstein or Ogston models somehow?

As stated above, we are in general agreement with this reviewer that the motion of NR2B in the condensed phase is more complex than the simple two-state picture we adopted as a semi-quantitative interpretation that is adequate for our present purposes. Within the multi-pronged analysis we have performed thus far, NR2B molecules clearly undergo anomalous diffusions in solution containing dense, percolated, and NR2B-binding molecular networks. As a first approximation, our simple two-state HMM analysis yielded two simple diffusion coefficients (0.17 μm2/s for the mobile state and 0.013 μm2/s for the confined state). For the diffusion coefficient in the mobile state, we regard it as providing a time scale for relatively faster diffusive motions (which may be further classified into various motion substates in the future) that are not bound or only weakly associated with the percolated network of strong interactions in the PSD condensed phase. For the confined or low-mobility state in our present formulation, these molecules are likely bound relatively tightly to the percolated networks, thus the diffusion coefficient should be much smaller than the unbounded form (i.e., the mobile state) according to the Stoke-Einstein model. However, due to the detection limitation of the supper resolution imaging method (resolution of ~20 nm), we could not definitively tell the actual diffusivity beyond the resolution limit. So the diffusion coefficient in the confined state can also be interpreted as a Gaussian distributed microscope detection error (𝑓(𝑥) =1 , which is x~N(0, σ2), where σ is the standard deviation of the Gaussian distribution viewed as the resolution of localization-based microscopy, x is the detection error between recorded localization and molecule’s actual position). The track length in the confined state is the distance between localizations in consecutive frames, which can be calculated by subtraction of two independent Gaussian distributions, and the distribution of this track length (r) will be r~N(0, 2σ2). To link the detection error with the fitted diffusion coefficient, we calculated the log likelihood function of Gaussian distributed localization error (, where σ is the standard deviation of the Gaussian distribution) for the maximum likelihood estimation process to fit the HMM model. The random walk shares a similar log likelihood term () in performing maximum likelihood estimation.

These two log likelihood functions will produce same fitting results with 2σ2 equivalent to 4Dt according to the likelihood function. In this way, the diffusion coefficient yielded by our HMM analyses for the confined state (0.0127 μm2/s) can be interpreted as the standard deviation of localization detection error (or microscope resolution limit), which is 𝜎 =√2𝐷𝑡 = 19.5 𝑛𝑚. We have included this consideration as an alternate interpretation of the confined-state or low-mobility motions with the results now provided in the “Materials and Methods” section in the sentence, viz., “… the L-component distribution may be reasonably fitted (albeit with some deviations, see below) to a simple-diffusion functional form with a parameter s =13.6 ± 3.7 nm, where s may be interpreted as a microscope detection error due to imaging limits or alternately expressed as s = DLt with DL = 0.006149 μm2/s being the fitted confined-state diffusion coefficient and t = 0.03s is the time interval of the time step between experimental frames. (The HMM-estimated confined-state Dc = 0.0127 μm2/s corresponds to s = 19.5 nm)” (p.32 of the revised manuscript).

(2) Equation 1 (and hence equation 2) is concerning. Consider a limit when P_m=1, that is, in the condensed phase, there are no confined particles, then the model becomes a diffusion equation with spatially dependent diffusivity, \partial c /\partial t = \nabla * (D(x) \nabla c). The molecules' diffusivity D(x) is D_d in the dilute phase and D_m in the condensed phase. No matter what values D_d and D_m are, at equilibrium the concentration should always be uniform everywhere. According to Equation 1, the concentration ratio will be D_d/D_m, so if D_d/D_m \neq 1, a concentration gradient is generated spontaneously, which violates the second law of thermodynamics. Can the authors please justify the use of this equation?

Indeed, the derivation of Equation 1 appears to be concerning. The flux J is proportional to D * dc/dx (not kDc as in the manuscript). At equilibrium dc/dx = 0 on both sides and c is constant everywhere. Can the authors please comment?

So then another question is, why does the Monte Carlo simulation result agree with Equation 1? I suspect this has to do with the behavior of particles crossing the boundary. Consider another limit where D_m = 0, that is, particles freeze in the condensed phase. If once a particle enters the condensed phase, it cannot escape, then eventually all particles will end up in the condensed phase and EF=infty. The authors likely used this scheme. But as mentioned above this appears to violate the second law.

Thanks for the incisive comment. After much in-depth considerations, we are in agreement with the reviewer that Eq.1 should not be presented as a relation that is generally applicable to diffusive motions of molecules in all phase-separated systems. There are cases in which this relation can need to unphysical outcomes as correctly pointed out by the reviewer.

Nonetheless, based on our theoretical/computational modeling, it is also clear, empirically, that Eq.1 holds approximately for the NR2B/PSD system we studied, and as such it is a useful approximate relation in our analysis. We have therefore provided a plausible physical perspective for Eq.1’s applicability as an approximate relation based upon a schematic consideration of diffusion on an underlying rugged (free) energy landscape (Zhang and Chan, 2012) of a phase-separated system (See Figure 3G in the revised manuscript), while leaving further studies of such energy landscape models to future investigations.

This additional perspective is now included in the following added passage under a new subheading in the revised manuscript:

"Physical picture and a two-state, two-phase diffusion model for equilibrium and dynamic properties of PSD condensates"

(3) Despite the above two major concerns described in (1) and (2), the enrichment due to the presence of a "confined state", is reasonable. The equilibrium between "confined" and "mobile" states is determined by its interaction with the other proteins and their ratio at equilibrium corresponds to the equilibrium constant. Therefore EF=1/Pm is reasonable and comes solely from thermodynamics. In fact, the equilibrium partition between the dilute and dense phases should solely be a thermodynamic property, and therefore one may expect that it should not have anything to do with diffusivity. Can the authors please comment on this alternative interpretation?

Thanks for this thought-provoking comment. We agree with the reviewer that the relative molecular densities in the condensed versus dilute phases are governed by thermodynamics unless there is energy input into the system. However, in our formulation, the mobile ratio should not be the only parameters for determining the enrichment fold in a phase separated system. In fact, the approximate relation (Eq.1) is EF ≈ Dd/PmDm, and thus EF ≈ 1/Pm only when Dd ≈ Dm . But the speed of mobile-state diffusion in the condensed phase is found to be appreciably smaller than that of diffusion in the dilute phase (Dd > Dm). In general, a hallmark of a phase separation system is to enrich involved molecules in the condensed phase, regardless whether the molecule is a driver (or scaffold) or a client of the system. Such enrichment is expected to be resulted from the net free energy gain due to increased molecular interactions of the condensed phase (as envisioned in Response Figure 9). For example, in the phase separation systems containing PrLD-SAMME (Figure 4 of the manuscript), Pm is close to 1, but the enrichment of PrLD-SAMME in the condensed phase is much greater than 1 (estimated to be ~77, based on the fluorescence intensity of the protein in the dilute and condensed phase; Figure 5—figure supplement 1). As far as Eq.1 is concerned, this is mathematically correct because the diffusion coefficient of PrLD-SAMME in the condensed phase (D ~0.2 μm2/s) is much smaller than the diffusion coefficient of a monomeric molecule with a similar molecular mass in dilute solution (D~ 100 μm2/s, measured by FRAP-based assay; the mobility of the molecules in the dilute solution in 3D is too fast to be tracked). Physically, it’s most likely that the slower molecular motion in the condensed phase is caused by favorable intermolecular interactions and the same favorable interactions underpinning the dynamic effects lead also to a larger equilibrium Boltzmann population.

Author Response

Reviewer #1 (Public Review):

The authors set out to extend modeling of bispecific engager pharmacology through explicit modelling of the search of T cells for tumour cells, the formation of an immunological synapse and the dissociation of the immunological synapse to enable serial killing. These features have not been included in prior models and their incorporation may improve the predictive value of the model.

Thank you for the positive feedback.

The model provides a number of predictions that are of potential interest- that loss of CD19, the target antigen, to 1/20th of its initial expression will lead to escape and that the bone marrow is a site where the tumour cells may have the best opportunity to develop loss variants due to the limited pressure from T cells.

Thank you for the positive feedback.

A limitation of the model is that adhesion is only treated as a 2D implementation of the blinatumomab mediated bridge between T cell and B cells- there is no distinct parameter related to the distinct adhesion systems that are critical for immunological synapse formation. For example, CD58 loss from tumours is correlated with escape, but it is not related to the target, CD19. While they begin to consider the immunological synapse, they don't incorporate adhesion as distinct from the engager, which is almost certainly important.

We agree that adhesion molecules play critical roles in cell-cell interaction. In our model, we assumed these adhesion molecules are constant (or not showing difference across cell populations). This assumption made us to focus on the BiTE-mediated interactions.

Revision: To clarify this point, we added a couple of sentences in the manuscript.

“Adhesion molecules such as CD2-CD58, integrins and selectins, are critical for cell-cell interaction. The model did not consider specific roles played by these adhesion molecules, which were assumed constant across cell populations. The model performed well under this simplifying assumption”.

In addition, we acknowledged the fact that “synapse formation is a set of precisely orchestrated molecular and cellular interactions. Our model merely investigated the components relevant to BiTE pharmacologic action and can only serve as a simplified representation of this process”.

While the random search is a good first approximation, T cell behaviour is actually guided by stroma and extracellular matrix, which are non-isotropic. In a lymphoid tissue the stroma is optimised for a search that can be approximated as brownian, or more accurately, a correlated random walk, but in other tissues, particularly tumours, the Brownian search is not a good approximation and other models have been applied. It would be interesting to look at observations from bone marrow or other sites to determine the best approximating for the search related to BiTE targets.

We agree that the tissue stromal factors greatly influence the patterns of T cell searching strategy. Our current model considered Brownian motion as a good first approximation for two reasons: 1) we define tissues as homogeneous compartments to attain unbiased evaluations of factors that influence BiTE-mediated cell-cell interaction, such as T cell infiltration, T: B ratio, and target expression. The stromal factors were not considered in the model, as they require spatially resolved tissue compartments to represent the gradients of stromal factors; 2) our model was primarily calibrated against in vitro data obtained from a “well-mixed” system that does not recapitulate specific considerations of tissue stromal factors. We did not obtain tissue-specific data to support the prediction of T cell movement. This is under current investigation in our lab. Therefore, we are cautious about assuming different patterns of T cell movement in the model when translating into in vivo settings. We acknowledged the limitation of our model for not considering the more physiologically relevant T-cell searching strategies.

Revision: In the Discussion, we added a limitation of our model: “We assumed Brownian motion in the model as a good first approximation of T cell movement. However, T cells often take other more physiologically relevant searching strategies closely associated with many stromal factors. Because of these stromal factors, the cell-cell encounter probabilities would differ across anatomical sites.”

Reviewer #3 (Public Review):

Liu et al. combined mechanistic modeling with in vitro experiments and data from a clinical trial to develop an in silico model to describe response of T cells against tumor cells when bi-specific T cell engager (BiTE) antigens, a standard immunotherapeutic drug, are introduced into the system. The model predicted responses of T cell and target cell populations in vitro and in vivo in the presence of BiTEs where the model linked molecular level interactions between BiTE molecules, CD3 receptors, and CD19 receptors to the population kinetics of the tumor and the T- cells. Furthermore, the model predicted tumor killing kinetics in patients and offered suggestions for optimal dosing strategies in patients undergoing BiTE immunotherapy. The conclusions drawn from this combined approach are interesting and are supported by experiments and modeling reasonably well. However, the conclusions can be tightened further by making some moderate to minor changes in their approach. In addition, there are several limitations in the model which deserves some discussion.

Strengths

A major strength of this work is the ability of the model to integrate processes from the molecular scales to the populations of T cells, target cells, and the BiTE antibodies across different organs. A model of this scope has to contain many approximations and thus the model should be validated with experiments. The authors did an excellent job in comparing the basic and the in vitro aspects of their approach with in vitro data, where they compared the numbers of engaged target cells with T cells as the numbers of the BiTE molecules, the ratio of effector and target cells, and the expressions of the CD3 and CD19 receptors were varied. The agreement with the model with the data were excellent in most cases which led to several mechanistic conclusions. In particular, the study found that target cells with lower CD19 expressions escape the T cell killing.

The in vivo extension of the model showed reasonable agreements with the kinetics of B cell populations in patients where the data were obtained from a published clinical trial. The model explained differences in B cell population kinetics between responders and non-responders and found that the differences were driven by the differences in the T cell numbers between the groups. The ability of the model to describe the in vivo kinetics is promising. In addition, the model leads to some interesting conclusions, e.g., the model shows that the bone marrow harbors tumor growth during the BiTE treatment. The authors then used the model to propose an alternate dosage scheme for BiTEs that needed a smaller dose of the drug.

Thank you for the positive comments.

Weaknesses

There are several weaknesses in the development of the model. Multiscale models of this nature contain parameters that need to be estimated by fitting the model with data. Some these parameters are associated with model approximations or not measured in experiments. Thus, a common practice is to estimate parameters with some 'training data' and then test model predictions using 'test data'. Though Supplementary file 1 provides values for some of the parameters that appeared to be estimated, it was not clear which dataset were used for training and which for test. The confidence intervals of the estimated parameters and the sensitivity of the proposed in vivo dosage schemes to parameter variations were unclear.

We agree with the reviewer on the model validation.

Revision: To ensure reproducibility, we summarized model assumptions and parameter values/sources in the supplementary file 1. To mimic tumor heterogeneity and evolution process, we applied stochastic agent-based models, which are challenging to be globally optimized against the data. The majority of key parameters was obtained or derived from the literature. Details have been provided in the response to Reviewer 3 - Question 1. In our modeling process, we manually optimized sensitive coefficient (β) for base model using pilot in-vitro data and sensitive coefficient (β) for in-vivo model by re-calibrating against the in-vitro data at a low BiTE concentration. BiTE concentrations in patients (mostly < 2 ng/ml) is only relevant to the low bound of the concentration range we investigated in vitro (0.65-2000 ng/ml). We have added some clarification/limitation of this approach in the text (details are provided in the following question). We understand the concerns, but the agent-based modeling nature prevent us to do global optimization.

The model appears to show few unreasonable behaviors and does not agree with experiments in several cases which could point to missing mechanisms in the model. Here are some examples. The model shows a surprising decrease in the T cell-target cell synapse formation when the affinity of the BiTEs to CD3 was increased; the opposite should have been more intuitive. The authors suggest degradation of CD3 could be a reason for this behavior. However, this probably could be easily tested by removing CD3 degradation in the model. Another example is the increase in the % of engaged effector cells in the model with increasing CD3 expressions does not agree well with experiments (Fig. 3d), however, a similar fold increase in the % of engaged effector cells in the model agrees better with experiments for increasing CD19 expressions (Fig. 3e). It is unclear how this can be explained given CD3 and CD19 appears to be present in similar copy numbers per cell (~104 molecules/cell), and both receptors bind the BiTE with high affinities (e.g., koff < 10-4 s-1).

Thank you for pointing this out. The bidirectional effect of CD3 affinity on IS formation is counterintuitive. In a hypothetical situation when there is no CD3 downregulation, the bidirectional effect disappears (as shown below), consistent with our view that CD3 downregulation accounts for the counterintuitive behavior. We have included the simulation to support our point. From a conceptual standpoint, the inclusion of CD3 degradation means the way to maximize synapse formation is for the BiTE to first bind tumor antigen, after which the tumor-BiTE complex “recruits” a T cell through the CD3 arm.

We agree that the model did not adequately capture the effect of CD3 expression at the highest BiTE concentration 100 ng/ml, while the effects at other BiTE concentrations were well captured (as shown below, left). The model predicted a much moderate effect of CD3 expression on IS formation at the highest concentration. This is partly because the model assumed rapid CD3 downregulation upon antibody engagement. We did a similar simulation as above, with moderate CD3 downregulation (as shown below, right). This increases the effect of CD3 expression at the highest BiTE concentration, consistent with experiments. Interestingly, a rapid CD3 downregulation rate, as we concluded, is required to capture data profiles at all other conditions. Considering BiTE concentration at 100 ng/ml is much higher than therapeutically relevant level in circulation (< 2 ng/ml), we did not investigate the mechanism underlying this inconsistent model prediction but we acknowledged the fact that the model under-predicted IS formation in Figure 3d. Notably, this discrepancy may rarely appear in our clinical predictions as the CD3 expression is low level and blood BiTE concentration is very low (< 2 ng/ml).

Revision: we have made text adjustment to increase clarity on these points. In addition, we added: “The base model underpredicted the effect of CD3 expression on IS formation at 100 ng/ml BiTE concentration, which is partially because of the rapid CD3 downregulation upon BiTE engagement and assay variation across experimental conditions.”

The model does not include signaling and activation of T cells as they form the immunological synapse (IS) with target cells. The formation IS leads to aggregation of different receptors, adhesion molecules, and kinases which modulate signaling and activation. Thus, it is likely the variations of the copy numbers of CD3, and the CD19-BiTE-CD3 will lead to variations in the cytotoxic responses and presumably to CD3 degradation as well. Perhaps some of these missing processes are responsible for the disagreements between the model and the data shown in Fig. 3. In addition, the in vivo model does not contain any development of the T cells as they are stimulated by the BiTEs. The differences in development of T cells, such as generation of dysfunctional/exhausted T cells could lead to the differences in responses to BiTEs in patients. In particular, the in vivo model does not agree with the kinetics of B cells after day 29 in non-responders (Fig. 6d); could the kinetics of T cell development play a role in this?

We agree that intracellular signaling is critical to T cell activation and cytotoxic effects. IS formation, T cell activation, and cytotoxicity are a cascade of events with highly coordinated molecular and cellular interactions. Compared to the events of T cell activation and cytotoxicity, IS formation occurs at a relatively earlier time. As shown in our study, IS formation can occur at 2-5 min, while the other events often need hours to be observed. We found that IS formation is primarily driven by two intercellular processes: cell-cell encounter and cell-cell adhesion. The intracellular signaling would be initiated in the process of cell-cell adhesion or at the late stage of IS formation. We think these intracellular events are relevant but may not be the reason why our model did not adequately capture the profiles in Figure 3d at the highest BiTE concentrations. Therefore, we did not include intracellular signaling in the models. Another reason was that we simulated our models at an agent level to mimic the process of tumor evolution, which is computationally demanding. Intracellular events for each cell may make it more challenging computationally.

T cell activation and exhaustion throughout the BiTE treatment is very complicated, time-variant and impacted by multiple factors like T cell status, tumor burden, BiTE concentration, immune checkpoints, and tumor environment. T cell proliferation and death rates are challenging to estimate, as the quantitative relationship with those factors is unknown. Therefore, T cell abundance (expansion) was considered as an independent variable in our model. T cell counts are measured in BiTE clinical trials. We included these data in our model to reveal expanded T cell population. Patients with high T cell expansion are often those with better clinical response. Notably, the T cell decline due to rapid redistribution after administration was excluded in the model. T cell abundance was included in the simulations in Figure 6 but not proof of concept simulations in Figure 7.

In Figure 6d, kinetics of T cell abundance had been included in the simulations for responders and non-responders in MT103-211 study. Thus, the kinetics of T cell development can’t be used to explain the disagreement between model prediction and observation after day 29 in non-responders. The observed data is actually median values of B-cell kinetics in non-responders (N = 27) with very large inter-subject variation (baseline from 10-10000/μL), which makes it very challenging to be perfectly captured by the model. A lot of non-responders with severe progression dropped out of the treatment at the end of cycle 1, which resulted in a “more potent” efficacy in the 2nd cycle. This might be main reason for the disagreement.

Variation in cytotoxic response was not included in our models. Tumor cells were assumed to be eradicated after the engagement with effecter cells, no killing rate or killing probability was implemented. This assumption reduced the model complexity and aligned well with our in-vitro and clinical data. Cytotoxic response in vivo is impacted by multiple factors like copy number of CD3, cytokine/chemokine release, tumor microenvironment and T cell activation/exhaustion. For example, the cytotoxic response and killing rate mediated by 1:1 synapse (ET) and other variants (ETE, TET, ETEE, etc.) are supposed to be different as well. Our model did not differentiate the killing rate of these synapse variants, but the model has quantified these synapse variants, providing a framework for us to address these questions in the future. We agree that differentiate the cytotoxic responses under different scenarios cell may improve model prediction and more explorations need to be done in the future.

Revision: We added a discussion of the limitations which we believe is informative to future studies.

“Our models did not include intracellular signaling processes, which are critical for T activation and cytotoxicity. However, our data suggests that encounter and adhesion are more relevant to initial IS formation. To make more clinically relevant predictions, the models should consider these intracellular signaling events that drive T cell activation and cytotoxic effects. Of note, we did consider the T cell expansion dynamics in organs as independent variable during treatment for the simulations in Figure 6. T cell expansion in our model is case-specific and time-varying.”

References:

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Author Response

Reviewer #1 (Public Review):

This study examines the factors underlying the assembly of MreB, an actin family member involved in mediating longitudinal cell wall synthesis in rod-shaped bacteria. Required for maintaining rod shape and essential for growth in model bacteria, single molecule work indicates that MreB forms treadmilling polymers that guide the synthesis of new peptidoglycan along the longitudinal cell wall. MreB has proven difficult to work with and the field is littered with artifacts. In vitro analysis of MreB assembly dynamics has not fared much better as helpfully detailed in the introduction to this study. In contrast to its distant relative actin, MreB is difficult to purify and requires very specific conditions to polymerize that differ between groups of bacteria. Currently, in vitro analysis of MreB and related proteins has been mostly limited to MreBs from Gram-negative bacteria which have different properties and behaviors from related proteins in Gram-positive organisms.

Here, Mao and colleagues use a range of techniques to purify MreB from the Gram-positive organism Geobacillus stearothermophilus, identify factors required for its assembly, and analyze the structure of MreB polymers. Notably, they identify two short hydrophobic sequences-located near one another on the 3-D structure-which are required to mediate membrane anchoring.

With regard to assembly dynamics, the authors find that Geobacillus MreB assembly requires both interactions with membrane lipids and nucleotide binding. Nucleotide hydrolysis is required for interaction with the membrane and interaction with lipids triggers polymerization. These experiments appear to be conducted in a rigorous manner, although the salt concentration of the buffer (500mM KCl) is quite high relative to that used for in vitro analysis of MreBs from other organisms. The authors should elaborate on their decision to use such a high salt buffer, and ideally, provide insight into how it might impact their findings relative to previous work.

Response 1.1. MreB proteins are notoriously difficult to maintain in a soluble form. Some labs deleted the N-terminal amphipathic or hydrophobic sequences to increase solubility, while other labs used full-length protein but high KCl concentration (300 mM KCl) (Harne et al, 2020; Pande et al., 2022; Popp et al, 2010; Szatmari et al, 2020). Early in the project, we tested many conditions and noticed that high KCl helped keeping a slightly better solubility of full length MreBGs, without the need for deleting a part of the protein. In addition, concentrations of salt > 100 mM would better mimic the conditions met by the protein in vivo. While 50-100 mM KCl is traditionally used in actin polymerization assays, physiological salt concentrations are around 100-150 mM KCl in invertebrates and vertebrates (Schmidt-Nielsen, 1975), around 50-250 in fungal and plant cells (Rodriguez-Navarro, 2000) and 200-300 mM in the budding yeast (Arino et al, 2010). However, cytoplasmic K+ concentration varies greatly (up to 800 mM) depending on the osmolality of the medium in both E. coli (Cayley et al, 1991; Epstein & Schultz, 1965; Rhoads et al, 1976), and B. subtilis, in which the basal intracellular concentration of KCl was estimated to be ~ 350 mM (Eisenstadt, 1972; Whatmore et al, 1990). 500 mM KCl can therefore be considered as physiological as 100 mM KCl for bacterial cells. Since we observed plenty of pairs of protofilaments at 500 mM KCl and this condition helped to avoid aggregation, we kept this high concentration as a standard for most of our experiments. Nonetheless, we had also performed TEM polymerization assays at 100 mM in line with most of MreB and F-actin in vitro literature, and found no difference in the polymerization (or absence of polymerization) conditions. This was indicated in the initial submission (e.g. M&M section L540 and footnote of Table S2) but since two reviewers bring it up as a main point, it is evident we failed at communicating it clearly, for which we apologize. This has been clarified in the revised version of the manuscript. We have also almost systematically added the 100 mM KCl concentration too as per reviewer #2 request and to conciliate our salt conditions with those used for some in vitro analysis of MreBs from other organisms (see also response to reviewer #2 comments 1A and 1B = Responses 2.1A, 2.1B below). We then decided to refer to the 100 mM KCl concentration as our “standard condition” in the revised version of the manuscript, but we compile and compare the results obtained at 500 mM too, as both concentrations are within the physiological range in Bacillus.

Additionally, this study, like many others on MreB, makes much of MreB's relationship to actin. This leads to confusion and the use of unhelpful comparisons. For example, MreB filaments are not actin-like (line 58) any more than any polymer is "actin-like." As evidenced by the very beautiful images in this manuscript, MreB forms straight protofilaments that assemble into parallel arrays, not the paired-twisted polymers that are characteristic of F-actin. Generally, I would argue that work on MreB has been hindered by rather than benefitted from its relationship to actin (E.g early FP fusion data interpreted as evidence for an MreB endoskeleton supporting cell shape or depletion experiments implicating MreB in chromosome segregation) and thus such comparisons should be avoided unless absolutely necessary.

Response 1.2. We completely agree with reviewer #1 regarding unhelpful comparisons of actin and MreB, and that work on MreB has been traditionally hindered from its relationship to eukaryotic actin. MreB is nonetheless a structural homolog of actin, with a close structural fold and common properties (polymerization into pairs of protofilaments, ATPase activity…). It still makes sense to refer to a protein with common features, common ancestry and widely studied as long as we don’t enclose our mind into a conceptual framework. This said, actin and MreB diverged very early in evolution, which may account for differences in their biochemical properties and cellular functions. Current data on MreB filaments confirm that they display F-actin-like and F-actin-unlike properties. We thank the reviewer for this insightful comment. We have revised the text to remove any inaccurate or unhelpful comparison to actin (in particular the ‘actin-like filaments’ statement, previously used once)

Reviewer #2 (Public Review):

The paper "Polymerization cycle of actin homolog MreB from a Gram-positive bacterium" by Mao et al. provides the second biochemical study of a gram-positive MreB, but importantly, the first study examines how gram-positive MreB filaments bind to membranes. They also show the first crystal structure of a MreB from a Gram-positive bacterium - in two nucleotide-bound forms, finally solving structures that have been missing for too long. They also elucidate what residues in Geobacillus MreB are required for membrane associations. Also, the QCM-D approach to monitoring MreB membrane associations is a direct and elegant assay.

While the above findings are novel and important, this paper also makes a series of conclusions that run counter to multiple in vitro studies of MreBs from different organisms and other polymers with the actin fold. Overall, they propose that Geobacillus MreB contains biochemical properties that are quite different than not only the other MreBs examined so far but also eukaryotic actin and every actin homolog that has been characterized in vitro. As the conclusions proposed here would place the biochemical properties of Geobacillus MreB as the sole exception to all other actin fold polymers, further supporting experiments are needed to bolster these contrasting conclusions and their overall model.

Response 2.0. We are grateful to reviewer #2 for stressing out the novelty and importance of our results. Most of our conclusions were in line with previous in vitro studies of MreBs (formation of pairs of straight filaments on a lipid layer, both ATP and GTP binding and hydrolysis, distortion of liposomes…), to the exception of the claimed requirement of NTP hydrolysis for membrane binding prior to polymerization based on the absence of pairs of filaments in free solution or in the presence of AMP-PNP in our experimental conditions (which we agree was not sufficient to make such a bold claim, see below). Thanks to the reviewer’s comments, we have performed many controls and additional experiments that lead us to refine our results and largely conciliate them with the literature. Please see the answer to the global review comments - our conclusions have been revised on the basis of our new data.

1. (Difference 1) - The predominant concern about the in vitro studies that makes it difficult to evaluate many of their results (much less compare them to other MreB/s and actin homologs) is the use of a highly unconventional polymerization buffer containing 500(!) mM KCL. As has been demonstrated with actin and other polymers, the high KCl concentration used here (500mM) is certain to affect the polymerization equilibria, as increasing salt increases the hydrophobic effect and inhibits salt bridges, and therefore will affect the affinity between monomers and filaments. For example, past work has shown that high salt greatly changes actin polymerization, causing: a decreased critical concentration, increased bundling, and a greatly increased filament stiffness (Kang et al., 2013, 2012). Similarly, with AlfA, increased salt concentrations have been shown to increase the critical concentration, decrease the polymerization kinetics, and inhibit the bundling of AlfA filaments (Polka et al., 2009).

A more closely related example comes from the previous observation that increasing salt concentrations increasingly slow the polymerization kinetics of B. subtilis MreB (Mayer and Amann, 2009). Lastly, These high salt concentrations might also change the interactions of MreB(Gs) with the membrane by screening charges and/or increasing the hydrophobic effect. Given that 500mM KCl was used throughout this paper, many (if not all) of the key experiments should be repeated in more standard salt concentration (~100mM), similar to those used in most previous in vitro studies of polymers.

Response 2.1A. As per reviewer #2 request, we have done at 100 mM KCl too most experiments (TEM, cryo-EM, QCMD and ATPase assays) initially performed at 500 mM KCl only. The KCl concentration affects both membrane binding and filament stiffness as anticipated by the reviewer but the main conclusions are the same. The revised version of the manuscript compiles and compares the results obtained at both high and low [KCl], both concentrations being within the physiological range in Bacillus. Please see point 1 of the response to the global review comments and the first response to reviewer 1 (Response 1.1) for further elaboration.

Please note that in Mayer & Amann, 2009 (B. subtilis MreB), light scattering in free solution was inversely proportional to the KCl concentration, with the higher light scattering signal at 0 mM KCl (!), a > 2-fold reduction below 30 mM KCl and no scatter at all at 250 mM, suggesting a “salting in” phenomenon (see also the “Other Points to address” answers 1A and 2, below) (Mayer & Amann, 2009). Since no effective polymer formation (e.g. polymers shown by EM) was demonstrated in these experiments, it cannot be excluded that KCl was simply preventing aggregation of B. subtilis MreB in solution, as we observe. For all their other light scattering experiments, the ‘standard polymerization condition’ used by Mayer & Amann was 0.2 mM ATP, 5 mM MgCl2, 1 mM EGTA and 10 mM imidazole pH 7.0, to which MreB (in 5 mM Tris pH 8.0) was added. No KCl was present in their ‘standard’ polymerization conditions.

This would test if the many divergent properties of MreB(Gs) reported here arise from some difference in MreB(Gs) relative to other MreBs (and actin homologs), or if they arise from the 400mM difference in salt concentration between the studies. Critically, it would also allow direct comparisons to be made relative to previous studies of MreB (and other actin homologs) that used much lower salt, thereby allowing them to definitively demonstrate whether MreB(Gs) is indeed an outlier relative to other MreB and actin homologs. I would suggest using 100mM KCL, as historically, all polymerization assays of actin and numerous actin homologs have used 50-100mM KCL: 50mM KCl (for actin in F buffer) or 100mM KCl for multiple prokaryotic actin homologs and MreB (Deng et al., 2016; Ent et al., 2014; Esue et al., 2006, 2005; Garner et al., 2004 ; Polka et al., 2009 ; Rivera et al., 2011 ; Salje et al., 2011). Likewise, similar salt concentrations are standard for tubulin (80 mM K-Pipes) and FtsZ (100 mM KCl or 100mM KAc in HMK100 buffer).

Response 2.1B. We appreciate the reviewer’s feedback on this point. Please note that, although actin polymerization assays are historically performed at 50-100 mM KCl and thus 100 mM KCl was used for other bacterial actin homologs (MamK, ParM and AlfA), MreB polymerization assays have previously been reported at 300 mM KCl too (Harne et al., 2020; Pande et al., 2022; Popp et al., 2010; Szatmari et al., 2020), which is closer to the physiological salt concentration in bacterial cells (see Response 1.1), but also in the absence of KCl (see above). As a matter of fact, we originally wanted to use a “standard polymerization condition” based on the literature on MreB, before realizing there was none: only half used KCl (the other half used NaCl, or no monovalent salt at all) and among these, KCl concentrations varied (out of 8 publications, 2 used 20 mM KCl, 2 used 50 mM KCl and 4 used 300 mM KCl).

1. (Difference 2) - One of the most important differences claimed in this paper is that MreB(Gs) filaments are straight, a result that runs counter to the curved T. Maritima and C. crescentus filaments detailed by the Löwe group (Ent et al., 2014; Salje et al., 2011). Importantly, this difference could also arise from the difference in salt concentrations used in each study (500mM here vs. 100mM in the Löwe studies), and thus one cannot currently draw any direct comparisons between the two studies.

One example of how high salt could be causing differences in filament geometry: high salts are known to greatly increase the bending stiffness of actin filaments, making them more rigid (Kang et al., 2013). Likewise, increasing salt is known to change the rigidity of membranes. As the ability of filaments to A) bend the membrane or B) Deform to the membrane depends on the stiffness of filaments relative to the stiffness of the membrane, the observed difference in the "straight vs. curved" conformation of MreB filaments might simply arise from different salt concentrations. Thus, in order to draw several direct comparisons between their findings and those of other MreB orthologs (as done here), the studies of MreB(GS) confirmations on lipids should be repeated at the same buffer conditions as used in the Löwe papers, then allowing them to be directly compared.

Response 2.2. We fully agreed with reviewer #2 that the salts could be affecting the assay and did cryo-EM experiments also in the presence of 100 mM KCl as requested. The results unambiguously showed countless curved liposomes on the contact areas with MreB (Fig. 2F-G and Fig. 2-S5), very similar to what was reported for Thermotoga and Caulobacter MreBs by the Lowe group. Our results therefore confirm the previous findings that MreBs can bend lipids, and suggest that, indeed, high salt may increase filament stiffness as it has been shown for actin filaments. We are very grateful to reviewer #2 for his suggestion and for drawing our attention to the work of Kang et al, 2013. The different bending observed when varying the salt concentration raise relevant questions regarding the in vivo behavior of MreB, since KCl was shown to vary greatly depending on the medium composition. The manuscript has been updated accordingly in the Results (from L243) and Discussion sections (L585-595).

1. (Difference 3) - The next important difference between MreB(Gs) and other MreBs is the claim that MreB polymers do not form in the absence of membranes.

A) This is surprising relative to other MreBs, as MreBs from 1) T. maritime (multiple studies), E.coli (Nurse and Marians, 2013), and C. crescentus (Ent et al., 2014) have been shown to form polymers in solution (without lipids) with electron microscopy, light scattering, and time-resolved multi-angle light scattering. Notably, the Esue work was able to observe the first phase of polymer formation and a subsequent phase of polymer bundling (Esue et al., 2006) of MreB in solution. 2) Similarly, (Mayer and Amann, 2009) demonstrated B. subtilis MreB forms polymers in the absence of membranes using light scattering.

Response 2.3A. The literature does convincingly show that Thermotoga MreB forms polymers in solution, without lipids (note that for Caulobacter MreB filaments were only reported in the presence of lipids, (van den Ent et al, 2014)). Assemblies reported in solution are bundles or sheets (included in at the earlier time points in the time-resolved EM experiments reported by Esue et al. 2006 mentioned by the reviewer – ‘2 minutes after adding ATP, EM revealed that MreB formed short filamentous bundles’) (Esue et al, 2006). However, and as discussed above (Response 2.1A), the light scattering experiments in Mayer et Amann, 2009 do not conclusively demonstrate the presence of polymers of B. subtilis MreB in solution (Mayer & Amann, 2009). We performed many light scattering experiments of B. subtilis MreB in solution in the past (before finding out that filaments were only forming in the presence of lipids), and got similar scattering curves (see two examples of DLS experiments in Author response image 1) in conditions in which NO polymers could ever been observed by EM while plenty of aggregates were present.

Author response image 1.

We did not consider these results publishable in the absence of true polymers observed by TEM. As pointed out on the interesting study from Nurse et al. (on E. coli MreB) (Nurse & Marians, 2013), one cannot rely only on light scattering only because non-specific aggregates would show similar patterns than polymers. Over the last two decades, about 15 publications showed polymers of MreB from several Gram-negative species, while none (despite the efforts of many) showed a single convincing MreB polymer from a Gram-positive bacterium by EM. A simple hypothesis is that a critical parameter was missing, and we present convincing evidence that lipids are critical for Geobacillus MreB to form pairs of filaments in the conditions tested. However, in solution too we do occasionally see pairs of filaments (Fig 2-S2), and also sheet-like structures among aggregates when the concentration of MreB is increased (Fig. 2-S2 and Fig. 3-S2). Thus, we agree with the reviewer that it cannot be claimed that Geobacillus MreB is unable to polymerize in the absence of lipids, but rather that lipids strongly stimulate its polymerization, condition depending.

B) The results shown in figure 5A also go against this conclusion, as there is only a 2-fold increase in the phosphate release from MreB(Gs) in the presence of membranes relative to the absence of membranes. Thus, if their model is correct, and MreB(Gs) polymers form only on membranes, this would require the unpolymerized MreB monomers to hydrolyze ATP at 1/2 the rate of MreB in filaments. This high relative rate of hydrolysis of monomers compared to filaments is unprecedented. For all polymers examined so far, the rate of monomer hydrolysis is several orders of magnitude less than that of the filament. For example, actin monomers are known to hydrolyze ATP 430,000X slower than the monomers inside filaments (Blanchoin and Pollard, 2002; Rould et al., 2006).

Response 2.3B. We agree with the reviewer. We have now found conditions where sheets of MreB form in solution (at high MreB concentration) in the presence of ADP and AMP-PNP. However, we have now added several controls that exclude efficient formation of polymers in solution in the presence of ATP at low concentrations of MreBGs (≤ 1.5 µM), the condition used for the malachite green assays. At these MreB concentrations, pairs of filaments are observed in the presence of lipids, but very unfrequently in solution, and sheets are not observed in solution either (Fig. 2-S2A, B). Yet, albeit puzzling, in these conditions Pi release is reproducibly observed in solution, reduced only ~ 2 to 3-fold relative to Pi release in the presence of lipids (Fig. 5A and Fig. 5-S1). A reinforcing observation is when the ATPase assays is performed at 100 mM KCl (Fig. 5A). In this condition MreB binding to lipids is increased relative to 500 mM KCl (Fig. 4-S4C), and the stimulation of the ATPase activity by the presence of lipids is also stronger that at 500 mM (Fig. 5-S1A). Further work is needed to characterize in detail the ATPase activity of MreB proteins, for which data in the literature is very scarce. We can’t exclude that MreB could nucleate in solution or form very unstable filaments that cannot be seen in our EM assay but consume ATP in the process. At the moment, the significance of the Pi released in solution is unknown and will require further investigation.

C) Thus, there is a strong possibility that MreB(Gs) polymers are indeed forming in solution in addition to those on the membrane, and these "solution polymers" may not be captured by their electron microscopy assay. For example, high salt could be interfering with the absorption of filaments to glow discharged lacking lipids.

Response 2.3C. We appreciate the reviewer’s insight about this critical point. Polymers presented in the original Fig. 2A were obtained at 500 mM KCl but we had tested the polymerization of MreB at 100 mM KCl as well, without noticing differences. We have nonetheless redone this quantitatively and used these data for the revised Fig. 2A, as we are now using 100 mM KCl as our standard polymerization condition throughout the revised manuscript. We also followed the other suggestion of the reviewer and tested glow discharged grids (a more classic preparation for soluble proteins) vs non-glow discharged EM grids, as well as a higher concentration of MreB. Grids are generally glow-discharged to make them hydrophilic in order to adsorb soluble proteins, but the properties of MreB (soluble but obviously presenting hydrophobic domains) made difficult to predict what support putative soluble polymers would preferentially interact with. Septins for example bind much better to hydrophobic grids despite their soluble properties (I. Adriaans, personal communication). Virtually no double filaments were observed in solution at either low or high [MreB]. The fact that in some conditions (high [MreB], other nucleotides) we were able to detect sheet-like structures excluded a technical issue that would prevent the detection of existing but “invisible” polymers here. We have added these new data in Fig. 2-S2.

As indicated above, the reviewer’s comments made us realize that we could not state or imply that MreB cannot polymerize in the absence of lipids. As a matter of fact, we always saw some random filaments in the EM fields, both in solution and in the presence of non-hydrolysable analogues, at very low frequency (Fig. 2A). And we do see now sheets at high MreB concentration (Fig. 2-S2B). We could be just missing the optimal conditions for polymerisation in solution, while our phrasing gave the impression that no polymers could ever form in the absence of ATP or lipids. Therefore, we have:

1) analyzed all TEM data to present it as semi-quantitative TEM, using our methodology originally implemented for the analysis of the mutants

2) reworked the text to remove any issuing statements and to indicate that MreBGs was only found to bind to a lipid monolayer as a double protofilament in the presence of ATP/GTP but that this does not exclude that filaments may also form in other conditions.

In order to definitively prove that MreB(Gs) does not have polymers in solution, the authors should:

i) conduct orthogonal experiments to test for polymers in solution. The simplest test of polymerization might be conducting pelleting assays of MreB(Gs) with and without lipids, sweeping through the concentration range as done in 2B and 5a.

Response 2.3Ci. Following reviewer #2 suggestion, we conducted a series of sedimentation assays in the presence and in the absence of lipids, at low (100 mM) and high (500 mM) salt, for both the wild-type protein and the three membrane-anchoring mutants (all at 1.3 µM). Sedimentation experiments in salt conditions preventing aggregation in solution (500 mM KCl) fitted with our TEM results: MreB wild-type pelleting increased in the presence of both ATP and lipids (Fig. R1). The sedimentation was further increased at 100 mM KCl, which would fit our other results indicating an increased interaction of MreB with the membrane. However, in addition to be poorly reproducible (in our hands), the approach does not discriminate between polymers and aggregates (or monomers bound to liposomes) and since MreB has a strong tendency to aggregate, we believe that the technique is ill-suited to reliably address MreB polymerization and prefer not to include sedimentation data in our manuscript. The recent work from Pande et al. (2022) illustrates well this issue since no sedimentation of MreB (at 2 µM) was observed in solution in conditions supporting polymerization (at 300 mM KCl): ‘the protein does not pellet on its own in the absence of liposome, irrespective of its polymerization state’, implying that sedimentation does not allow to detect MreB5 filaments in solution (Pande et al., 2022).

ii) They also could examine if they see MreB filaments in the absence of lipids at 100mM salt (as was seen in both Löwe studies), as the high salt used here might block the charges on glow discharged grids, making it difficult for the polymer to adhere.

See above, Response 2.3C

iii) Likewise, the claim that MreB lacking the amino-terminus and the α2β7 hydrophobic loop "is required for polymerization" is questionable as if deleting these resides blocks membrane binding, the lack of polymers on the membrane on the grid is not unexpected, as these filaments that cannot bind the membrane would not be observable. Given these mutants cannot bind the membrane, mutant polymers could still indeed exist in solution, and thus pelleting assays should be used to test if non-membrane associated filaments composed of these mutants do or do not exist.

Response 2.3Ciii. This is a fair point, we thank the reviewer for this remark. We did not mean to state or imply that the hydrophobic loop was required for polymerization per se, but that polymerization into double filaments only efficiently occurs upon membrane binding, which is mediated by the two hydrophobic sequences. We tested all three mutants by sedimentation as suggested by reviewer #2. In the salt condition that limits aggregation (500 mM KCl) the mutants did not pellet while the wild-type protein did (in the presence of lipids) (Fig. R2 below), in agreement with our EM data. We tested the absence of lipids on the mutant bearing the 2 deletions and observed that the (partial) sedimentation observed at low KCl concentration was ATP and lipid dependent (Fig. R3).

Given our concerns about MreB sedimentation assays (see above, Response 2.3Ci), we prefer not to include these sedimentation data in our manuscript. Instead, we tested by TEM the possible polymerization of the mutants in solution (we only tested them in the presence of lipids in the initial submission). No filaments were detected in solution for any of the mutants (Fig. 4-S3A).

A final note, the results shown in "Figure 1 - figure supplement 2, panel C" appear to directly refute the claim that MreB(Gs) requires lipids to polymerize. As currently written, it appears they can observe MreB(Gs) filaments on EM grids without lipids. If these experiments were done in the presence of lipids, the figure legend should be updated to indicate that. If these experiments were done in the absence of lipids, the claim that membrane association is required for MreB polymerizations should be revised.

The TEM experiments show were indeed performed in the presence of lipids. We apologize for this was not clearly stated in the legend. To prevent all confusion, we have nevertheless removed these images in this figure since the polymerization conditions and lipid requirement are not yet presented when this figure is referred to in the text. We have instead added a panel with the calibration curve for the size exclusion profiles as per request of reviewer #3. The main point of this figure is to show the tendency of MreBGs to aggregate: analytical size-exclusion chromatography shows a single peak corresponding to the monomeric MreBGs, molecular weight ~ 37 KDa, in our purification conditions, but it can readily shift to a peak corresponding to high MW aggregates, depending on the protein concentration and/or storage conditions.

1. (Difference 4) - The next difference between this study and previous studies of MreB and actin homologs is the conclusion that MreB(Gs) must hydrolyze ATP in order to polymerize. This conclusion is surprising, given the fact that both T. Maritima (Salje · 2011, Bean 2008) and B. subtilis MreB (Mayer 2009) have been shown to polymerize in the presence of ATP as well as AMP-PNP.

Likewise, MreB polymerization has been shown to lag ATP hydrolysis in not only T. maritima MreB (Esue 2005), eukaryotic actin, and all other prokaryotic actin homologs whose polymerization and phosphate release have been directly compared: MamK (Deng et al., 2016), AlfA (Polka et al., 2009), and two divergent ParM homologs (Garner et al., 2004; Rivera et al., 2011). Currently, the only piece of evidence supporting the idea that MreB(Gs) must hydrolyze ATP in order to polymerize comes from 2 observations: 1) using electron microscopy, they cannot see filaments of MreB(Gs) on membranes in the presence of AMP-PNP or ApCpp, and 2) no appreciable signal increase appears testing AMPPNP- MreB(Gs) using QCM-D. This evidence is by no means conclusive enough to support this bold claim: While their competition experiment does indicate AMPPNP binds to MreB(Gs), it is possible that MreB(Gs) cannot polymerize when bound to AMPPNP.

For example, it has been shown that different actin homologs respond differently to different non-hydrolysable analogs: Some, like actin, can hydrolyze one ATP analog but not the other, while others are able to bind to many different ATP analogs but only polymerize with some of one of them.

Response 2.4. We agree with the reviewer, it is uncertain what analogs bind because they are quite different to ATP and some proteins just do not like them, they can change conditions such that filaments stop forming as well and be (theoretically) misleading. This is why we had tested ApCpp in addition to AMP-PNP as non-hydrolysable analog (Fig. 3A). As indicated above, our new complementary experiments (Fig. 3-S1B-D) now show that some rare (i.e. unfrequently and in limited amount) dual polymers are detected in the presence of ApCpp (Fig. 3A) and at high MreB concentration only in the presence of AMP-PNP (Fig. 3-S1B-D), suggesting different critical concentrations in the presence of alternative nucleotides. We have dampened our conclusions, in the light of our new data, and modified the discussion accordingly.

Thus, to further verify their "hydrolysis is needed for polymerization" conclusion, they should:

A. Test if a hydrolysis deficient MreB(Gs) mutant (such as D158A) is also unable to polymerize by EM.

Response 2.4A. We thank the reviewer for this suggestion. As this conclusion has been reviewed on the basis of our new data (see previous response), testing putative ATPase deficient mutants is no longer required here. The study of ATPase mutants is planned for future studies (see Response 3.10 to reviewer #3).

B. They also should conduct an orthogonal assay of MreB polymerization aside from EM (pelleting assays might be the easiest). They should test if polymers of ATP, AMP-PNP, and MreB(Gs)(D158A) form in solution (without membranes) by conducting pelleting assays. These could also be conducted with and without lipids, thereby also addressing the points noted above in point 3.

Response 2.4B. Please see Response 2.3Ci above.

C. Polymers may indeed form with ATP-gamma-S, and this non-hydrolysable ATP analog should be tested.

Response 2.4C. It is fairly possible that ATP-γ-S supports polymerization since it is known to be partially hydrolysable by actin giving a mild phenotype (Mannherz et al, 1975). This molecule can even be a bona fide substrate for some ATPases (e.g. (Peck & Herschlag, 2003). Thus, we decided to exclude this “non-hydrolysable” analog and tested instead AMP-PNP and ApCpp. We know that ATP-γ-S has been and it is still frequently used, but we preferred to avoid it for the moment for the above-indicated reasons. We chose AMPPNP and AMPPCP instead because (1) they were shown to be completely non-hydrolysable by actin, in contrast to ATP-γ-S; (2) they are widely used (the most commonly used for structural studies; (Lacabanne et al, 2020), (3) AMPPNP was previously used in several publications on MreB (Bean & Amann, 2008; Nurse & Marians, 2013; Pande et al., 2022; Popp et al., 2010; Salje et al, 2011; van den Ent et al., 2014)and thus would allow direct comparison. AMPPCP was added to confirm the finding with AMP-PNP. There are many other analogs that we are planning to explore in future studies (see next Response, 2.4D).

D. They could also test how the ADP-Phosphate bound MreB(Gs) polymerizes in bulk and on membranes, using beryllium phosphate to trap MreB in the ADP-Pi state. This might allow them to further refine their model.

Response 2.4D. We plan to address the question of the transition state in depth in following-up work, using a series of analogs and mutants presumably affected in ATPase activity, both predicted and identified in a genetic screen. As indicated above, it is uncertain what analogs bind because they are quite different to ATP and some may bind but prevent filament formation. Thus, we anticipate that trying just one may not be sufficient, they can change conditions and be (theoretically) misleading and thus a thorough analysis is needed to address this question. Since our model and conclusions have been revised on the basis of our new data, we believe that these experiments are beyond the scope of the current manuscript.

E. Importantly, the Mayer study of B. subtilis MreB found the same results in regard to nucleotides, "In polymerization buffer, MreB produced phosphate in the presence of ATP and GTP, but not in ADP, AMP, GDP or AMP-PNP, or without the readdition of any nucleotide". Thus this paper should be referenced and discussed

Response 2.4E. We agree that Pi release was detected previously. We have added the reference (L121)

1. (Difference 5) - The introduction states (lines 128-130) "However, the need for nucleotide binding and hydrolysis in polymerization remains unclear due to conflicting results, in vivo and in vitro, including the ability of MreB to polymerize or not in the presence of ADP or the non-hydrolysable ATP analog AMP-PNP."

A) While this is a great way to introduce the problem, the statement is a bit vague and should be clarified, detaining the conflicting results and appropriate references. For example, what conflicting in vivo results are they referring to? Regarding "MreB polymerization in AMP-PNP", multiple groups have shown the polymerization of MreB(Tm) in the presence of AMP-PNP, but it is not clear what papers found opposing results.

Response 2.5A. Thanks for the comment. We originally did not detail these ‘conflicting results’ in the Introduction because we were doing it later in the text, with the appropriate references, in particular in the Discussion (former L433-442). We have now removed this from the Discussion section and added a sentence in the introduction too (L123-130) quickly detailing the discrepancies and giving the references.

• For more clarity, we have removed the “in vivo” (which referred to the distinct results reported for the presumed ATPase mutants by the Garner and Graumann groups) and focus on the in vitro discrepancies only.

• These discrepancies are the following: while some studies showed indeed polymerization (as assessed by EM) of MreBTm in the presence of AMPPNP, the studies from Popp et al and Esue et al on T. maritima MreB, and of Nurse et al on E. coli MreB reported aggregation in the presence of AMP-PNP (Esue et al., 2006; Popp et al., 2010) or ADP (Nurse & Marians, 2013), or no assembly in the presence of ADP (Esue et al., 2006). As for the studies reporting polymerization in the presence of AMP-PNP by light scattering only (Bean & Amann, 2008; Gaballah et al, 2011; Mayer & Amann, 2009; Nurse & Marians, 2013), they could not differentiate between aggregates or true polymers and thus cannot be considered conclusive.

B) The statement "However, the need for nucleotide binding and hydrolysis in polymerization remains unclear due to conflicting results, in vivo and in vitro, including the ability of MreB to polymerize or not in the presence of ADP or the non-hydrolyzable ATP analog AMP-PNP" is technically incorrect and should be rephrased or further tested.

i. For all actin (or tubulin) family proteins, it is not that a given filament "cannot polymerize" in the presence of ADP but rather that the ADP-bound form has a higher critical concentration for polymer formation relative to the ATP-bound form. This means that the ADP polymers can indeed polymerize, but only when the total protein exceeds the ADP critical concentration. For example, many actin-family proteins do indeed polymerize in ADP: ADP actin has a 10-fold higher critical concentration than ATP actin, (Pollard, 1984) and the ADP critical concentrations of AlfA and ParM are 5X and 50X fold higher (respectively) than their ATP-bound forms(Garner et al., 2004; Polka et al., 2009)

Response 2.5Bi. Absolutely correct. We apologize for the lack of accuracy of our phrasing and have corrected it (L123).

ii. Likewise, (Mayer and Amann, 2009) have already demonstrated that B. subtilis MreB can polymerize in the presence of ADP, with a slightly higher critical concentration relative to the ATP-bound form.

Response 2.5Bii. In Mayer and Amann, 2009, the same light scattering signal (interpreted as polymerization) occurred regardless of the nucleotide, and also in the absence of nucleotide (their Fig. 10) and ATP-, ADP- and AMP-PNP-MreB ‘displayed nearly indistinguishable critical concentrations’. They concluded that MreB polymerization is nucleotide-independent. Please see below (responses to ’Other points to address’) our extensive answer to the Mayer & Amann recurring point of reviewer #2

Thus, to prove that MreB(Gs) polymers do not form in the presence of ADP would require one to test a large concentration range of ADP-bound MreB(Gs). They should test if ADP- MreB(Gs) polymerizes at the highest MreB(Gs) concentrations that can be assayed. Even if this fails, it may be the MreB(Gs) ADP polymerizes at higher concentrations than is possible with their protein preps (13uM). An even more simple fix would be to simply state MreB(Gs)-ADP filaments do not form beneath a given MreB(Gs) concentration.

We agree with the reviewer. Our wording was overstating our conclusions. Based on our new quantifications (Fig. 3-S1B, D), we have rephrased the results section and now indicate that pairs of filaments are occasionally observed in the presence of ADP in our conditions across the range of MreB concentration that could be tested, suggesting a higher critical concentration for MreB-ADP (L310-312). Only at the highest MreB concentration, sheet- and ribbon-like structures were observed in the presence of ADP (Fig. 3-S2B).

Other Points to address:

1) There are several points in this paper where the work by Mayer and Amann is ignored, not cited, or readily dismissed as "hampered by aggregation" without any explanation or supporting evidence of that fact.

We have cited the Mayer study where appropriate. However, we cannot cite it as proof of polymerization in such or such condition since their approach does not show that polymers were obtained in their conditions. Again, they based all their conclusions solely on light scattering experiments, which cannot differentiate between polymers and aggregates.

A) Lines 100-101 - While the irregular 3-D formations seen formed by MreB in the Dersch 2020 paper could be interpreted as aggregates, stating that the results from specifically the Gaballah and Meyer papers (and not others) were "hampered by aggregation" is currently an arbitrary statement, with no evidence or backing provided. Overall, these lines (and others in the paper) dismiss these two works without giving any evidence to that point. Thus, they should provide evidence for why they believe all these papers are aggregation, or remove these (and other) dismissive statements.

We apologize if our statements about these reports seemed dismissive or disrespectful, it was definitely not our intention. Light scattering shows an increase of size of particles over time, but there is no way to tell if the scattering is due to organized (polymers) or disorganized (aggregation) assemblies. Thus, it cannot be considered a conclusive evidence of polymerization without the proof that true filaments are formed by the protein in the conditions tested, as confirmed by EM for example. MreB is known to easily aggregate (see our size exclusion chromatography profiles and ones from Dersch 2020 (Dersch et al, 2020), and note that no chromatography profiles were shown in the Mayer report) and, as indicated above, we had similar light scattering results for MreB for years, while only aggregates could be observed by TEM (see above Response 2.3A). Several observations also suggest that aggregation instead of polymerization might be at play in the Mayer study, for example ‘polymerization’ occurring in salt-less buffer but ‘inhibited’ with as low as 100 mM KCl, which should rather be “salting in” (see below). We did not intend to be dismissive, but it seemed wrong to report their conclusions as conclusive evidence. We thought that we had cited these papers where appropriate but then explained that they show no conclusive proof of polymerization and why, but it is evident that we failed at communicating it clearly. We have reworked the text to remove any issuing and arbitrary statement about our concerns regarding these reports (e.g. L93 & L126).

One important note - There are 2 points indicating that dismissing the Meyer and Amann work as aggregation is incorrect:

1) the Meyer work on B. subtilis MreB shows both an ATP and a slightly higher ADP critical concentration. As the emergence of a critical concentration is a steady-state phenomenon arising from the association/dissociation of monomers (and a kinetically limiting nucleation barrier), an emergent critical concentration cannot arise from protein aggregation, critical concentrations only arise from a dynamic equilibrium between monomer and polymer.

• Critical concentration for ATP, ADP or AMPPNP were described in Mayer & Amann (Mayer & Amann, 2009) as “nearly indistinguishable” (see Response 2.5Bii)
• Protein aggregation depends on the solution (pH and ions), protein concentration and temperature. And above a certain concentration, proteins can become instable, thus a critical concentration for aggregation can emerge.

2) Furthermore, Meyer observed that increased salt slowed and reduced B. subtilis MreB light scattering, the opposite of what one would expect if their "polymerization signal" was only protein aggregation, as higher salts should increase the rate of aggregation by increasing the hydrophobic effect.

It is true that at high salt concentration proteins can precipitate, a phenomenon described as “salting out”. However, it is also true that salts help to solubilize proteins (“salting in”), and that proteins tend to precipitate in the absence of salt. Considering that the starting point of the Mayer and Amann experiment (Mayer & Amann, 2009) is the absence of salt (where they observed the highest scattering) and that they gradually reduce this scattering by increasing KCl (the scattering is almost abolished below 100 mM only!) it is plausible that a salting-in phenomenon might be at play, due to increased solubility of MreB by salt. In any case, this cannot be taken as a proof that polymerization rather than aggregation occurred.

B) Lines 113-137 -The authors reference many different studies of MreB, including both MreB on membranes and MreB polymerized in solution (which formed bundles). However, they again neglect to mention or reference the findings of Meyer and Amann (Mayer and Amann, 2009), as it was dismissed as "aggregation". As B. subtilis is also a gram-positive organism, the Meyer results should be discussed.

We did cite the Mayer and Amann paper but, as explained above, we cannot cite this study as an example of proven polymerization. We avoided as much as possible to polemicize in the text and cited this paper when possible. Again, we have reworked the text to avoid any issuing or dismissive statement. Also, we forgot mentioned this study at L121 as an example of reported ATPase activity, and this has now been corrected.

2) Lines 387-391 state the rates of phosphate release relative to past MreB findings: "These rates of Pi release upon ATP hydrolysis (~ 1 Pi/MreB in 6 min at 53{degree sign}C) are comparable to those observed for MreBTm and MreB(Ec) in vitro". While the measurements of Pi release AND ATP hydrolysis have indeed been measured for actin, this statement does not apply to MreB and should be corrected: All MreB papers thus far have only measured Pi release alone, not ATP hydrolysis at the same time. Thus, it is inaccurate to state "rates of Pi release upon ATP hydrolysis" for any MreB study, as to accurately determine the rate of Pi release, one must measure: 1. The rate of polymer over time, 2) the rate of ATP hydrolysis, and 3) the rate of phosphate release. For MreB, no one has, so far, even measured the rates of ATP hydrolysis and phosphate release with the same sample.

We completely agree with the reviewer, we apologize if our formulation was inaccurate. We have corrected the sentence (L479). Thank you for pointing out this mistake.

3) The interpretation of the interactions between monomers in the MreB crystal should be more carefully stated to avoid confusion. While likely not their intention, the discussions of the crystal packing contacts of MreB can appear to assume that the monomer-monomer contacts they see in crystals represent the contacts within actual protofilaments. One cannot automatically assume the observations of monomer-monomer contacts within a crystal reflect those that arise in the actual filament (or protofilament).

We agree, we thank the reviewer for his comments. We have revamped the corresponding paragraph.

A) They state, "the apo form of MreBGs forms less stable protofilaments than its G- homologs ." Given filaments of the Apo form of MreB(GS) or b. subtilis have never been observed in solution, this statement is not accurate: while the contacts in the crystal may change with and without nucleotide, if the protein does not form polymers in solution in the apo state, then there are no "real" apo protofilaments, and any statements about their stability become moot. Thus this statement should be rephrased or appropriately qualified.

see above.

B) Another example: while they may see that in the apo MreB crystal, the loop of domain IB makes a single salt bridge with IIA and none with IIB. This contrasts with every actin, MreB, and actin homolog studied so far, where domain IB interacts with IIB. This might reflect the real contacts of MreB(Gs) in the solution, or it may be simply a crystal-packing artifact. Thus, the authors should be careful in their claims, making it clear to the reader that the contacts in the crystal may not necessarily be present in polymerized filaments.

Again, we agree with the reviewer, we cannot draw general conclusions about the interactions between monomers from the apo form. We have rephrased this paragraph.

4) lines 201-202 - "Polymers were only observed at a concentration of MreB above 0.55 μM (0.02 mg/mL)". Given this concentration dependence of filament formation, which appears the same throughout the paper, the authors could state that 0.55 μM is the critical concentration of MreB on membranes under their buffer conditions. Given the lack of critical concentration measurement in most of the MreB literature, this could be an important point to make in the field.

Following reviewer’s #2 suggestion, we have now estimated the critical concentration (Cc=0.4485 µM) and reported it in the text. (L218).

5) Both mg/ml and uM are used in the text and figures to refer to protein concentration. They should stick to one convention, preferably uM, as is standard in the polymer field.

Sorry for the confusion. We have homogenized to MreB concentrations to µM throughout the text and figures.

6) Lines 77-78 - (Teeffelen et al., 2011) should be referenced as well in regard to cell wall synthesis driving MreB motion.

This has been corrected, sorry for omitting this reference.

7) Line 90 - "Do they exhibit turnover (treadmill) like actin filaments?". This phrase should be modified, as turnover and treadmilling are two very different things. Turnover is the lifetime of monomers in filaments, while treadmilling entails monomer addition at one end and loss at the other. While treadmilling filaments cause turnover, there are also numerous examples of non-treadmilling filaments undergoing turnover: microtubules, intermediate filaments, and ParM. Likewise, an antiparallel filament cannot directionally treadmill, as there is no difference between the two filament ends to confer directional polarity.

This is absolutely true, we apologize for our mistake. The sentence has been corrected (L82).

8) Throughout the paper, the term aggregation is used occasionally to describe the polymerization shown in many previous MreB studies, almost all of which very clearly showed "bundled" filaments, very distinct entities from aggregates, as a bundle of polymers cannot form without the filaments first polymerizing on their own. Evidence to this point, polymerization has been shown to precede the bundling of MreB(Tm) by (Esue et al., 2005).

We agree with reviewer #2 about polymers preceding bundles and “sheets”. However, we respectfully disagree that we used the word aggregation “throughout the paper” to describe structures that clearly showed polymers or sheets of filaments. A search (Ctrl-F: “aggreg”) reveals only 6 matches, 3 describing our own observations (L152, 163/5, and 1023/28), one referring to (Salje et al., 2011) (L107) but citing her claim that they observed aggregation (due to the N-terminus), and the last two (L100, L440) refer (again) to the Gaballah/Mayer/Dersch publications to say that aggregation could not be excluded in these reports as discussed above (Dersch et al., 2020; Gaballah et al., 2011; Mayer & Amann, 2009).

9) lines 106-108 mention that "The N-terminal amphipathic helix of E. coli MreB (MreBEc) was found to be necessary for membrane binding. " This is not accurate, as Salje observed that one single helix could not cause MreB to mind to the membrane, but rather, multiple amphipathic helices were required for membrane association (Salje et al., 2011).

Salje et al showed that in vivo the deletion of the helix abolishes the association of MreB to the membrane. This publication also shows that in vitro, addition of the helix to GFP (not to MreB) prompts binding to lipid vesicles, and that this was increased if there are 2 copies of the helix, but they could not test this directly in vitro with MreB (which is insoluble when expressed with its N-terminus). This prompted them to speculate that multiple MreBs could bind better to the membrane than monomers. However, this remained to be demonstrated. Additional hydrophobic regions in MreB such as the hydrophobic loop could participate to membrane anchoring but are absent in their in vitro assays with GFP.

The Salje results imply that dimers (or further assemblies) of MreB drive membrane association, a point that should be discussed in regard to the question "What prompts the assembly of MreB on the inner leaflet of the cytoplasmic membrane?" posed on lines 86-87.

We agree that this is an interesting point. As it is consistent with our results, we have incorporated it to our model (Fig. 6) and we are addressing it in the discussion L573-575.

10) On lines 414-415, it is stated, "The requirement of the membrane for polymerization is consistent with the observation that MreB polymeric assemblies in vivo are membrane-associated only." While I agree with this hypothesis, it must be noted that the presence or absence of MreB polymers in the cytoplasm has not been directly tested, as short filaments in the cytoplasm would diffuse very quickly, requiring very short exposures (<5ms) to resolve them relative to their rate of diffusion. Thus, cytoplasmic polymers might still exist but have not been tested.

This is also an interesting point. Indeed if a nucleated form, or very short (unbundled) polymers exist in the cytoplasm, they have not been tested by fluorescence microscopy. However, the polymers that localize at the membrane (~ 200 nm), if soluble, would have been detected in the cytoplasm by the work of reviewer #2, us or others.

11) lines 429-431 state, "but polymerization in the presence of ADP was in most cases concluded from light scattering experiments alone, so the possibility that aggregation rather than ordered polymerization occurred in the process cannot be excluded."

A) If an increased light scattering signal is initiated by the addition of ADP (or any nucleotide), that signal must come from polymerization or multimerization. What the authors imply is that there must be some ADP-dependent "aggregation" of MreB, which has not been seen thus far for any polymer. Furthermore, why would the addition of ADP initiate aggregation?

We did not mean that ADP itself would prompt aggregation, but that the protein would aggregate in the buffer regardless of the presence of ADP or other nucleotides. The Mayer & Amann study claims that MreB “polymerization” is nucleotide-independent, as they got identical curves with ATP, ADP, AMPPNP and even with no nucleotides at all (Fig. 10 in their paper, pasted here) (Mayer & Amann, 2009).

Their experiments with KCl are also remarkable as when they lowered the salt they got faster and faster “polymerization”, with the strongest light scattering signal in the absence of any salt. The high KCl concentration in which they got almost no more “polymers” was 75 mM KCl, and ‘polymerization was almost entirely inhibited at 100 mM’ (Fig. 7, pasted below). Yet the intracellular level of KCl in bacteria is estimated to be ~300 mM (see Response 1.1)

B) Likewise, the statement "Differences in the purity of the nucleotide stocks used in these studies could also explain some of the discrepancies" is unexplained and confusing. How could an impurity in a nucleotide stock affect the past MreB results, and what is the precedent for this claim?

We meant that the presence of ATP in the ADP stocks might have affected the outcome of some assays, generating the conflicting results existing in the literature. We agree this sentence was confusing, we have removed it.

12) lines 467-469 state, "Thus, for both MreB and actin, despite hydrolyzing ATP before and after polymerization, respectively, the ADP-Pi-MreB intermediate would be the long-lived intermediate state within the filaments."

A) For MreB, this statement is extremely speculative and unbiased, as no one has measured 1) polymerization, 2) ATP hydrolysis, and 3) phosphate release. For example, it could be that ATP hydrolysis is slow, while phosphate release is fast, as is seen in the actin from Saccharomyces cerevisiae.

We agree that this was too speculative. This has been removed from the (extensively) modified Discussion section. Thanks for the comment.

B) For actin, the statement of hydrolysis of ATP of monomer occurring "before polymerization" is functionally irrelevant, as the rate of ATP hydrolysis of actin monomers is 430,000 times slower than that of actin monomers inside filaments (Blanchoin and Pollard, 2002; Rould et al., 2006).

We agree that the difference of hydrolysis rate between G-actin and F-actin implies that ATP hydrolysis occurs after polymerization. We are afraid that we do not follow the reviewer’s point here, we did not say or imply that ATP hydrolysis by actin monomers was functionally relevant.

13) Lines 442-444. "On the basis of our data and the existing literature, we propose that the requirement for ATP (or GTP) hydrolysis for polymerization may be conserved for most MreBs." Again, this statement both here (and in the prior text) is an extremely bold claim, one that runs contrary to a large amount of past work on not just MreB, but also eukaryotic actin and every actin homolog studied so far. They come to this model based on 1) one piece of suggestive data (the behavior of MreB(GS) bound to 2 non-hydrolysable ATP analogs in 500mM KCL), and 2) the dismissal (throughout the paper) of many peer-reviewed MreB papers that run counter to their model as "aggregation" or "contaminated ATP stocks ." If they want to make this bold claim that their finding invalidates the work of many labs, they must back it up with further validating experiments.

We respectfully disagree that our model was based on “one piece of suggestive data” and backed-up by dismissing most past work in the field. We only wanted to raise awareness about the conflicting data between some reports (listed in response 2.5a), and that the claims made by some publications are to be taken with caution because they only rely on light scattering or, when TEM was performed, showed only disorganized structures.

This said, we clearly failed in proposing our model and we are sorry to see that we really annoyed the reviewer with our suspicion that the work by Mayer & Amann reports aggregation. As indicated above, we have amended our manuscript relative to this point. We also agree that our suggestion to generalize our findings to most MreBs was unsupported, and overstated considering how confusing some result from the literature are. We have refined our model and reworked the text to take on board the reviewer’s remarks as well as the new data generated during the revision process.

We would like to thank reviewer #2 for his in-depth review of our manuscript.  

Reviewer #3 (Public Review):

The major claim from the paper is the dependence of two factors that determine the polymerization of MreB from a Gram-positive, thermophilic bacteria 1) The role of nucleotide hydrolysis in driving the polymerization. 2) Lipid bilayer as a facilitator/scaffold that is required for hydrolysis-dependent polymerization. These two conclusions are contrasting with what has been known until now for the MreB proteins that have been characterized in vitro. The experiments performed in the paper do not completely justify these claims as elaborated below.

We understand the reviewer’ concerns in view of the existing literature on actin and Gram-negative MreBs. We may just be missing the optimal conditions for polymerisation in solution, while our phrasing gave the impression that polymers could never form in the absence of ATP or lipids. Our new data actually shows that MreBGs at higher concentration can assemble into bundle- and sheet-like structures in solution and in the presence of ADP/AMP-PNP. Pairs of filaments are however only observed in the presence of lipids for all conditions tested. As indicated in the answers to the global review comments, we have included our new data in the manuscript, revised our conclusions and claims about the lipid requirement and expanded on these points in the Discussion.

Major comments:

1) No observation of filaments in the absence of lipid monolayer can also be accounted due to the higher critical concentration of polymerization for MreBGS in that condition. It is seen that all the negative staining without lipid monolayer condition has been performed at a concentration of 0.05 mg/mL. It is important to check for polymerization of the MreBGS at higher concentration ranges as well, in order to conclusively state the requirement of lipids for polymerization.

Response 3.1. 0.05 mg/ml (1.3µM) is our standard condition, and our leeway was limited by the rapid aggregation observed at higher MreB concentrations, as indicated in the text. We have now tested as well 0.25 mg/ml (6.5 µM - the maximum concentration possible before major aggregation occurs in our experimental conditions). At this higher concentration, we see some sheet-like structures in solution, confirming a requirement of a higher concentration of MreB for polymerization in these conditions (see the answers to the global review comments for more details)

We thank the reviewer for pushing us to address this point. We have revised our conclusions accordingly.

2) The absence of filaments for the non-hydrolysable conditions in the lipid layer could also be because the filaments that might have formed are not binding to the planar lipid layer, and not necessarily because of their inability to polymerize.

Response 3.2. This is a fair point. To test the possibility that polymers would form but would not bind to the lipid layer we have now added additional semi-quantitative EM controls (for both the non-hydrolysable ATP analogs and the three ‘membrane binding’ deletion mutants) testing polymerization in solution (without lipids) and also using plasma-treated grids. These showed that in our standard polymerization conditions, virtually no polymers form in solution (Fig. 3-S1B and Fig. 4-S4A). Albeit at very low frequency, some dual protofilaments were however detected in the presence of ADP or AMP-PNP at the high MreB concentration (Fig. 3-S1D). At this high MreB concentration, the sheet-like structures occasionally observed in solution in the presence of ATP were frequent in the presence of ADP and very frequent in the presence of AMP-PNP (Fig. 3-S2B). We have revised our conclusions on the basis of these new data: MreBGs can form polymeric assemblies in solution and in the absence of ATP hydrolysis at a higher critical concentration than in the presence of ATP and lipids.

See the answers to the global review comments (point 2) and Response 2.3C to reviewer #2 for more details.

3) Given the ATPase activity measurements, it is not very convincing that ATP rather than ADP will be present in the structure. The ATP should have been hydrolysed to ADP within the structure. The structure is now suggestive that MreB is not capable of hydrolysis, which is contradictory to the ATP hydrolysis data.

Response 3.3. We thank the reviewer for her insightful remarks about the MreB-ATP crystal structure. The electron density map clearly demonstrates the presence of 3 phosphates. However, as suggested by the reviewer, the density which was attributed to a Mg2+ ion was to be interpreted as a water molecule. The absence of Mg2+ in the crystal could thus explain why the ATP had not been hydrolyzed.

References

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Author Response

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

eLife assessment

This important paper exploits new cryo-EM tomography tools to examine the state of chromatin in situ. The experimental work is meticulously performed and convincing, with a vast amount of data collected. The main findings are interpreted by the authors to suggest that the majority of yeast nucleosomes lack a stable octameric conformation. Despite the possibly controversial nature of this report, it is our hope that such work will spark thought-provoking debate, and further the development of exciting new tools that can interrogate native chromatin shape and associated function in vivo.

We thank the Editors and Reviewers for their thoughtful and helpful comments. We also appreciate the extraordinary amount of effort needed to assess both the lengthy manuscript and the previous reviews. Below, we provide our point-by-point response in bold blue font. Nearly all comments have been addressed in the revised manuscript. For a subset of comments that would require us to speculate, we have taken a conservative approach because we either lack key information or technical expertise: Instead of adding the speculative replies to the main text, we think it is better to leave them in the rebuttal for posterity. Readers will thereby have access to our speculation and know that we did not feel confident enough to include these thoughts in the Version of Record.

Reviewer #1 (Public Review):

This manuscript by Tan et al is using cryo-electron tomography to investigate the structure of yeast nucleosomes both ex vivo (nuclear lysates) and in situ (lamellae and cryosections). The sheer number of experiments and results are astounding and comparable with an entire PhD thesis. However, as is always the case, it is hard to prove that something is not there. In this case, canonical nucleosomes. In their path to find the nucleosomes, the authors also stumble over new insights into nucleosome arrangement that indicates that the positions of the histones is more flexible than previously believed.

Please note that canonical nucleosomes are there in wild-type cells in situ, albeit rarer than what’s expected based on our HeLa cell analysis and especially the total number of yeast nucleosomes (canonical plus non-canonical). The negative result (absence of any canonical nucleosome classes in situ) was found in the histone-GFP mutants.

Major strengths and weaknesses:

Personally, I am not ready to agree with their conclusion that heterogenous non-canonical nucleosomes predominate in yeast cells, but this reviewer is not an expert in the field of nucleosomes and can't judge how well these results fit into previous results in the field. As a technological expert though, I think the authors have done everything possible to test that hypothesis with today's available methods. One can debate whether it is necessary to have 35 supplementary figures, but after working through them all, I see that the nature of the argument needs all that support, precisely because it is so hard to show what is not there. The massive amount of work that has gone into this manuscript and the state-of-the art nature of the technology should be warmly commended. I also think the authors have done a really great job with including all their results to the benefit of the scientific community. Yet, I am left with some questions and comments:

Could the nucleosomes change into other shapes that were predetermined in situ? Could the authors expand on if there was a structure or two that was more common than the others of the classes they found? Or would this not have been found because of the template matching and later reference particle used?

Our best guess (speculation) is that one of the class averages that is smaller than the canonical nucleosome contains one or more non-canonical nucleosome classes. However, we do not feel confident enough to single out any of these classes precisely because we do not yet know if they arise from one non-canonical nucleosome structure or from multiple – and therefore mis-classified – non-canonical nucleosome structures (potentially with other non-nucleosome complexes mixed in). We feel it is better to leave this discussion out of the manuscript, or risk sending the community on wild goose chases.

Our template-matching workflow uses a low-enough cross-correlation threshold that any nucleosome-sized particle (plus minus a few nanometers) would be picked, which is why the number of hits is so large. So unless the noncanonical nucleosomes quadrupled in size or lost most of their histones, they should be grouped with one or more of the other 99 class averages (WT cells) or any of the 100 class averages (cells with GFP-tagged histones). As to whether the later reference particle could have prevented us from detecting one of the non-canonical nucleosome structures, we are unable to tell because we’d really have to know what an in situ non-canonical nucleosome looks like first.

Could it simply be that the yeast nucleoplasm is differently structured than that of HeLa cells and it was harder to find nucleosomes by template matching in these cells? The authors argue against crowding in the discussion, but maybe it is just a nucleoplasm texture that side-tracks the programs?

Presumably, the nucleoplasmic “side-tracking” texture would come from some molecules in the yeast nucleus. These molecules would be too small to visualize as discrete particles in the tomographic slices, but they would contribute textures that can be “seen” by the programs – in particular RELION, which does the discrimination between structural states. We are not sure what types of density textures would side-track RELION’s classification routines.

The title of the paper is not well reflected in the main figures. The title of Figure 2 says "Canonical nucleosomes are rare in wild-type cells", but that is not shown/quantified in that figure. Rare is comparison to what? I suggest adding a comparative view from the HeLa cells, like the text does in lines 195-199. A measure of nucleosomes detected per volume nucleoplasm would also facilitate a comparison.

Figure 2’s title is indeed unclear and does not align with the paper’s title and key conclusion. The rarity here is relative to the expected number of nucleosomes (canonical plus non-canonical). We have changed the title to:

“Canonical nucleosomes are a minority of the expected total in wild-type cells”.

We would prefer to leave the reference to HeLa cells to the main text instead of as a figure panel because the comparison is not straightforward for a graphical presentation. Instead, we now report the total number of nucleosomes estimated for this particular yeast tomogram (~7,600) versus the number of canonical nucleosomes classified (297; 594 if we assume we missed half of them). This information is in the revised figure legend:

“In this tomogram, we estimate there are ~7,600 nucleosomes (see Methods on how the calculation is done), of which 297 are canonical structures. Accounting for the missing disc views, we estimate there are ~594 canonical nucleosomes in this cryolamella (< 8% the expected number of nucleosomes).”

If the cell contains mostly non-canonical nucleosomes, are they really non-canonical? Maybe a change of language is required once this is somewhat sure (say, after line 303).

This is an interesting semantic and philosophical point. From the yeast cell’s “perspective”, the canonical nucleosome structure would be the form that is in the majority. That being said, we do not know if there is one structure that is the majority. From the chromatin field’s point of view, the canonical nucleosome is the form that is most commonly seen in all the historical – and most contemporary – literature, namely something that resembles the crystal structure of Luger et al, 1997. Given these two lines of thinking, we added the following clarification as lines 312 – 316:

“At present, we do not know what the non-canonical nucleosome structures are, meaning that we cannot even determine if one non-canonical structure is the majority. Until we know the non-canonical nucleosomes’ structures, we will use the term non-canonical to describe all the nucleosomes that do not have the canonical (crystal) structure.”

The authors could explain more why they sometimes use conventional the 2D followed by 3D classification approach and sometimes "direct 3-D classification". Why, for example, do they do 2D followed by 3D in Figure S5A? This Figure could be considered a regular figure since it shows the main message of the paper.

Since the classification of subtomograms in situ is still a work in progress, we felt it would be better to show one instance of 2-D classification for lysates and one for lamellae. While it is true that we could have presented direct 3-D classification for the entire paper, we anticipate that readers will be interested to see what the in situ 2-D class averages look like.

The main message is that there are canonical nucleosomes in situ (at least in wild-type cells), but they are a minority. Therefore, the conventional classification for Figure S5A should not be a main figure because it does not show any canonical nucleosome class averages in situ.

Figure 1: Why is there a gap in the middle of the nucleosome in panel B? The authors write that this is a higher resolution structure (18Å), but in the even higher resolution crystallography structure (3Å resolution), there is no gap in the middle.

There is a lower concentration of amino acids at the middle in the disc view; unfortunately, the space-filling model in Figure 1A hides this feature. The gap exists in experimental cryo-EM density maps. See Author response image 1 for an example (pubmed.ncbi.nlm.nih.gov/29626188). The size of the gap depends on the contour level and probably the contrast mechanism, as the gap is less visible in the VPP subtomogram averages. To clarify this confusing phenomenon, we added the following lines to the figure legend:

“The gap in the disc view of the nuclear-lysate-based average is due to the lower concentration of amino acids there, which is not visible in panel A due to space-filling rendering. This gap’s visibility may also depend on the contrast mechanism because it is not visible in the VPP averages.”

Author response image 1.

Reviewer #2 (Public Review):

Nucleosome structures inside cells remain unclear. Tan et al. tackled this problem using cryo-ET and 3-D classification analysis of yeast cells. The authors found that the fraction of canonical nucleosomes in the cell could be less than 10% of total nucleosomes. The finding is consistent with the unstable property of yeast nucleosomes and the high proportion of the actively transcribed yeast genome. The authors made an important point in understanding chromatin structure in situ. Overall, the paper is well-written and informative to the chromatin/chromosome field.

We thank Reviewer 2 for their positive assessment.

Reviewer #3 (Public Review):

Several labs in the 1970s published fundamental work revealing that almost all eukaryotes organize their DNA into repeating units called nucleosomes, which form the chromatin fiber. Decades of elegant biochemical and structural work indicated a primarily octameric organization of the nucleosome with 2 copies of each histone H2A, H2B, H3 and H4, wrapping 147bp of DNA in a left handed toroid, to which linker histone would bind.

This was true for most species studied (except, yeast lack linker histone) and was recapitulated in stunning detail by in vitro reconstitutions by salt dialysis or chaperone-mediated assembly of nucleosomes. Thus, these landmark studies set the stage for an exploding number of papers on the topic of chromatin in the past 45 years.

An emerging counterpoint to the prevailing idea of static particles is that nucleosomes are much more dynamic and can undergo spontaneous transformation. Such dynamics could arise from intrinsic instability due to DNA structural deformation, specific histone variants or their mutations, post-translational histone modifications which weaken the main contacts, protein partners, and predominantly, from active processes like ATP-dependent chromatin remodeling, transcription, repair and replication.

This paper is important because it tests this idea whole-scale, applying novel cryo-EM tomography tools to examine the state of chromatin in yeast lysates or cryo-sections. The experimental work is meticulously performed, with vast amount of data collected. The main findings are interpreted by the authors to suggest that majority of yeast nucleosomes lack a stable octameric conformation. The findings are not surprising in that alternative conformations of nucleosomes might exist in vivo, but rather in the sheer scale of such particles reported, relative to the traditional form expected from decades of biochemical, biophysical and structural data. Thus, it is likely that this work will be perceived as controversial. Nonetheless, we believe these kinds of tools represent an important advance for in situ analysis of chromatin. We also think the field should have the opportunity to carefully evaluate the data and assess whether the claims are supported, or consider what additional experiments could be done to further test the conceptual claims made. It is our hope that such work will spark thought-provoking debate in a collegial fashion, and lead to the development of exciting new tools which can interrogate native chromatin shape in vivo. Most importantly, it will be critical to assess biological implications associated with more dynamic - or static forms- of nucleosomes, the associated chromatin fiber, and its three-dimensional organization, for nuclear or mitotic function.

Thank you for putting our work in the context of the field’s trajectory. We hope our EMPIAR entry, which includes all the raw data used in this paper, will be useful for the community. As more labs (hopefully) upload their raw data and as image-processing continues to advance, the field will be able to revisit the question of non-canonical nucleosomes in budding yeast and other organisms. 

Reviewer #1 (Recommendations For The Authors):

The manuscript sometimes reads like a part of a series rather than a stand-alone paper. Be sure to spell out what needs to be known from previous work to read this article. The introduction is very EM-technique focused but could do with more nucleosome information.

We have added a new paragraph that discusses the sources of structural variability to better prepare readers, as lines 50 – 59:

“In the context of chromatin, nucleosomes are not discrete particles because sequential nucleosomes are connected by short stretches of linker DNA. Variation in linker DNA structure is a source of chromatin conformational heterogeneity (Collepardo-Guevara and Schlick, 2014). Recent cryo-EM studies show that nucleosomes can deviate from the canonical form in vitro, primarily in the structure of DNA near the entry/exit site (Bilokapic et al., 2018; Fukushima et al., 2022; Sato et al., 2021; Zhou et al., 2021). In addition to DNA structural variability, nucleosomes in vitro have small changes in histone conformations (Bilokapic et al., 2018). Larger-scale variations of DNA and histone structure are not compatible with high-resolution analysis and may have been missed in single-particle cryo-EM studies.”

Line 165-6 "did not reveal a nucleosome class average in..". Add "canonical", since it otherwise suggests there were no nucleosomes.

Thank you for catching this error. Corrected.

Lines 177-182: Why are the disc views missed by the classification analysis? They should be there in the sample, as you say.

We suspect that RELION 3 is misclassifying the disc-view canonical nucleosomes into the other classes. The RELION developers suspect that view-dependent misclassification arises from RELION 3’s 3-D CTF model. RELION 4 is reported to be less biased by the particles’ views. We have started testing RELION 4 but do not have anything concrete to report yet.

Line 222: a GFP tag.

Fixed.

Line 382: "Note that the percentage .." I can't follow this sentence. Why would you need to know how many chromosome's worth of nucleosomes you are looking at to say the percentage of non-canonical nucleosomes?

Thank you for noticing this confusing wording. The sentence has been both simplified and clarified as follows in lines 396 – 398:

“Note that the percentage of canonical nucleosomes in lysates cannot be accurately estimated because we cannot determine how many nucleosomes in total are in each field of view.”

Line 397: "We're not implying that..." Please add a sentence clearly stating what you DO mean with mobility for H2A/H2B.

We have added the following clarifying sentence in lines 412 – 413:

“We mean that H2A-H2B is attached to the rest of the nucleosome and can have small differences in orientation.”

Line 428: repeated message from line 424. "in this figure, the blurring implies.."

Redundant phrase removed.

Line 439: "on a HeLa cell" - a single cell in the whole study?

Yes, that study was done on a single cell.

A general comment is that the authors could help the reader more by developing the figures and making them more pedagogical, a list of suggestions can be found below.

Thank you for the suggestions. We have applied all of them to the specific figure callouts and to the other figures that could use similar clarification.

Figure 2: Help the reader by avoiding abbreviations in the figure legend. VPP tomographic slice - spell out "Volta Phase Plate". Same with the term "remapped" (panel B) what does that mean?

We spelled out Volta phase plate in full and explained “remapped” the additional figure legend text:

“the class averages were oriented and positioned in the locations of their contributing subtomograms”.

Supplementary figures:

Figure S3: It is unclear what you mean with "two types of BY4741 nucleosomes". You then say that the canonical nucleosomes are shaded blue. So what color is then the non-canonical? All the greys? Some of them look just like random stuff, not nucleosomes.

“Two types” is a typo and has been removed and “nucleosomes” has been replaced with “candidate nucleosome template-matching hits” to accurately reflect the particles used in classification.

Figure S6: Top left says "3 tomograms (defocus)". I wonder if you meant to add the defocus range here. I have understood it like this is the same data as shown in Figure S5, which makes me wonder if this top cartoon should not be on top of that figure too (or exclusively there).

To make Figures S6 (and S5) clearer, we have copied the top cartoon from Figure S6 to S5.

Note that we corrected a typo for these figures (and the Table S7): the number of template-matched candidate nucleosomes should be 93,204, not 62,428.

The description in the parentheses (defocus) is shorthand for defocus phase contrast and was not intended to also display a defocus range. All of the revised figure legends now report the meaning of both this shorthand and of the Volta phase plate (VPP).

To help readers see the relationship between these two figures, we added the following clarifying text to the Figure S5 and S6 legends, respectively:

“This workflow uses the same template-matched candidate nucleosomes as in Figure S6; see below.”

“This workflow uses the same template-matched candidate nucleosomes as in Figure S5.”

Figure S7: In the first panel, it is unclear why the featureless cylinder is shown as it is not used as a reference here. Rather, it could be put throughout where it was used and then put the simulated EM-map alone here. If left in, it should be stated in the legend that it was not used here.

It would indeed be much clearer to show the featureless cylinder in all the other figures and leave the simulated nucleosome in this control figure. All figures are now updated. The figure legend was also updated as follows:

“(A) A simulated EM map from a crystal structure of the nucleosome was used as the template-matching and 3-D classification reference.”

Figure S18: Why are there classes where the GFP density is missing? Mention something about this in the figure legend.

We have appended the following speculations to explain the “missing” GFP densities:

“Some of the class averages are “missing” one or both expected GFP densities. The possible explanations include mobility of a subpopulation of GFPs or H2A-GFPs, incorrectly folded GFPs, or substitution of H2A for the variant histone H2A.Z.”

Reviewer #2 (Recommendations For The Authors):

My specific (rather minor) comments are the following:

1) Abstract:

yeast -> budding yeast.

All three instances in the abstract have been replaced with “budding yeast”.

It would be better to clarify what ex vivo means here.

We have appended “(in nuclear lysates)” to explain the meaning of ex vivo.

2) Some subtitles are unclear.

e.g., "in wild-type lysates" -> "wild-type yeast lysates"

Thank you for this suggestion. All unclear instances of subtitles and sample descriptions throughout the text have been corrected.

3) Page 6, Line 113. "...which detects more canonical nucleosomes." A similar thing was already mentioned in the same paragraph and seems redundant.

Thank you for noticing this redundant statement, which is now deleted.

4) Page 25, Line 525. "However, crowding is an unlikely explanation..." Please note that many macromolecules (proteins, RNAs, polysaccharides, etc.) were lost during the nuclei isolation process.

This is a good point. We have rewritten this paragraph to separate the discussion on technical versus biological effects of crowding, in lines 538 – 546:

“Another hypothesis for the low numbers of detected canonical nucleosomes is that the nucleoplasm is too crowded, making the image processing infeasible. However, crowding is an unlikely technical limitation because we were able to detect canonical nucleosome class averages in our most-crowded nuclear lysates, which are so crowded that most nucleosomes are butted against others (Figures S15 and S16). Crowding may instead have biological contributions to the different subtomogram-analysis outcomes in cell nuclei and nuclear lysates. For example, the crowding from other nuclear constituents (proteins, RNAs, polysaccharides, etc.) may contribute to in situ nucleosome structure, but is lost during nucleus isolation.”

5) Page 7, Line 126. "The subtomogram average..." Is there any explanation for this?

Presumably, the longer linker DNA length corresponds to the ordered portion of the ~22 bp linker between consecutive nucleosomes, given the ~168 bp nucleosome repeat length. We have appended the following explanation as the concluding sentence, lines 137 – 140:

“Because the nucleosome-repeat length of budding yeast chromatin is ~168 bp (Brogaard et al., 2012), this extra length of DNA may come from an ordered portion of the ~22 bp linker between adjacent nucleosomes.”

6) "Histone GFP-tagging strategy" subsection:

Since this subsection is a bit off the mainstream of the paper, it can be shortened and merged into the next one.

We have merged the “Histone GFP-tagging strategy” and “GFP is detectable on nucleosome subtomogram averages ex vivo” subsections and shortened the text as much as possible. The new subsection is entitled “Histone GFP-tagging and visualization ex vivo”

7) Page 16, Line 329. "Because all attempts to make H3- or H4-GFP "sole source" strains failed..." Is there a possible explanation here? Cytotoxic effect because of steric hindrance of nucleosomes?

Yes, it is possible that the GFP tag is interfering with the nucleosomes interactions with its numerous partners. It is also possible that the histone-GFP fusions do not import and/or assemble efficiently enough to support a bare-minimum number of functional nucleosomes. Given that the phenotypic consequences of fusion tags is an underexplored topic and that we don’t have any data on the (dead) transformants, we would prefer to leave out the speculation about the cause of death in the attempted creation of “sole source” strains.

Author Response

Reviewer #1 (Public Review):

The manuscript investigates how humans store temporal sequences of tones in working memory. The authors mainly focus on a theory named "Language of thought" (LoT). Here the structure of a stimulus sequence can be stored in a tree structure that integrates the dependencies of a stimulus stored in working memory. To investigate the LoT hypothesis, participants listened to multiple stimulus sequences that varied in complexity (e.g., alternating tones vs. nearly random sequence). Simultaneously, the authors collected fMRI or MEG data to investigate the neuronal correlates of LoT complexity in working memory. Critical analysis was based on a deviant tone that violated the stored sequence structure. Deviant detection behavior and a bracketing task allowed a behavioral analysis.

Results showed accurate bracketing and fast/correct responses when LoT complexity is low. fMRI data showed that LoT complexity correlated with the activation of 14 clusters. MEG data showed that LoT complexity correlated mainly with activation from 100-200 ms after stimulus onset. These and other analyses presented in the manuscript lead the authors to conclude that such tone sequences are represented in human memory using LoT in contrast to alternative representations that rely on distinct memory slot representations.

Strengths

The study provides a concise and easily accessible introduction. The task and stimuli are well described and allow a good understanding of what participants experience while their brain activation is recorded. Results are extensive as they include multiple behavioral investigations and brain activation data from two different measurement modalities. The presentation of the behavioral results is intuitive. The analysis provided a direct comparison of the LoT with an alternative model based on estimating a transition-probability measure of surprise.

For the fMRI data, the whole brain analysis was accompanied by detailed region of interest analyses, including time course analysis, for the activation clusters correlated with LoT complexity. In addition, the activation clusters have been set in relation (overlap and region of interest analyses) to a math and a language localizer. For the MEG data, the authors investigated the LoT complexity effect based on linear regression, including an analysis that also included transitional probabilities and multivariate decoding analysis. The discussion of the results focused on comparing the activation patterns of the task with the localizer tasks. Overall, the authors have provided considerable new data in multiple modalities on a well-designed experiment investigating how humans represent sequences in auditory working memory.

Weaknesses

The primary issue of the manuscript is the missing formal description of the LoT model and alternatives, inconsistencies in the model comparisons, and no clear argumentation that would allow the reader to understand the selection of the alternative model. Similar to a recent paper by similar authors (Planton et al., 2021 PLOS Computational Biology), an explicit model comparison analysis would allow a much stronger conclusion. Also, these analyses would provide a more extensive evidence base for the favored LoT model. Needed would be a clear argumentation for why the transitional probabilities were identified as the most optimal alternative model for a critical test. A clear description of the models (e.g., how many free parameters) and a description of the simulation procedure (e.g., are they trained, etc.) Here it would be strongly advised to provide the scripts that allow others to reproduce the simulations.

We thank the reviewer for the requests and critiques. Although this paper follows upon our extensive prior behavioral work (Planton et al.), we agree that it should stand alone and that therefore the models need to be described more fully. We have now added a formal description of the LoT in the subsection The Language of Thought for binary sequences in the Results section and have added a formal and verbal description of the selected sequences in Figure 1-figure supplement 1. Furthermore, we added a model comparison similar to the one done in (Planton et al., 2021 PLOS Computational Biology). This analysis is now included in Figure 2 and in the Behavioral data subsection of the Results section. It replicates previous behavioral results obtained in Planton et al., 2021 PLOS Computational Biology, namely that complexity, as measured by minimal description length in the binary version of the “language of geometry” was the best predictor of participants’ behaviour.

Interestingly, we found that the model that considered both complexity and surprise had even lower AIC suggesting that statistical learning is simultaneously occurring in the brain (Brain signatures of a multiscale process of sequence learning in humans, M Maheu, S Dehaene, F Meyniel - eLife, 2019). In this respect, we do not consider surprise from transition probabilities as an alternative model but rather as a mechanism that is occurring in parallel to sequence compression. The main goal of this work was to determine how sequence processing was affected by sequence structure, captured by the language of thought. In this line, we didn't select the tested sequences in order to investigate statistical learning but, instead, chose them with similar global statistical properties.

The MEG experiment provided us with the opportunity to separate temporally the contributions of statistical mechanisms from the ones of sequence compression according to the language of thought. Indeed, contrary to the fMRI experiment, we could model at the item level the statistical properties of individual sounds. We report the results when accounting jointly for statistical processing and LoT-complexity in Supplementary materials.

The different models considered in previous work didn’t need to be trained. The sequence complexity they provided could be analytically computed based on sequence minimal description length.

Furthermore, the manuscript needs a clear motivation for the type of sequences and some methodological decisions. Central here is the quadratic trend selectively used for the fMRI analysis but not for the other datasets.

To design the MEG, we had to decrease the number of sequences from 10 to 7. We selected them based on the LoT-complexity and the type of sequence information they spanned. As a consequence, the predictors for linear and quadratic complexity are very correlated (82%). Unfortunately, due to low SNR, this doesn’t allow to robustly account for the contributions of quadratic complexity in the MEG-recorded brain signals. Still, in response to the referee, we performed a linear regression as a function of quadratic complexity on the residuals of the regression as function of statistics and complexity that we report here. No significant clusters were found for habituation and standard trials but two were found (corresponding to the same topography) for deviant trials for late time-points.

In Author response image 1 regression coefficients for the quadratic complexity regressor regressed on the residuals of the surprise from transition probabilities and complexity. In Author response image 2, 2 significant clusters were found for the deviant sounds.

We also averaged the decoding scores from Figure7.A over the time-window obtained from the temporal cluster-based permutation test (see Author response image 2). The choice of complexity values didn’t allow any clear assessment of the contribution of the quadratic complexity term.

In summary, in the current design, we do not think that the number of tested sequences allows us to clearly conclude that no quadratic effect can be found for Habituation and Standard trials. We would need to re-design an experiment to test specifically the quadratic complexity contribution to brain signals in MEG.

Author response image 1.

Author response image 2.

Also, the description of the linear mixed models is missing (e.g., the random effect structure, e.g., see Bates, D., Kliegl, R., Vasishth, S., & Baayen, H. (2015). Parsimonious mixed models. arXiv preprint arXiv:1506.04967.). Moreover, sample sizes have not been justified by a power analysis.

The linear mixed model that is considered in this work is very simple, it only uses Subject as a random variable. This is now stated clearly in the corresponding part in the Experimental procedures section:

To test whether subject performance correlated with LoT complexity, we performed linear regressions on group-averaged data, as well linear mixed models including participant as the (only) random factor. The random effect structure of the mixed models was kept minimal, and did not include any random slopes, to avoid the convergence issues often encountered when attempting to fit more complex models.

Author Response

Reviewer #1 (Public Review):

The actual description of the methods does not allow the reader to evaluate the precision of two important processing steps. First, rCBF measures are supposed to be restricted to the cortex, but given the pCASL image spatial resolution, partial volume effects with white matter probably exist, especially in younger infants. Furthermore, segmenting tissues on the basis of anatomical images (especially T1-weighted) is complicated in the first postnatal year. As rCBF measurements are very different between grey and white matter, the performed procedure might impact the measures at each age, or even lead to a systematic bias on age-dependent changes. Second, the methodology and accuracy of the brain registration across infants are little detailed whereas it is a challenging aspect given the intense brain growth and folding, the changing contrast in T1w images at these ages, and the importance of this step to perform reliable voxelwise comparison across ages.

We thank the reviewer for this comment. We have added more descriptions in the methods to address this comment. Briefly, individual rCBF map was generated in the individual space and calibrated by phase contrast MRI to minimize the individual variations of processing parameters such as T1 of arterial blood (Aslan et al., 2010). Cortical segmentation was also conducted in individual space. Then different types of images including rCBF map and gray matter segmentation probability map in the individual space were normalized into the template space. An averaged gray matter probability map was generated after inter-subject normalization. After carefully testing multiple thresholds in the averaged gray matter probability maps, 40% probability minimizing the contamination of white matter and CSF while keeping the continuity of the cortical gray matter mask across the cerebral cortex was used to generate the binary gray matter mask shown on the left panel of Figure R1 below. Despite poor contrasts and poor cortical segmentation of T1-weighted images of younger infants rightfully pointed out by this reviewer, the poor cortical segmentation of younger infants was compensated by the averaged cortical mask and measurement of rCBF in the template space. As demonstrated in the right three panels in Figure R1, the rCBF measure in the cortical mask in the template space is consistent across ages for accurate and reliable voxelwise comparison across age.

Figure R1. The gray matter mask and segmented cortical mask overlaid on rCBF map of three representative infants aged 3, 6, and 20 months in the template space. The gray matter mask on the left panel was created to minimize the contamination of white matter and CSF while keeping the continuity of the cortical gray matter mask across the cerebral cortex. The contour of the gray matter mask was highlighted with bule line.

The authors achieved their aim in showing that the rCBF increase differs across brain regions (the DMN showing intense changes compared to the visual and sensorimotor networks). Nevertheless, an analysis of covariance (instead of an ANOVA) including the infants' age as covariate (in addition to the brain region) would have allowed them to evaluate the interaction between age and region (i.e. different slopes of age-related changes across regions) in a more rigorous manner. Regarding the evaluation of the coupling between physiological (rCBF) and functional connectivity measures, the results only partly support the authors' conclusion. Actually, both measures strongly depend on the infants' age, as the authors highlight in the first parts of the study. Thus, considering this common age dependency would be required to show that the physiological and connectivity measurements are specifically related and that there is indeed a coupling.

We thank the reviewer for this comment. Following the reviewer’s suggestion, we conducted an analysis of covariance (ANCOVA) and found significant interaction between regions and age (F(6, 322) = 2.45, p < 0.05) with age as a covariate. This ANCOVA result is consistent with Figure 3c showing differential rCBF increase rates across brain regions. The ANCOVA result was added in the last paragraph in the Results section “Faster rCBF increases in the DMN hub regions during infant brain development”.

Regarding the evaluation of the coupling between physiological (rCBF) and functional connectivity measures (FC), the Figure 5, Figure 5–figure supplement 1 and 2 were generated exactly to test that the FC-rCBF coupling specifically localized in the DMN is not due to mutual age dependency. Briefly, Figure 5B demonstrated significant correlation only clustered in the DMN regions using the correlation method demonstrated in Figure 5-figure supplement 1. Furthermore, nonparametric permutation tests with 10,000 permutations were conducted. Such permutation tests are sensitive and effective with Figure 5c revealing significant coupling only in the DMN regions. If coupling is related to mutual age dependency, Figure 5c would demonstrate significant coupling in Vis and SM network regions too.

Author Response

Reviewer #1 (Public Review):

Briggs et al use a combination of mathematical modelling and experimental validation to tease apart the contributions of metabolic and electronic coupling to the pancreatic beta cell functional network. A number of recent studies have shown the existence of functional beta cell subpopulations, some of which are difficult to fully reconcile with established electrophysiological theory. More generally, the contribution of beta cell heterogeneity (metabolism, differentiation, proliferation, activity) to islet function cannot be explained by existing combined metabolic/electrical oscillator models. The present studies are thus timely in modelling the islet electrical (structural) and functional networks. Importantly, the authors show that metabolic coupling primarily drives the islet functional network, giving rise to beta cell subpopulations. The studies, however, do not diminish the critical role of electrical coupling in dictating glucose responsiveness, network extent as well as longer-range synchronization. As such, the studies show that islet structural and functional networks both act to drive islet activity, and that conclusions on the islet structural network should not be made using measures of the functional network (and vice versa).

Strengths:

• State-of-the-art multi-parameter modelling encompassing electrical and metabolic components.

• Experimental validation using advanced FRAP imaging techniques, as well as Ca2+ data from relevant gap junction KO animals.

• Well-balanced arguments that frame metabolic and electrical coupling as essential contributors to islet function.

• Likely to change how the field models functional connectivity and beta cell heterogeneity.

Weaknesses:

• Limitations of FRAP and electrophysiological gap junction measures not considered.

• Limitations of Cx36 (gap junction) KO animals not considered.

• Accuracy of citations should be improved in a few cases.

We thank reviewer 1 for their positive comments, including the many strengths in the approaches, arguments and impact. We do note the weaknesses raised by the reviewer and have addressed them following the comments below.

We would like to also note that when we refer to metabolic activity driving the functional network, we are not referring to metabolic coupling between beta cells. Rather we mean that two cells that show either high levels of metabolic activity (glycolytic flux) or that show similar levels metabolic activity will show increased synchronization and thus a functional network edge as compares to cells with elevated gap junction conductance. Increased metabolic activity would likely generate increased depolarizing currents that will provide an increased coupling current to drive synchronization; whereas similar metabolic activity would mean a given coupling current could more readily drive synchronized activity. We have substantially rewritten the manuscript to clarify this point.

Reviewer #2 (Public Review):

In their present work, Briggs et al. combine biophysical simulations and experimental recordings of beta cell activity with analyses of functional network parameters to determine the role played by gap-junctional coupling, metabolism, and KATP conductance in defining the functional roles that the cells play in the functional networks, assess the structure-function relationship, and to resolve an important current open question in the field on the role of so-called hub cells in islets of Langerhans.

Combining differential equation-based simulations on 1000 coupled cells with demanding calcium, NAPDH, and FRAP imaging, as well as with advanced network analyses, and then comparing the network metrics with simulated and experimentally determined properties is an achievement in its own right and a major methodological strength. The findings have the potential to help resolve the issue of the importance of hub cells in beta cell networks, and the methodological pipeline and data may prove invaluable for other researchers in the community.

However, methodologically functional networks may be based on different types of calcium oscillations present in beta cells, i.e., fast oscillations produced by bursts of electrical activity, slow oscillations produced by metabolic/glycolytic oscillations, or a mixture of both. At present, the authors base the network analyses on fast oscillations only in the case of simulated traces and on a mixture of fast and slow oscillations in the case of experimental traces. Since different networks may depend on the studied beta cell properties to a different extent (e.g., fast oscillation-based networks may, more importantly, depend on electrical properties and slow oscillationbased networks may more strongly depend on metabolic properties), it is important that in drawing the conclusions the authors separately address the influence of a cell's electrical and metabolic properties on its functional role in the network based on fast oscillations, slow oscillations, or a mixture of both.

We thank reviewer 2 for their positive comments, including addressing the importance of this study as it pertains to islet biology and acknowledging methodological complexities of this study. We also thank the reviewer for their careful reading and providing useful comments. We have integrated each comment into the manuscript. Most importantly, we have now extended our analysis to both fast and slow oscillations by incorporating an additional mathematical model of coupled slow oscillations and performing additional experimental analysis of fast, slow, and mixed oscillations.

Reviewer #3 (Public Review):

Over the past decade, novel approaches to understanding beta cell connectivity and how that contributes to the overall function of the pancreatic islet have emerged. The application of network theory to beta cell connectivity has been an extremely useful tool to understand functional hierarchies amongst beta cells within an islet. This helps to provide functional relevance to observations from structural and gene expression data that beta cells are not all identical.

There are a number of "controversies" in this field that have arisen from the mathematical and subsequent experimental identification of beta "hub" cells. These are small populations of beta cells that are very highly connected to other beta cells, as assessed by applying correlation statistics to individual beta cell calcium traces across the islet.

In this paper Briggs et al set out to answer the following areas of debate:

They use computational datasets, based on established models of beta cells acting in concert (electrically coupled) within an islet-like structure, to show that it is similarities in metabolic parameters rather than "structural" connections (ie proximity which subserves gap junction coupling) that drives functional network behaviour. Whilst the computational models are quite relevant, the fact that the parameters (eg connectivity coefficients) are quite different to what is measured experimentally, confirm the limitations of this model. Therefore it was important for the authors to back up this finding by performing both calcium and metabolic imaging of islet beta cells. These experimental data are reported to confirm that metabolic coupling was more strongly related to functional connectivity than gap junction coupling. However, a limitation here is that the metabolic imaging data confirmed a strong link between disconnected beta cells and low metabolic coupling but did not robustly show the opposite. Similarly, I was not convinced that the FRAP studies, which indirectly measured GJ ("structural") connections were powered well enough to be related to measures of beta cell connectivity.

The group goes on to provide further analytical and experimental data with a model of increasing loss of GJ connectivity (by calcium imaging islets from WT, heterozygous (50% GJ loss), and homozygous (100% loss). Given the former conclusion that it was metabolic not GJ connectivity that drives small world network behaviour, it was surprising to see such a great effect on the loss of hubs in the homs. That said, the analytical approaches in this model did help the authors confirm that the loss of gap junctions does not alter the preferential existence of beta cell connectivity and confirms the important contribution of metabolic "coupling". One perhaps can therefore conclude that there are two types of network behaviour in an islet (maybe more) and the field should move towards an understanding of overlapping network communities as has been done in brain networks.

Overall this is an extremely well-written paper which was a pleasure to read. This group has neatly and expertly provided both computational and experimental data to support the notion that it is metabolic but not "structural" ie GJ coupling that drives our observations of hubs and functional connectivity. However, there is still much work to do to understand whether this metabolic coupling is just a random epiphenomenon or somehow fated, the extent to which other elements of "structural" coupling - ie the presence of other endocrine cell types, the spatial distribution of paracrine hormone receptors, blood vessels and nerve terminals are also important.

We thank reviewer 3 for their positive comments, including the methodology, writing style, and the importance of this paper to the broader islet community. We thank the reviewer for their very in-depth and helpful comments. We have addressed each comment below and made significant changes to the manuscript according. We conducted more FRAP experiments and separated results into slow, fast, and mixed oscillations. We included analysis of an additional computational model that simulates slow calcium oscillations. Additionally, we substantially rewrote the paper to clarify that we are not referring to metabolic coupling and speak on the broader implications of network theory and our findings.

Reviewer #4 (Public Review):

This manuscript describes a complex, highly ambitious set of modeling and experimental studies that appear designed to compare the structural and functional properties of beta cell subpopulations within the islet network in terms of their influence on network synchronization. The authors conclude that the most functionally coupled cell subpopulations in the islet network are not those that are most structurally coupled via gap junctions but those that are most metabolically active.

Strengths of the paper include (1) its use of an interdisciplinary collection of methods including computer simulations, FRAP to monitor functional coupling by gap junctions, the monitoring of Ca2+ oscillations in single beta cells embedded in the network, and the use of sophisticated approaches from probability theory. Most of these methods have been used and validated previously. Unfortunately, however, it was not clear what the underlying premise of the paper actually is, despite many stated intentions, nor what about it is new compared to previous studies, an additional weakness.

Although the authors state that they are trying to answer 3 critical questions, it was not clear how important these questions are in terms of significance for the field. For example, they state that a major controversy in the field is whether network structure or network function mediates functional synchronization of beta cells within the islet. However, this question is not much debated. As an example, while it is known that there can be long-range functional coupling in islets, no workers in the field believe there is a physical structure within islets that mediates this, unlike the case for CNS neurons that are known to have long projections onto other neurons. Beta cells within the islets are locally coupled via gap junctions, as stated repeatedly by the authors but these mediate short-range coupling. Thus, there are clearly functional correlations over long ranges but no structures, only correlated activity. This weakness raises questions about the overall significance of the work, especially as it seems to reiterate ideas presented previously.

We thank reviewer 4 for their positive comments, including our multidisciplinary use of mathematical models and experimental imaging techniques. We have now included an additional model of slow oscillations (the Integrated Oscillator Model) to improve our conclusions. We also thank reviewer 4 for the insightful comments. We have carefully reviewed each comment and made significant changes to the manuscript accordingly. In particular, we have significantly rewritten the introduction and discussion attempting to clarify what is new in our manuscript and what is previously shown. Additionally, we agree with the reviewers’ sentiment that there is little debate over whether, for example, there are physical structures within the islet that mediate long-range functional connections. However, there is current debate over whether functional beta-cell subpopulations can dictate islet dynamics (see [11]–[13]). This debate can be framed by observing whether these functional subpopulations emerge from the islet due to physical connections (structural network) or something more nuisance (such as intrinsic dynamics). We have reframed the introduction and discussion to clarify this debate as well as more clearly state the premise of the paper.

Specific Comments

1). The authors state it is well accepted that the disruption of gap junctional coupling is a pathophysiological characteristic of diabetes, but this is not an opinion widely accepted by the field, although it has been proposed. The authors should scale back on such generalizations, or provide more compelling evidence to support such a claim.

Thank you for pointing this out, we have provided more specific citations and changes the wording from “well accepted” to “has been documented”. See Discussion page 13 lines 415-416.

2) The paper relies heavily on simulations performed using a version of the model of Cha et al (2011). While this is a reasonable model of fast bursting (e.g. oscillations having periods <1 min.), the Ca2+ oscillations that were recorded by the authors and shown in Fig. 2b of the manuscript are slow oscillations with periods of 5 min and not <1 min, which is a weakness of the model in the current context. Furthermore, the model outputs that are shown lack the well-known characteristics seen in real islets, such as fast-spiking occurring on prolonged plateaus, again as can be seen by comparing the simulated oscillations shown in Fig. 1d with those in Fig. 2b. It is recommended that the simulations be repeated using a more appropriate model of slow oscillations or at least using the model of Cha et al but employed to simulate in slower bursting.

The reviewer raises an important point and caveat associated with our simulated model and experimental data. This point was also made by other reviewers, and a similar response to this comment can be found elsewhere in response to reviewer 2 point 6. To address this comment, we have performed several additional experiments and analyses:

1) We collected additional Ca2+ (to identify the functional network and hubs) and FRAP data (to assess gap junction permeability) in islets which show either pure slow, pure fast, or mixed oscillations. We generated networks based on each time scale to compare with FRAP gap junction permeability data. We found that the conclusions of our first draft to be consistent across all oscillation types. There was no relationship between gap junction conductance, as approximated using FRAP, and normalized degree for slow (Figure 3j), fast (Figure 3 Supp 1d,e), or mixed (Figure 3 Supp 1g,h) oscillations. We also include discussion of these conclusions - See Results page 7 lines 184-186 and lines 188-191, Discussion page 12 lines 357-360.

2) We also performed additional simulations with a coupled ‘Integrated Oscillator Model’ which shows slow oscillations because of metabolic oscillations (Figure 2). We compared connectivity with gap junction coupling and underlying cell parameters. In this case, there is an association between functional and structural networks, with highly-connected hub cells showing higher gap junction conductance (Figure 2f) but also low KATP channel conductance (gKATP) (Figure 2e). However, there are some caveats to these findings – given the nature of the IOM model, we were limited to simulating smaller islets (260 cells) and less heterogeneity in the calcium traces was observed. Additional analysis suggests the greater association between functional and structural networks in this model was a result of the smaller islets, and the association was also dependent on threshold (unlike in the Cha-Noma fast oscillator model) robust. These limitations and results are discussed further (Discussion page 11 lines 344-354).

Additionally, in the IOM, the underlying cell dynamics of highly-connected hub cells are differentiated by KATP channel conductance (gKATP), which is different than in the fast oscillator model (differentiated by metabolism, kglyc). However this difference between models can be linked to differences in the way duty cycle is influenced by gKATP and kglyc (Figure 1h, Figure 2g). In each model there was a similar association between duty cycle and highly-connected hub cells. We also discuss these findings (Discussion page 11 lines 334-343).

Overall these results and discussion with respect to the coupled IOM oscillator model can be found in Figure 2, Results page 6 lines 128-156 and Discussion page 11 lines 332-354.

3) Much of the data analyzed whether obtained via simulation or through experiment seems to produce very small differences in the actual numbers obtained, as can be seen in the bar graphs shown in Figs. 1e,g for example (obtained from simulations), or Fig. 2j (obtained from experimental measurements). The authors should comment as to why such small differences are often seen as a result of their analyses throughout the manuscript and why also in many cases the observed variance is high. Related to the data shown, very few dots are shown in Figs. 1eg or Fig 4e and 4h even though these points were derived from simulations where 100s of runs could be carried out and many more points obtained for plotting. These are weaknesses unless specific and convincing explanations are provided.

We thank the reviewer for these comments, which are similar to those of reviewer 2 (point 4) and reviewer 3 (point 6). Indeed there is some variability between cells in both simulations and experiments related to the metabolic activity in hubs and non-hubs. The variability points to potentially other factors being involved in determining hubs beyond simply kglyc, including a minor role for gap junction coupling structural network and potentially cell position and other intrinsic factors. We now discuss this point – see Discussion page 12 lines 364-266.

The differences between hubs and nonhubs appear small because the value of kglyc is very small. For figure 1e, the average kglyc for nonhubs was 1.26x10-4 s-1 (which is the average of the distribution because most cells are non hubs) while the average kglyc for hubs was 1.4x10-4 s-1 which is about half of a standard deviation higher. The paired t-test controls for the small value of average kglyc.

For simulation data each of the 5 dots corresponds to a simulated islet averaged over 1000 cells (or 260 cells for coupled IOM). The computational resources are high to generate such data so it is not feasible to conduct 100s of runs. Again, we note the comparisons between hubs and non-hubs are paired, and we find statistically significant differences for kglyc in figure 1 using only 5 paired data points. That we find these differences indicates the substantial difference between hubs and non-hubs. This is further supported all effect sizes being much greater than 0.8 for all significantly different findings (Cha Noma - kglyc: 2.85, gcoup: 0.82) (IOM: gKATP: 1.27, gcoup: 2.94) – We have included these effect sizes in the captions see Figure 1 and 2 captions (pages 34, 36)

To consider all of the available data rather than the average across an entire islet, we created a kernel density estimate the kglyc for hubs and nonhubs created by concatenating every single cell in each of the five islets. A kstest results in a highly significant difference (P<0.0001) between these two distributions.

Author response image 1.

4) The data shown in Fig. 4i,j are intended to compare long-range synchronization at different distances along a string of coupled cells but the difference between the synchronized and unsynchronized cells for gcoup and Kglyc was subtle, very much so.

Thank you for pointing out these subtle differences. The y-axis scale for i and j is broad to allow us to represent all distances on a single plot. After correction for multiple comparison, the differences were still statistically significant. As the reviewer mentioned in point 3, each plot contains only five data points, each of which represent the average of a single simulated islet, therefore we are not concerned about statistical significance coming from too large of a sample size. We also checked the differences between synchronized and nonsynchronized cell pairs in figure 4 panels e and h (now figure 5 e, h). These are the same data as i and j but normalized such that all of the distances could be averaged together. We again found statistical significance between synchronized and non-synchronized cell pairs. As can be seen in Author response image 2 the difference between synchronized and non-synchronized cell pairs is greater than the variability between simulated islets. Thus, in this case the variability is not substantial.

Author response image 2.

5) The data shown in Fig. 5 for Cx36 knockout islets are used to assess the influence of gap junctional coupling, which is reasonable, but it would be reassuring to know that loss of this gene has no effects on the expression of other genes in the beta cell, especially genes involved with glucose metabolism.

This is an important point. Previous studies have assessed that no significant change in NAD(P)H is observed in Cx36 deficient islets – see Benninger et al J.Physiol 2011 [14]. Islet architecture is also retained. Further the insulin secretory response of dissociated Cx36 knockout beta cells is the same as that of dissociated wildtype beta cells, further indicating no significant defect in the intrinsic ability of the beta cell to release insulin – see Benninger et al J.Physiol 2011 [14]. We now Mention these findings in the discussion. See Discussion page 14 lines 459-464.

6) In many places throughout the paper, it is difficult to ascertain whether what is being shown is new vs. what has been shown previously in other studies. The paper would thus benefit strongly from added text highlighting the novelty here and not just restating what is known, for instance, that islets can exhibit small-world network properties. This detracts from the strengths of the paper and further makes it difficult to wade through. Even the finding here that metabolic characteristics of the beta cells can infer profound and influential functional coupling is not new, as the authors proposed as much many years ago. Again, this makes it difficult to distill what is new compared to what is mainly just being confirmed here, albeit using different methods.

Thank you for the suggestion, we have made significant modifications throughout the Introduction, Discussion and Results to be clearer about what is known from previous work and what is newly found in this manuscript.

Reviewer #5 (Public Review):

The authors use state-of-the-art computation, experiment, and current network analysis to try and disaggregate the impact of cellular metabolism driving cellular excitability and structural electrical connections through gap junctions on islet synchronization. They perform interesting simulations with a sophisticated mathematical model and compare them with closely associated experiments. This close association is impressive and is an excellent example of using mathematics to inform experiments and experimental results. The current conclusions, however, appear beyond the results presented. The use of functional connectivity is based on correlated calcium traces but is largely without an understood biophysical mechanism. This work aims to clarify such a mechanism between metabolism and structural connection and comes out on the side of metabolism driving the functional connectivity, but both are required and more nuanced conclusions should be drawn.

We thank reviewer 5 for their positive comments, including our multifaceted experimental and computational techniques. We also found the reviewers careful reading and thoughtful comments to be very helpful and we have worked to integrate each comment into our manuscript. It is evident from the reviewer comments that we did not clearly explain what was meant by our conclusions concerning the functional network reflecting metabolism rather than gap junctions. We have conducted significant rewriting to show that we are not concluding that communication (metabolic or electric) occurs due to conduits other than gap junctions. Rather, our data suggest that the functional network (which reflects calcium synchronization) reflects intrinsic dynamics of the cells, which include metabolic rates, more than individual gap junction connections.

References referred to in this response to reviewers document:

[1] A. Stožer et al., “Functional connectivity in islets of Langerhans from mouse pancreas tissue slices,” PLoS Comput Biol, vol. 9, no. 2, p. e1002923, 2013.

[2] N. L. Farnsworth, A. Hemmati, M. Pozzoli, and R. K. Benninger, “Fluorescence recovery after photobleaching reveals regulation and distribution of connexin36 gap junction coupling within mouse islets of Langerhans,” The Journal of physiology, vol. 592, no. 20, pp. 4431–4446, 2014.

[3] C.-L. Lei, J. A. Kellard, M. Hara, J. D. Johnson, B. Rodriguez, and L. J. Briant, “Beta-cell hubs maintain Ca2+ oscillations in human and mouse islet simulations,” Islets, vol. 10, no. 4, pp. 151–167, 2018.

[4] N. R. Johnston et al., “Beta cell hubs dictate pancreatic islet responses to glucose,” Cell metabolism, vol. 24, no. 3, pp. 389–401, 2016.

[5] V. Kravets et al., “Functional architecture of pancreatic islets identifies a population of first responder cells that drive the first-phase calcium response,” PLoS Biology, vol. 20, no. 9, p. e3001761, 2022.

[6] H. Ren et al., “Pancreatic α and β cells are globally phase-locked,” Nature Communications, vol. 13, no. 1, p. 3721, 2022.

[7] A. Stožer et al., “From Isles of Königsberg to Islets of Langerhans: Examining the function of the endocrine pancreas through network science,” Frontiers in Endocrinology, vol. 13, p. 922640, 2022.

[8] J. Zmazek et al., “Assessing different temporal scales of calcium dynamics in networks of beta cell populations,” Frontiers in physiology, vol. 12, p. 337, 2021.

[9] M. E. Corezola do Amaral et al., “Caloric restriction recovers impaired β-cell-β-cell gap junction coupling, calcium oscillation coordination, and insulin secretion in prediabetic mice,” American Journal of Physiology-Endocrinology and Metabolism, vol. 319, no. 4, pp. E709–E720, 2020.

[10] J. M. Dwulet, J. K. Briggs, and R. K. P. Benninger, “Small subpopulations of beta-cells do not drive islet oscillatory [Ca2+] dynamics via gap junction communication,” PLOS Computational Biology, vol. 17, no. 5, p. e1008948, May 2021, doi: 10.1371/journal.pcbi.1008948.

[11] B. E. Peercy and A. S. Sherman, “Do oscillations in pancreatic islets require pacemaker cells?,” Journal of Biosciences, vol. 47, no. 1, pp. 1–11, 2022.

[12] G. A. Rutter, N. Ninov, V. Salem, and D. J. Hodson, “Comment on Satin et al.‘Take me to your leader’: an electrophysiological appraisal of the role of hub cells in pancreatic islets. Diabetes 2020; 69: 830–836,” Diabetes, vol. 69, no. 9, pp. e10–e11, 2020.

[13] L. S. Satin and P. Rorsman, “Response to comment on satin et al.‘Take me to your leader’: An electrophysiological appraisal of the role of hub cells in pancreatic islets. Diabetes 2020; 69: 830–836,” Diabetes, vol. 69, no. 9, pp. e12–e13, 2020.

[14] R. K. Benninger, W. S. Head, M. Zhang, L. S. Satin, and D. W. Piston, “Gap junctions and other mechanisms of cell–cell communication regulate basal insulin secretion in the pancreatic islet,” The Journal of physiology, vol. 589, no. 22, pp. 5453–5466, 2011.

[15] R. Fried, Erectile dysfunction as a cardiovascular impairment. Academic Press, 2014. [16] T. Pipatpolkai, S. Usher, P. J. Stansfeld, and F. M. Ashcroft, “New insights into KATP channel gene mutations and neonatal diabetes mellitus,” Nature Reviews Endocrinology, vol. 16, no. 7, pp. 378–393, 2020.

[17] A. M. Notary, M. J. Westacott, T. H. Hraha, M. Pozzoli, and R. K. P. Benninger, “Decreases in Gap Junction Coupling Recovers Ca2+ and Insulin Secretion in Neonatal Diabetes Mellitus, Dependent on Beta Cell Heterogeneity and Noise,” PLOS Computational Biology, vol. 12, no. 9, p. e1005116, Sep. 2016, doi: 10.1371/journal.pcbi.1005116.

[18] J. V. Rocheleau, G. M. Walker, W. S. Head, O. P. McGuinness, and D. W. Piston, “Microfluidic glucose stimulation reveals limited coordination of intracellular Ca2+ activity oscillations in pancreatic islets,” Pro ceedings of the National Academy of Sciences, vol. 101, no. 35, pp. 12899–12903, 2004. [19] R. K. Benninger, M. Zhang, W. S. Head, L. S. Satin, and D. W. Piston, “Gap junction coupling and calcium waves in the pancreatic islet,” Biophysical journal, vol. 95, no. 11, pp. 5048–5061, 2008.

Author Response

Reviewer #1 (Public Review):

This paper presents an interesting data set from historic Western Eurasia and North Africa. Overall, I commend the authors for presenting a comprehensive paper that focuses the data analysis of a large project on the major points, and that is easy to follow and well-written. Thus, I have no major comments on how the data was generated, or is presented. Paradoxically, historical periods are undersampled for ancient DNA, and so I think this data will be useful. The presentation is clever in that it focuses on a few interesting cases that highlight the breadth of the data.

The analysis is likewise innovative, with a focus on detecting "outliers" that are atypical for the genetic context where they were found. This is mainly achieved by using PCA and qpAdm, established tools, in a novel way. Here I do have some concerns about technical aspects, where I think some additional work could greatly strengthen the major claims made, and lay out if and how the analysis framework presented here could be applied in other work.

clustering analysis

I have trouble following what exactly is going on here (particularly since the cited Fernandes et al. paper is also very ambiguous about what exactly is done, and doesn't provide a validation of this method). My understanding is the following: the goal is to test whether a pair of individuals (lets call them I1 and I2) are indistinguishable from each other, when we compare them to a set of reference populations. Formally, this is done by testing whether all statistics of the form F4(Ref_i, Ref_j; I1, I2) = 0, i.e. the difference between I1 and I2 is orthogonal to the space of reference populations, or that you test whether I1 and I2 project to the same point in the space of reference populations (which should be a subset of the PCA-space). Is this true? If so, I think it could be very helpful if you added a technical description of what precisely is done, and some validation on how well this framework works.

We agree that the previous description of our workflow was lacking, and have substantially improved the description of the entire pipeline (Methods, section “Modeling ancestry and identifying outliers using qpAdm”), making it clearer and more descriptive. To further improve clarity, we have also unified our use of methodology and replaced all mentions of “qpWave” with “qpAdm”. In the reworked Methods section mentioned above, we added a discussion on how these tests are equivalent in certain settings, and describe which test we are exactly doing for our pairwise individual comparisons, as well as for all other qpAdm tests downstream of cluster discovery. In addition, we now include an additional appendix document (Appendix 4) which, for each region, shows the results from our individual-based qpAdm analysis and clustering in the form of heatmaps, in addition to showing the clusters projected into PC space.

An independent concern is the transformation from p-values to distances. I am in particular worried about i) biases due to potentially different numbers of SNPs in different samples and ii) whether the resulting matrix is actually a sensible distance matrix (e.g. additive and satisfies the triangle inequality). To me, a summary that doesn't depend on data quality, like the F2-distance in the reference space (i.e. the sum of all F4-statistics, or an orthogonalized version thereof) would be easier to interpret. At the very least, it would be nice to show some intermediate results of this clustering step on at least a subset of the data, so that the reader can verify that the qpWave-statistics and their resulting p-values make sense.

We agree that calling the matrix generated from p-values a “distance matrix” is a misnomer, as it does not satisfy the triangle inequality, for example. We still believe that our clustering generates sensible results, as UPGMA simply allows us to project a positive, symmetric matrix to a tree, which we can then use, given some cut-off, to define clusters. To make this distinction clear, we now refer to the resulting matrix as a “dissimilarity matrix” instead. As mentioned above, we now also include a supplementary figure for each region visualizing the clustering results.

Regarding the concerns about p-values conflating both signal and power, we employ a stringent minimum SNP coverage filter for these analyses to avoid extremely-low coverage samples being separated out (min. SNPs covered: 100,000). In addition, we now show that cluster size and downstream outlier status do not depend on SNP coverage (Figure 2 - Suppl. 3).

The methodological concerns lead me to some questions about the data analysis. For example, in Fig2, Supp 2, very commonly outliers lie right on top of a projected cluster. To my understanding, apart from using a different reference set, the approach using qpWave is equivalent to using a PCA-based clustering and so I would expect very high concordance between the approaches. One possibility could be that the differences are only visible on higher PCs, but since that data is not displayed, the reader is left wondering. I think it would be very helpful to present a more detailed analysis for some of these "surprising" clustering where the PCA disagrees with the clustering so that suspicions that e.g. low-coverage samples might be separated out more often could be laid to rest.

To reduce the risk of artifactual clusters resulting from our pipeline, we devised a set of QC metrics (described in detail below) on the individuals and clusters we identified as outliers. Driven by these metrics, we implemented some changes to our outlier detection pipeline that we now describe in substantially more detail in the Methods (see comment above). Since the pipeline involves running many thousands of qpAdm analyses, it is difficult to manually check every step for all samples – instead, we focused our QC efforts on the outliers identified at the end of the pipeline. To assess outlier quality we used the following metrics, in addition to manual inspection:

First, for an individual identified as an outlier at the end of the pipeline, we check its fraction of non-rejected hypotheses across all comparisons within a region. The rationale here is that by definition, an outlier shouldn’t cluster with many other samples within its region, so a majority of hypotheses should be rejected (corresponding to gray and yellow regions in the heatmaps, Appendix 4). Through our improvements to the pipeline, the fraction of non-rejected hypotheses was reduced from an average of 5.3% (median 1.1%) to an average of 3.8% (median 0.6%), while going from 107 to 111 outliers across all regions.

Second, we wanted to make sure that outlier status was not affected by the inclusion of pre-historic individuals in our clustering step within regions. To represent majority ancestries that might have been present in a region in the past, we included Bronze and Copper Age individuals in the clustering analysis. We found that including these individuals in the pairwise analysis and clustering improved the clusters overall. However, to ensure that their inclusion did not bias the downstream identification of outliers, we also recalculated the clustering without these individuals. We inspected whether an individual identified as an outlier would be part of a majority cluster in the absence of Bronze and Copper Age individuals, which was not the case (see also the updated Methods section for more details on how we handle time periods within regions).

In response to the “surprising” outliers based on the PCA visualizations in Figure 2, Supplement 2: with our updated outlier pipeline, some of these have disappeared, for example in Western and Northern Europe. However, in some regions the phenomenon remains. We are confident this isn’t a coverage effect, as we’ve compared the coverage between outliers and non-outliers across all clusters (see previous comment, Figure 2 - Suppl. 3), as well as specifically for “surprising” outliers compared to contemporary non-outliers – none of which showed any differences in the coverage distributions of “surprising” outliers (Author response images 1 and 2). In addition, we believe that the quality metrics we outline above were helpful in minimizing artifactual associations of samples with clusters, which could influence their downstream outlier status. As such, we think it is likely that the qpAdm analysis does detect a real difference between these sets of samples, even though they project close to each other in PCA space. This could be the result of an actual biological difference hidden from PCA by the differences in reference space (see also the reply to the following comment). Still, we cannot fully rule out the possibility of latent technical biases that we were not able to account for, so we do not claim the outlier pipeline is fully devoid of false positives. Nevertheless, we believe our pipeline is helpful in uncovering true, recent, long-range dispersers in a high-throughput and automated manner, which is necessary to glean this type of insight from hundreds of samples across a dozen different regions.

Author response image 1.

SNP coverage comparison between outliers and non-outliers in region-period pairings with “surprising” outliers (t-test p-value: 0.242).

Author response image 2.

PCA projection (left) and SNP coverage comparison (right) for “surprising” outliers and surrounding non-outliers in Italy_IRLA.

One way the presentation could be improved would be to be more consistent in what a suitable reference data set is. The PCAs (Fig2, S1 and S2, and Fig6) argue that it makes most sense to present ancient data relative to present-day genetic variation, but the qpWave and qpAdm analysis compare the historic data to that of older populations. Granted, this is a common issue with ancient DNA papers, but the advantage of using a consistent reference data set is that the analyses become directly comparable, and the reader wouldn't have to wonder whether any discrepancies in the two ways of presenting the data are just due to the reference set.

While it is true that some of the discrepancies are difficult to interpret, we believe that both views of the data are valuable and provide complementary insights. We considered three aspects in our decision to use both reference spaces: (1) conventions in the field (including making the results accessible to others), (2) interpretability, and (3) technical rigor.

Projecting historical genomes into the present-day PCA space allows for a convenient visualization that is common in the field of ancient DNA and exhibits an established connection to geographic space that is easy to interpret. This is true especially for more recent ancient and historical genomes, as spatial population structure approaches that of present day. However, there are two challenges: (1) a two-dimensional representation of a fairly high-dimensional ancestry space necessarily incurs some amount of information loss and (2) we know that some axes of genetic variation are not well-represented by the present-day PCA space. This is evident, for example, by projecting our qpAdm reference populations into the present-day PCA, where some ancestries which we know to be quite differentiated project closely together (Author response image 3). Despite this limitation, we continue to use the PCA representation as it is well resolved for visualization and maximizes geographical correspondence across Eurasia.

On the other hand, the qpAdm reference space (used in clustering and outlier detection) has higher resolution to distinguish ancestries by more comprehensively capturing the fairly high-dimensional space of different ancestries. This includes many ancestries that are not well resolved in the present-day PCA space, yet are relevant to our sample set, for example distinguishing Iranian Neolithic ancestry against ancestries from further into central and east Asia, as well as distinguishing between North African and Middle Eastern ancestries (Author response image 3).

To investigate the differences between these two reference spaces, we chose pairwise outgroup-f3 statistics (to Mbuti) as a pairwise similarity metric representing the reference space of f-statistics and qpAdm in a way that’s minimally affected by population-specific drift. We related this similarity measure to the euclidean distance on the first two PCs between the same set of populations (Author response image 4). This analysis shows that while there is almost a linear correspondence between these pairwise measures for some populations, others comparisons fall off the diagonal in a manner consistent with PCA projection (Author response image 3), where samples are close together in PCA but not very similar according to outgroup-f3. Taken together, these analyses highlight the non-equivalence of the two reference spaces.

In addition, we chose to base our analysis pipeline on the f-statistics framework to (1) afford us a more principled framework to disentangle ancestries among samples and clusters within and across regions (using 1-component vs. 2-component models of admixture), while (2) keeping a consistent, representative reference set for all analyses that were part of the primary pipeline. Meanwhile, we still use the present-day PCA space for interpretable visualization.

Author response image 3.

Projection of qpAdm reference population individuals into present-day PCA.

Author response image 4.

Comparison of pairwise PCA projection distance to outgroup-f3 similarity across all qpAdm reference population individuals. PCA projection distance was calculated as the euclidean distance on the first two principal components. Outgroup-f3 statistics were calculated relative to Mbuti, which is itself also a qpAdm reference population. Both panels show the same data, but each point is colored by either of the two reference populations involved in the pairwise comparison.

PCA over time

It is a very interesting observation that the Fst-vs distance curve does not appear to change after the bronze age. However, I wonder if the comparison of the PCA to the projection could be solidified. In particular, it is not obvious to me how to compare Fig 6 B and C, since the data in C is projected onto that in Fig B, and so we are viewing the historic samples in the context of the present-day ones. Thus, to me, this suggests that ancient samples are most closely related to the folks that contribute to present-day people that roughly live in the same geographic location, at least for the middle east, north Africa and the Baltics, the three regions where the projections are well resolved. Ideally, it would be nice to have independent PCAs (something F-stats based, or using probabilistic PCA or some other framework that allows for missingness). Alternatively, it could be helpful to quantify the similarity and projection error.

The fact that historical period individuals are “most closely related to the folks that contribute to present-day people that roughly live in the same geographic location” is exactly the point we were hoping to make with Figures 6 B and C. We do realize, however, that the fact that one set of samples is projected into the PC space established by the other may suggest that this is an obvious result. To make it more clear that it is not, we added an additional panel to Figure 6, which shows pre-historical samples projected into the present-day PC space. This figure shows that pre-historical individuals project all across the PCA space and often outside of present-day diversity, with degraded correlation of geographic location and projection location (see also Author response image 5). This illustrates the contrast we were hoping to communicate, where projection locations of historical individuals start to “settle” close to present-day individuals from similar geographic locations, especially in contrast with pre-historic individuals.

Author response image 5.

Comparing geographic distance to PCA distance between pairs of historical and pre-historical individuals matched by geographic space. For each historical period individual we selected the closest pre-historical individual by geographic distance in an effort to match the distributions of pairwise geographic distance across the two time periods (left). For these distributions of individuals matched by geographic distance, we then queried the euclidean distance between their projection locations in the first two principal components (right).

Author Response

Reviewer #3 (Public Review):

The authors explore the use of SRT as a host-directed therapy for use in combination with other first-line TB antibiotics. This manuscript is of substantial importance since TB is a major world health concern, and there is growing interest in the development of host-directed therapies to augment existing therapies for TB. Demonstrating the effectiveness of adding an FDA-approved drug to existing cocktails of anti-TB drugs has potentially exciting implications.

The manuscript is bolstered by their use of multiple in vitro and in vivo models of infection, as well as a clinically relevant strain of TB. While their findings generally support the use of SRT as an effective HDT/treatment, the mechanistic details underlying the effectiveness of SRT remain somewhat obscure, and as presented, the in vitro experiments support more limited conclusions.

Major concerns:

In vitro studies (i.e. bacterial culture) were only performed with SRT up to 6 uM while the cultured cell experiments used a range up to 20 uM. 5 uM had almost no effect on the viability/growth of Mtb in macrophages. The authors should use the same concentrations in vitro as their macrophage studies to test whether SRT directly impacts Mtb viability to be able to rule in/out that SRT does not impact Mtb viability when cultured.

We haven’t seen any appreciable decrease in the growth of Mtb at upto 20M in in vitro experiments, nearly 30-40% restriction after 8 days of culture. We used in combination of HR a lower dose of 6mM in combination with HR to offset the effect of minimal SRT inhibitory effects so that only the effect of SRT is understood.

The mechanism of action of SRT during TB infection and the conclusions drawn by the authors are not supported by the limited experimentation. SRT is presented as an antagonist of polyI:C-induced type I IFNs, but during TB infection, cytosolic DNA sensing via the cGAS/STING axis constitutes the major pathway through which type I IFNs are induced in macrophages.

To offer more support that SRT inhibits type I IFN, the authors should consider measuring the the actual amount of type I IFN using an IFNb ELISA. Additionally, the authors should use human/mouse primary macrophages (not just THP1 reporter cells) and measure transcript levels (at key time points post infection) and protein levels of type I IFN and other proinflammatory mediators (e.g. TNFa, IL-1, IL-6) +/- SRT to determine if SRT is specific to the type I IFN response. If this is indeed the case, other NFkB genes/cytokines should not be impacted.

Moreover, to draw the conclusion that "augmentation property of SRT is due to its ability to inhibit IFN signalling" a set of experiments using an IFN blocking antibody would enhance Figure 2, as both cGAS and STING KO macs have significant differences in basal gene expression and their ability to respond to innate immune stimuli.

Because the first half of the paper focuses on type I IFNs during macrophage infection to explain the mechanism of action for SRT, additional analysis of the mouse infections to examine levels of type I IFNs, as well as IL-1B and IFN-g (in serum/tissues?), is important for connecting the two halves of the manuscript. The in vivo data would also be strengthened by quantitative analysis of histological changes by, for example, blinded pathology scoring. This type of quantitation would also permit statistical analyses of this important pathology readout.

We have performed analyse of tissue cytokine levels and did not see stark differences in the levels between HRZE and HRZES at two time points of 4 and 8weeks post treatment (Figure below). We feel that such studies would need a more comprehensive analyses of the immunological response induced in the host by the treatment at multiple time points. Such studies would be part of a more focussed plan in the future proposals and manuscripts. We have also conducted a manual scoring of the lesions between the groups and have recorded this data in the manuscript (Fig.4-figure supplement 1)

The authors conclude that SRT functions through an inflammasome-related function, but this conclusion requires further support of actual inflammasome activation, such as IL-1B secretion by ELISA or IL-1B processing by western blot analysis, rather than Il1b gene expression alone. Additional functional readouts of inflammasome activation like cell death assays would also strengthen this conclusion.

We thank the reviewer for these suggestions. These studies are currently underway and will be part of a future manuscript detailing the mechanistics of SRT mediated increase in antibiotic efficacy.

What strain of TB was used in these studies? The results and methods do not indicate the strain used, which is critical to know since different strains have varying pathogenesis phenotypes.

We have used Mtb Erdman for routine drug sensitive and N73 for the drug tolerant studies. This has been added in the text.

Minor concerns:

It might be worth consistently using the more common INH and RIF abbreviations to increase the clarity/readability of the MS and figures.

We have used the conventional clinical abbreviations used for INH and Rifampicin What is the physiological concentration of SRT when taken for depression and how does that compare to the concentrations used in vitro? Are the in vitro concentrations feasible to achieve in patients?

In Figure 3B, why is there a spike in TNF-a in the HRS treated cells only at 42h?

The authors wish to thank the reviewer for this query. We have reanalysed the data and have depicted the modified figures in the current text version. The spike at 42H for TNF was an oversight and due to an erroneous representation of the values in the figure.

Was statistical analysis performed on the data in Figure 3B and D?

Yes, we have incorporated this information in the modified figure.

A description/discussion of the different mouse strains use in infection - what benefits each has as a model and why several were used - would help convey the impact of the in vivo studies.

These have been incorporated in the text. A discussion of the mouse strains and their immunopathology in infection has been included in the text.

Since antibiotics and SRT were administered ad libitum, how did the authors ensure that mice took enough of the antibiotics and especially SRT? Is it known whether these drugs affect the water taste enough to affect a mouse's willingness to drink them?

We preferred the use of ad libitum delivery of TB drugs in drinking water as used in the previous studies by Vilchèze et .al, 2018 Antimicrob Agents Chemother 23;62(3):e02165-17. To avoid non drinking, we used 5% glucose in the water of all animals including the non-antibiotic treated groups. We also followed the uptake of water during the treatment and found comparable levels of usage between the groups.

Was statistical analysis performed on time-to-death experiments?

Because of the inherent differences in the susceptibility and response between males and females C3HEBFEJ mice, we did not perform statistical analyses between the groups.

Were CFUs measured in mice from Figure 4 to determine empirically how effective the antibiotic treatments were? And if SRT impacted their effectiveness?

We have not tested the effect of SRT on bacterial burdens on bacteria treated with HR alone as these studies were aimed at deciphering chronic pathology. We have tested the effect on bacterial loads in the C3HEBFEJ model with the four-drug therapy and the C57BL6 and Balbc models of infection.

The H&E images could use some additional labels to more easily discern what groups they belong to.

These have been incorporated in the figure.

Author Response

Reviewer #1 (Public Review):

This is a carefully-conducted fMRI study looking at how neural representations in the hippocampus, entorhinal cortex, and ventromedial prefrontal cortex change as a function of local and global spatial learning. Collectively, the results from the study provide valuable additional constraints on our understanding of representational change in the medial temporal lobes and spatial learning. The most notable finding is that representational similarity in the hippocampus post-local-learning (but prior to any global navigation trials) predicts the efficiency of subsequent global navigation.

Strengths:

The paper has several strengths. It uses a clever two-phase paradigm that makes it possible to track how participants learn local structure as well as how they piece together global structure based on exposure to local environments. Using this paradigm, the authors show that - after local learning - hippocampal representations of landmarks that appeared within the same local environment show differentiation (i.e., neural similarity is higher for more distant landmarks) but landmarks that appeared in different local environments show the opposite pattern of results (i.e., neural similarity is lower for more distant landmarks); after participants have the opportunity to navigate globally, the latter finding goes away (i.e., neural similarity for landmarks that occurred in different local environments is no longer influenced by the distance between landmarks). Lastly, the authors show that the degree of hippocampal sensitivity to global distance after local-only learning (but before participants have the opportunity to navigate globally) negatively predicts subsequent global navigation efficiency. Taken together, these results meaningfully extend the space of data that can be used to constrain theories of MTL contributions to spatial learning.

We appreciate Dr. Norman’s generous feedback here along with his other insightful comments. Please see below for a point-by-point response. We note that responses to a number of Dr. Norman’s points were surfaced by the Editor as Essential revisions; as such, in a number of instances in the point-by-point below we direct Dr. Norman to our responses above under the Essential revisions section.

Weaknesses:

General comment 1: The study has an exploratory feel, in the sense that - for the most part - the authors do not set forth specific predictions or hypotheses regarding the results they expected to obtain. When hypotheses are listed, they are phrased in a general way (e.g., "We hypothesized that we would find evidence for both integration and differentiation emerging at the same time points across learning, as participants build local and global representations of the virtual environment", and "We hypothesized that there would be a change in EC and hippocampal pattern similarity for items located on the same track vs. items located on different tracks" - this does not specify what the change will be and whether the change is expected to be different for EC vs. hippocampus). I should emphasize that this is not, unto itself, a weakness of the study, and it appears that the authors have corrected for multiple comparisons (encompassing the range of outcomes explored) throughout the paper. However, at times it was unclear what "denominator" was being used for the multiple comparisons corrections (i.e., what was the full space of analysis options that was being corrected for) - it would be helpful if the authors could specify this more concretely, throughout the paper.

We appreciate this guidance and the importance of these points. We have taken a number of steps to clarify our hypotheses, we now distinguish a priori predictions from exploratory analyses, and we now explicitly indicate throughout the manuscript how we corrected for multiple comparisons. For full details, please see above for our response to Essential Revisions General comment #1.

General comment 2: Some of the analyses featured prominently in the paper (e.g., interactions between context and scan in EC) did not pass multiple comparisons correction. I think it's fine to include these results in the paper, but it should be made clear whenever they are mentioned that the results were not significant after multiple comparisons correction (e.g., in the discussion, the authors say "learning restructures representations in the hippocampus and in the EC", but in that sentence, they don't mention that the EC results fail to pass multiple comparisons correction).

Thank you for encouraging greater clarity here. As noted directly above, we now explicitly indicate our a priori predictions, we state explicitly which results survive multiple comparisons correction, and we added necessary caveats for effects that should be interpreted with caution.

General comment 3: The authors describe the "flat" pattern across the distance 2, 3, and 4 conditions in Figure 4c (post-global navigation) and in Figure 5b (in the "more efficient" group) as indicating integration. However, this flat pattern across 2, 3, and 4 (unto itself) could simply indicate that the region is insensitive to location - is there some other evidence that the authors could bring to bear on the claim that this truly reflects integration? Relatedly, in the discussion, the authors say "the data suggest that, prior to Global Navigation, LEs had integrated only the nearest landmarks located on different tracks (link distance 2)" - what is the basis for this claim? Considered on its own, the fact that similarity was high for link distance 2 does not indicate that integration took place. If the authors cannot get more direct evidence for integration, it might be useful for them to hedge a bit more in how they interpret the results (the finding is still very interesting, regardless of its cause).

Based on the outcomes of additional behavioral and neural analyses that were helpfully suggested by reviewers, we revised discussion of this aspect of the data. Please see our response above under Essential Revisions General comment #4 for full details of the changes made to the manuscript.

Reviewer #2 (Public Review):

This paper presents evidence of neural pattern differentiation (using representational similarity analysis) following extensive experience navigating in virtual reality, building up from individual tracks to an overall environment. The question of how neural patterns are reorganized following novel experiences and learning to integrate across them is a timely and interesting one. The task is carefully designed and the analytic setup is well-motivated. The experimental approach provides a characterization of the development of neural representations with learning across time. The behavioral analyses provide helpful insight into the participants' learning. However, there were some aspects of the conceptual setup and the analyses that I found somewhat difficult to follow. It would also be helpful to provide clearer links between specific predictions and theories of hippocampal function.

We appreciate the Reviewer’s careful read of our manuscript and their thoughtful guidance for improvement, which we believe strengthened the revised product. We note that responses to a number of the Reviewer’s points were surfaced by the Editor as Essential revisions; as such, in a number of instances in the point-by-point below we direct the Reviewer to our responses above under the Essential revisions section.

General comment 1: The motivation in the Introduction builds on the assumption that global representations are dependent on local ones. However, I was not completely sure about the specific predictions or assumptions regarding integration vs. differentiation and their time course in the present experimental design. What would pattern similarity consistent with 'early evidence of global map learning' (p. 7) look like? Fig. 1D was somewhat difficult to understand. The 'state space' representation is only shown in Figure 1 while all subsequent analyses are averaged pairwise correlations. It would be helpful to spell out predictions as they relate to the similarity between same-route vs. different-route neural patterns.

We appreciate this feedback. An increase in pattern similarity across features that span tracks would indicate the linking of those features together. ‘Early evidence’ here describes the point in experience where participants had traversed local (within-track) paths but had yet to traverse across-tracks.

Figure 1D seeks to communicate the high-level conceptual point about how similarity (abstractly represented as state-space distance) may change in one of two directions as a function of experience.

General comment 2: The shared landmarks could be used by the participants to infer how the three tracks connected even before they were able to cross between them. It is possible that the more efficient navigators used an explicit encoding strategy to help them build a global map of the world. While I understand the authors' reasoning for excluding the shared landmarks (p. 13), it seems like it could be useful to run an analysis including them as well - one possibility is that they act as 'anchors' and drive the similarity between different tracks early on; another is that they act as 'boundaries' and repel the representations across routes. Assuming that participants crossed over at these landmarks, these seem like particularly salient aspects of the environment.

We agree that these shared landmarks play an important role in learning the global environment and guiding participants’ navigation. However, they also add confounding elements to the analyses; mainly, shared landmarks are located near multiple goal locations and associated with multiple tracks, and transition probabilities differ at shared landmarks because they have an increased number of neighboring landmarks and fractals. In the initial submission, shared landmarks were included in all analyses except (a) global distance models and (b) context models (which compare items located on the same vs different tracks).

With respect to (a) the global distance models, we ran these models while including shared landmarks and the results did not differ (see figure below and compare to Fig. 5 in the revised manuscript):

Distance representations in the Global Environment, with shared landmarks included. These data can be compared to Figure 5 of the revised manuscript, which does not include shared landmarks (see page 5 of this response letter).

We continue to report the results from models excluding shared landmarks due to the confounding factors described above, with the following addition to the Results section:

“We excluded shared landmarks from this model as they are common to multiple tracks; however, the results do not differ if these landmarks are included in the analysis.”

With respect to (b) the context analyses (which compare items located on the same vs different tracks), we cannot include shared landmarks in these analyses because they are common amongst multiple tracks and thus confound the analyses. Finally, we are unable to conduct additional analyses investigating shared landmarks specifically (for example, examining how similarity between shared landmarks evolves across learning) due to very low trial counts. We share the Reviewer’s perspective that the role of shared landmarks during the building of map representations promises to provide additional insights and believe this is a promising question for future investigation.

General comment 3: What were the predictions regarding the fractals vs. landmarks (p. 13)? It makes sense to compare like-to-like, but since both were included in the models it would be helpful to provide predictions regarding their similarity patterns.

We are grateful for the feedback on how to improve the consistency of results reporting. In the revision, we updated the relevant sections of the manuscript to include results from fractals. Please see our above response to Essential Revisions General comment #5 for additions made to the text.

General comment 4: The median split into less-efficient and more-efficient groups does not seem to be anticipated in the Introduction and results in a small-N group comparison. Instead, as the authors have a wealth of within-individual data, it might be helpful to model single-trial navigation data in relation to pairwise similarity values for each given pair of landmarks in a mixed-effects model. While there won't be a simple one-to-one mapping and fMRI data are noisy, this approach would afford higher statistical power due to more within-individual observations and would avoid splitting the sample into small subgroups.

We appreciate this very helpful suggestion. Following this guidance, we removed the median-split analysis and ran a mixed-effects model relating trial-wise navigation data (at the beginning of the Global Navigation Task) to pairwise similarity values for each given pair of landmarks and fractals (Post Local Navigation). We also altered our approach to the across-participant analysis examining brain-behavior relationships. Please see our above response to Essential Revisions General comment #3 for additions to the revised manuscript.

General comment 5: If I understood correctly, comparing Fig. 4B and Fig. 5B suggests that the relationship between higher link distance and lower representational similarity was driven by less efficient navigators. The performance on average improved over time to more or less the same level as within-track (Fig. 2). Were less efficient navigators particularly inefficient on trials with longer distances? In the context of models of hippocampal function, this suggests that good navigators represented all locations as equidistant while poorer navigators showed representations more consistent with a map - locations that were further apart were more distant in their representational patterns. Perhaps more fine-grained analyses linking neural patterns to behavior would be helpful here.

Following the above guidance, we removed the median-split analyses when exploring across-participant brain-behavior relationships (see Essential Revisions General comment #3), replacing it with a mixed-effects model analysis, and we revised our discussion of the across-track link distance effects (see Essential Revisions General comment #4). For this reason, we were hesitant and ultimately decided against conducting the proposed fine-grained analyses on the median-split data.

General comment 6: I'm not completely sure how to interpret the functional connectivity analysis between the vmPFC and the hippocampus vs. visual cortex (Fig. 6). The analysis shows that the hippocampus and visual cortex are generally more connected than the vmPFC and visual cortex - but this relationship does not show an experience-dependent relationship and is consistent with resting-state data where the hippocampus tends to cluster into the posterior DMN network.

We expected to see an experience-dependent relationship between vmPFC and hippocampal pattern similarity, and agree that these findings are difficult to interpret. Based on comments from several reviewers, we removed the second-order similarity analysis from the manuscript in favor of an analysis which models the relationship between vmPFC pattern similarity and hippocampal pattern similarity. Moreover, given the exploratory nature of the vmPFC analyses, and following guidance from Reviewer 1 about the visual cortex control analyses, both were moved to the Appendix. Please see our above response to Essential Revisions General comment #7 for further details of the changes made to the manuscript.

Reviewer #3 (Public Review):

Fernandez et al. report results from a multi-day fMRI experiment in which participants learned to locate fractal stimuli along three oval-shaped tracks. The results suggest the concurrent emergence of a local, differentiated within-track representation and a global, integrated cross-track representation. More specifically, the authors report decreases in pattern similarity for stimuli encountered on the same track in the entorhinal cortex and hippocampus relative to a pre-task baseline scan. Intriguingly, following navigation on the individual tracks, but prior to global navigation requiring track-switching, pattern similarity in the hippocampus correlated with link distances between landmark stimuli. This effect was only observed in participants who navigated less efficiently in the global navigation task and was absent after global navigation.

Overall, the study is of high quality in my view and addresses relevant questions regarding the differentiation and integration of memories and the formation of so-called cognitive maps. The results reported by the authors are interesting and are based upon a well-designed experiment and thorough data analysis using appropriate techniques. A more detailed assessment of strengths and weaknesses can be found below.

Strengths

1) The authors address an interesting question at the intersection of memory differentiation and integration. The study is further relevant for researchers interested in the question of how we form cognitive maps of space.

2) The study is well-designed. In particular, the pre-learning baseline scan and the random-order presentation of stimuli during MR scanning allow the authors to track the emergence of representations in a well-controlled fashion. Further, the authors include an adequate control region and report direct comparisons of their effects against the patterns observed in this control region.

3) The manuscript is well-written. The introduction provides a good overview of the research field and the discussion does a good job of summarizing the findings of the present study and positioning them in the literature.

We thank Dr. Bellmund for his positive evaluation of the manuscript. We greatly appreciate the insightful feedback, which we believe strengthened the manuscript’s clarity and potential impact. We note that responses to a number of Dr. Bellmund’s points were surfaced by the Editor as Essential revisions; as such, in a number of instances in the point-by-point below we direct the Reviewer to our responses above under the Essential revisions section.

Weaknesses

General comment 1: Despite these distinct strengths, the present study also has some weaknesses. On the behavioral level, I am wondering about the use of path inefficiency as a metric for global navigation performance. Because it is quantified based on the local response, it conflates the contributions of local and global errors.

We appreciate this point with respect to path inefficiency during global navigation. As noted below, following Dr. Bellmund’s further insightful guidance, we now complement the path inefficiency analyses with additional metrics of across-track (global) navigation performance, which effectively separate local from global errors (please see below response to Author recommendation #1).

General comment 2: For the distance-based analysis in the hippocampus, the authors choose to only analyze landmark images and do not include fractal stimuli. There seems to be little reason to expect that distances between the fractal stimuli, on which the memory task was based, would be represented differently relative to distances between the landmarks.

We are grateful for the feedback on how to improve the consistency of results reporting. In the revision, we updated the relevant sections of the manuscript to include results from fractals. Please see our above response to Essential Revisions General comment #5 for full details.

General comment 3: Related to the aforementioned analysis, I am wondering why the authors chose the link distance between landmarks as their distance metric for the analysis and why they limit their analysis to pairs of stimuli with distance 1 or 2 and do not include pairs separated by the highest possible distance (3).

We appreciate the request for clarification here. Beginning with the latter question, we note that the highest possible distance varies between within-track vs. across-track paths. If participants navigate in the Local Navigation Task using the shortest or most efficient path, the highest possible within-track link distance between two stimuli is 2. For this reason, the Local Navigation/within-track analysis includes link distances of 1 and 2. For the Global Navigation analysis, we also include pairs of stimuli with link distances of 3 and 4 when examining across-track landmarks.

Regarding the use of link distance as the distance metric, we note that the path distance (a.u.) varies only slightly between pairs of stimuli with the same link distance. As such, categorical treatment link distance accounts for the vast majority of the variance in path distance and thus is a suitable approach. Please note that in the new trial-level brain-behavior analysis included in the revised manuscript (which replaces the median-split analysis), we used the length of the optimal path.

General comment 4: Surprisingly, the authors report that across-track distances can be observed in the hippocampus after local navigation, but that this effect cannot be detected after global, cross-track navigation. Relatedly, the cross-track distance effect was detected only in the half of participants that performed relatively badly in the cross-track navigation task. In the results and discussion, the authors suggest that the effect of cross-track distances cannot be detected because participants formed a "more fully integrated global map". I do not find this a convincing explanation for why the effect the authors are testing would be absent after global navigation and for why the effect was only present in those participants who navigated less efficiently.

We appreciate Dr. Bellmund’s input here, which was shared by other reviewers. We revised and clarified the Discussion based on reviewer comments. Please see our above response to Essential Revisions General comment #4 for full details.

General comment 5: The authors report differences in the hippocampal representational similarity between participants who navigated along inefficient vs. efficient paths. These are based on a median split of the sample, resulting in a comparison of groups including 11 and 10 individuals, respectively. The median split (see e.g. MacCallum et al., Psychological Methods, 2002) and the low sample size mandate cautionary interpretation of the resulting findings about interindividual differences.

We appreciate the feedback we received from multiple reviewers with respect to the median-split brain-behavior analysis. We replaced the median-split analysis with the following: 1) a mixed-effects model predicting neural pattern similarity Post Local Navigation, with a continuous metric of task performance (each participant’s median path inefficiency for across-track trials in the first four test runs of Global Navigation) and link distance as predictors; and 2) a mixed-effects model relating trial-wise navigation data to pairwise similarity values for each given pair of landmarks and fractals (as suggested by Reviewer 2). Please see our above response to Essential Revisions General comment #3 for additions to the revised manuscript.

Author Response

Reviewer #2 (Public Review):

Silberberg et al. present a series of cryo-EM structures of the ATP dependent bacterial potassium importer KdpFABC, a protein that is inhibited by phosphorylation under high environmental K+ conditions. The aim of the study was to sample the protein's conformational landscape under active, non-phosphorylated and inhibited, phosphorylated (Ser162) conditions.

Overall, the study presents 5 structures of phosphorylated wildtype protein (S162-P), 3 structures of phosphorylated 'dead' mutant (D307N, S162-P), and 2 structures of constitutively active, non-phosphorylatable protein (S162A).

The true novelty and strength of this work is that 8 of the presented structures were obtained either under "turnover" or at least 'native' conditions without ATP, ie in the absence of any non-physiological substrate analogues or stabilising inhibitors. The remaining 2 were obtained in the presence of orthovanadate.

Comparing the presented structures with previously published KdpFACB structures, there are 5 structural states that have not been reported before, namely an E1-P·ADP state, an E1-P tight state captured in the autoinhibited WT protein (with and without vanadate), and two different nucleotide-free 'apo' states and an E1·ATP early state.

Of these new states, the 'tight' states are of particular interest, because they appear to be 'off-cycle', dead end states. A novelty lies in the finding that this tight conformation can exist both in nucleotide-free E1 (as seen in the published first KdpFABC crystal structure), and also in the phosphorylated E1-P intermediate.

By EPR spectroscopy, the authors show that the nucleotide free 'tight' state readily converts into an active E1·ATP conformation when provided with nucleotide, leading to the conclusion that the E1-P·ADP state must be the true inhibitory species. This claim is supported by structural analysis supporting the hypothesis that the phosphorylation at Ser162 could stall the KdpB subunit in an E1P state unable to convert into E2P. This is further supported by the fact that the phosphorylated sample does not readily convert into an E2P state when exposed to vanadate, as would otherwise be expected.

The structures are of medium resolution (3.1 - 7.4 Å), but the key sites of nucleotide binding and/or phosphorylation are reasonably well supported by the EM maps, with one exception: in the 'E1·ATP early' state determined under turnover conditions, I find the map for the gamma phosphate of ATP not overly convincing, leaving the question whether this could instead be a product-inhibited, Mg-ADP bound E1 state resulting from an accumulation of MgADP under the turnover conditions used. Overall, the manuscript is well written and carefully phrased, and it presents interesting novel findings, which expand our knowledge about the conformational landscape and regulatory mechanisms of the P-type ATPase family.

We thank the reviewer for their comments and helpful insights. We have addressed the points as follows:

However in my opinion there are the following weaknesses in the current version of the manuscript:

1) A lack of quantification. The heart of this study is the comparison of the newly determined KdpFABC structures with previously published ones (of which there are already 10). Yet, there are no RMSD calculations to illustrate the magnitude of any structural deviations. Instead, the authors use phrases like 'similar but not identical to', 'has some similarities', 'virtually identical', 'significant differences'. This makes it very hard to appreciate the true level of novelty/deviation from known structures.

This is a very valid point and we thank the reviewers for bringing it up. To provide a better overview and appreciation of conformational similarities and significant differences we have calculated RMSDs between all available structures of KdpFABC. They are summarised in the new Table 1 – Table Supplement 2. We have included individual rmsd values, whenever applicable and relevant, in the respective sections in the text and figures. We note that the RMSDs were calculated only between the cytosolic domains (KdpB N,A,P domains) after superimposition of the full-length protein on KdpA, which is rigid across all conformations of KdpFABC (see description in material and methods lines 1184-1191 or the caption to Table 1 – Table Supplement 2). We opted to not indicate the RMSD calculated between the full-length proteins, as the largest part of the complex does not undergo large structural changes (see Figure 1 – Figure Supplement 1, the transmembrane region of KdpB as well as KdpA, KdpC and KdpF show relatively small to no rearrangements compared to the cytosolic domains), and would otherwise obscure the relevant RMSD differences discussed here.

Also the decrease in EPR peak height of the E1 apo tight state between phosphorylated and non-phosphorylated sample - a key piece of supporting data - is not quantified.

EPR distance distributions have been quantified by fitting and integrating a gaussian distribution curve, and have been added to the corresponding results section (lines 523-542) and the methods section (lines 1230-1232).

2) Perhaps as a consequence of the above, there seems to be a slight tendency towards overstatements regarding the novelty of the findings in the context of previous structural studies. The E1-P·ATP tight structure is extremely similar to the previously published crystal structure (5MRW), but it took me three reads through the paper and a structural superposition (overall RMSD less than 2Å), to realise that. While I do see that the existing differences, the two helix shifts in the P- and A- domains - are important and do probably permit the usage of the term 'novel conformation' (I don't think there is a clear consensus on what level of change defines a novel conformation), it could have been made more clear that the 'tight' arrangement of domains has actually been reported before, only it was not termed 'tight'.

As indicated above we have now included an extensive RMSD table between all available KdpFABC structures. To ensure a meaningful comparison, the rmsd are only calculated between the cytosolic domains after superimposition of the full-length protein on KdpA, as the transmembrane region of KdpFABC is largely rigid (see figure below panel B). However, we have to note that in the X-ray structure the transmembrane region of KdpB is displaced relative to the rest of the complex when compared to the arrangement found in any of the other 18 cryo-EM structures, which all align well in the TMD (see figure below panel C). These deviations make the crystal structure somewhat of an outlier and might be a consequence of the crystal packing (see figure below panel A). For completeness in our comparison with the X-Ray structure, we have included an RMSD calculated when superimposed on KdpA and additional RMSD that was calculated between structures when aligned on the TMD of KdpB (see figure below panel D,E). The reported RMSD that the reviewer mentiones of less than 2Å was probably obtained when superimposing the entire complex on each other (see figure below panel F). However, we do not believe that this is a reasonable comparison as the TMD of the complex is significantly displaced, which stands in strong contrast to all other RMSDs calculated between the rest of the structures where the TMD aligns well (see figure below panel B).

From the resulting comparisons, we conclude that the E1P-tight and the X-Ray structure do have a certain similarity but are not identical. In particular not in the relative orientation of the cytosolic domains to the rest of the complex. We hope that including the RMSD in the text and separately highlighting the important features of the E1P tight state in the section “E1P tight is the consequence of an impaired E1P/E2P transition“ makes the story now more conclusive.

Likewise, the authors claim that they have covered the entire conformational cycle with their 10 structures, but this is actually not correct, as there is no representative of an E2 state or functional E1P state after ADP release.

This is correct, and we have adjusted the phrasing to “close to the entire conformational cycle” or “the entire KdpFABC conformational cycle except the highly transient E1P state after ADP release and E2 state after dephosphorylation.”

3) A key hypothesis this paper suggests is that KdpFABC cannot undergo the transition from E1P tight to E2P and hence gets stuck in this dead end 'off cycle' state. To test this, the authors analysed an S162-P sample supplied with the E2P inducing inhibitor orthovanadate and found about 11% of particles in an E2P conformation. This is rationalised as a residual fraction of unphosphorylated, non-inhibited, protein in the sample, but the sample is not actually tested for residual unphosphorylated fraction or residual activity. Instead, there is a reference to Sweet et al, 2020. So the claim that the 11% E2P particles in the vanadate sample are irrelevant, whereas the 14% E1P tight from the turnover dataset are of key importance, would strongly benefit from some additional validation.

We have added an ATPase assay that shows the residual ATPase activity of WT KdpFABC compared to KdpFABS162AC, both purified from E. coli LB2003 cells, which is identical to the protein production and purification for the cryo-EM samples (see Figure 2-Suppl. Figure 5). The residual ATPase activity is ca. 14% of the uninhibited sample, which correlates with the E2-P fraction in the orthovanadate sample.

Reviewer #3 (Public Review):

The authors have determined a range of conformations of the high-affinity prokaryotic K+ uptake system KdpFABC, and demonstrate at least two novel states that shed further light on the structure and function of these elusive protein complexes.

The manuscript is well-written and easy to follow. The introduction puts the work in a proper context and highlights gaps in the field. I am however missing an overview of the currently available structures/states of KdpFABC. This could also be implemented in Fig. 6 (highlighting new vs available data). This is also connected to one of my main remarks - the lack of comparisons and RMSD estimates to available structures. Similarity/resemblance to available structures is indicated several times throughout the manuscript, but this is not quantified or shown in detail, and hence it is difficult for the reader to grasp how unique or alike the structures are. Linked to this, I am somewhat surprised by the lack of considerable changes within the TM domain and the overlapping connectivity of the K indicated in Table 1 - Figure Supplement 1. According to Fig. 6 the uptake pathway should be open in early E1 states, but not in E2 states, contrasting to the Table 1 - Figure Supplement 1, which show connectivity in all structures? Furthermore, the release pathway (to the inside) should be open in the E2-P conformation, but no release pathway is shown as K ions in any of the structures in Table 1 - Figure Supplement 1. Overall, it seems as if rather small shifts in-between the shown structures (are the structures changing from closed to inward-open)? Or is it only KdpA that is shown?

We thank the reviewer for their positive response and constructive criticisms. We have addressed these comments as follows:

1. The overview of the available structures has been implemented in Fig. 6, with the new structures from this study highlighted in bold.

2. RMSD values have been added to all comparisons, with a focus on the deviations of the cytosolic domains, which are most relevant to our conformational assignments and discussions.

3. To highlight the (comparatively small) changes in the TMD, we have expanded Table 1 - Figure Supplement 1 to include panels showing the outward-open half-channel in the E1 states with a constriction at the KdpA/KdpB interface and the inward-open half-channel in the E2 states. The largest observable rearrangements do however take place in the cytosolic domains. This is an absolute agreement with previous studies, which focused more on the transition occurring within the transmembrane region during the transport cycle (Stock et al, Nature Communication 2018; Silberberg et al, Nature Communication 2021; Sweet et al., PNAS 2021).

4. The ions observed in the intersubunit tunnel are all before the point at which the tunnel closes, explaining why there is no difference in this region between E1 and E2 structures. Moreover, as we discussed in our last publication (Silberberg, Corey, Hielkema et al., 2021, Nat. Comms.), the assignment of non-protein densities along the entire length of the tunnel is contentious and can only be certain in the selectivity filter of KdpA and the CBS of KdpB.

5. The release pathway from the CBS does not feature any defined K+ coordination sites, so ions are not expected to stay bound along this inward-open half-channel.

My second key remark concerns the "E1-P tight is the consequence of an impaired E1-P/E2-P transition" section, and the associated discussion, which is very interesting. I am not convinced though that the nucleotide and phosphate mimic-stabilized states (such as E1-P:ADP) represent the high-energy E1P state, as I believe is indicated in the text. Supportive of this, in SERCA, the shifts from the E1:ATP to the E1P:ADP structures are modest, while the following high-energy Ca-bound E1P and E2P states remain elusive (see Fig. 1 in PMID: 32219166, from 3N8G to 3BA6). Or maybe this is not what the authors claim, or the situation is different for KdpFABC? Associated, while I agree with the statement in rows 234-237 (that the authors likely have caught an off-cycle state), I wonder if the tight E1-P configuration could relate to the elusive high-energy states (although initially counter-intuitive as it has been caught in the structure)? The claims on rows 358-360 and 420-422 are not in conflict with such an idea, and the authors touch on this subject on rows 436-450. Can it be excluded that it is the proper elusive E1P state? If the state is related to the E1P conformation it may well have bearing also on other P-type ATPases and this could be expanded upon.

This a good point, particularly since the E1P·ADP state is the most populated state in our sample, which is also counterintuitive to “high-energy unstable state”. One possible explanation is that this state already has some of the E1-P strains (which we can see in the clash of D307-P with D518/D522), but the ADP and its associated Mg2+ in particular help to stabilize this. Once ADP dissociates and takes the Mg2+ with it, the full destabilization takes effect in the actual high-energy E1P state. Nonetheless, we consider it fair to compare the E1P tight with the E1P·ADP to look for electrostatic relaxation. We have clarified the sequence of events and our hypothesized role the ADP/Mg2+ have in stabilizing the E1P·ADP state that we can see (lines 609-619): “Moreover, a comparison of the E1P tight structure with the E1P·ADP structure, its most immediate precursor in the conformational cycle obtained, reveals a number of significant rearrangements within the P domain (Figure 5B,C). First, Helix 6 (KdpB538-545) is partially unwound and has moved away from helix 5 towards the A domain, alongside the tilting of helix 4 of the A domain (Figure 5B,C – arrow 2). Second, and of particular interest, are the additional local changes that occur in the immediate vicinity of the phosphorylated KdpBD307. In the E1P·ADP structure, the catalytic aspartyl phosphate, located in the D307KTG signature motif, points towards the negatively charged KdpBD518/D522. This strain is likely to become even more unfavorable once ADP dissociates in the E1P state, as the Mg2+ associated with the ADP partially shields these clashes. The ensuing repulsion might serve as a driving force for the system to relax into the E2 state in the catalytic cycle.”

We believe it is highly unlikely that the reported E1-P tight state represents an on-cycle high-energy E1P intermediate. For one, we observe a relaxation of electrostatic strains in this structure, in particular when compared to the obtained E1P ADP state. By contrast, the E1P should be the most energetically unfavourable state possible to ensure the rapid transition to the E2P state. As such, this state should be a transient state, making it less likely to be obtainable structurally as an accumulated state. Additionally, the association of the N domain with the A domain in the tight conformation, which would have to be reverted, would be a surprising intermediary step in the transition from E1P to E2P. Altogether, the here reported E1P tight state most likely represents an off-cycle state.

Author Response

Reviewer #1 (Public Review):

Buglak et al. describe a role for the nuclear envelope protein Sun1 in endothelial mechanotransduction and vascular development. The study provides a full mechanistic investigation of how Sun1 is achieving its function, which supports the concept that nuclear anchoring is important for proper mechanosensing and junctional organization. The experiments have been well designed and were quantified based on independent experiments. The experiments are convincing and of high quality and include Sun1 depletion in endothelial cell cultures, zebrafish, and in endothelial-specific inducible knockouts in mice.

We thank the reviewer for their enthusiastic comments and for noting our use of multiple model systems.

Reviewer #2 (Public Review):

Endothelial cells mediate the growth of the vascular system but they also need to prevent vascular leakage, which involves interactions with neighboring endothelial cells (ECs) through junctional protein complexes. Buglak et al. report that the EC nucleus controls the function of cell-cell junctions through the nuclear envelope-associated proteins SUN1 and Nesprin-1. They argue that SUN1 controls microtubule dynamics and junctional stability through the RhoA activator GEF-H1.

In my view, this study is interesting and addresses an important but very little-studied question, namely the link between the EC nucleus and cell junctions in the periphery. The study has also made use of different model systems, i.e. genetically modified mice, zebrafish, and cultured endothelial cells, which confirms certain findings and utilizes the specific advantages of each model system. A weakness is that some important controls are missing. In addition, the evidence for the proposed molecular mechanism should be strengthened.

We thank the reviewer for their interest in our work and for highlighting the relative lack of information regarding connections between the EC nucleus and cell periphery, and for noting our use of multiple model systems. We thank the reviewer for suggesting additional controls and mechanistic support, and we have made the revisions described below.

Specific comments:

1) Data showing the efficiency of Sun1 inactivation in the murine endothelial cells is lacking. It would be best to see what is happening on the protein level, but it would already help a great deal if the authors could show a reduction of the transcript in sorted ECs. The excision of a DNA fragment shown in the lung (Fig. 1-suppl. 1C) is not quantitative at all. In addition, the gel has been run way too short so it is impossible to even estimate the size of the DNA fragment.

We agree that the DNA excision is not sufficient to demonstrate excision efficiency. We attempted examination of SUN1 protein levels in mutant retinas via immunofluorescence, but to date we have not found a SUN1 antibody that works in mouse retinal explants. We argue that mouse EC isolation protocols enrich but don’t give 100% purity, so that RNA analysis of lung tissue also has caveats. Finally, we contend that our demonstration of a consistent vascular phenotype in Sun1iECKO mutant retinas argues that excision has occurred. To test the efficiency of our excision protocol, we bred Cdh5CreERT2 mice with the ROSAmT/mG excision reporter (cells express tdTomato absent Cre activity and express GFP upon Cre-mediated excision (Muzumdar et al., 2007). Utilizing the same excision protocol as used for the Sun1iECKO mice, we see a significantly high level of excision in retinal vessels only in the presence of Cdh5CreERT2 (Reviewer Figure 1).

Reviewer Figure 1: Cdh5CreERT2 efficiently excises in endothelial cells of the mouse postnatal retina. (A) Representative images of P7 mouse retinas with the indicated genotypes, stained for ERG (white, nucleus). tdTomato (magenta) is expressed in cells that have not undergone Cre-mediated excision, while GFP (green) is expressed in excised cells. Scale bar, 100μm. (B) Quantification of tdTomato fluorescence relative to GFP fluorescence as shown in A. tdTomato and GFP fluorescence of endothelial cells was measured by creating a mask of the ERG channel. n=3 mice per genotype. ***, p<0.001 by student’s two-tailed unpaired t-test.

2) The authors show an increase in vessel density in the periphery of the growing Sun1 mutant retinal vasculature. It would be important to add staining with a marker labelling EC nuclei (e.g. Erg) because higher vessel density might reflect changes in cell size/shape or number, which has also implications for the appearance of cell-cell junctions. More ECs crowded within a small area are likely to have more complicated junctions. Furthermore, it would be useful and straightforward to assess EC proliferation, which is mentioned later in the experiments with cultured ECs but has not been addressed in the in vivo part.

We concur that ERG staining is important to show any changes in nuclear shape or cell density in the post-natal retina. We now include this data in Figure1-figure supplement 1F-G. We do not see obvious changes in nuclear shape or number, though we do observe some crowding in Sun1iECKO retinas, consistent with increased density. However, when normalized to total vessel area, we do not observe a significant difference in the nuclear signal density in Sun1iECKO mutant retinas relative to controls.

3) It appears that the loss of Sun1/sun1b in mice and zebrafish is compatible with major aspects of vascular growth and leads to changes in filopodia dynamics and vascular permeability (during development) without severe and lasting disruption of the EC network. It would be helpful to know whether the loss-of-function mutants can ultimately form a normal vascular network in the retina and trunk, respectively. It might be sufficient to mention this in the text.

We thank the reviewer for pointing this out. It is true that developmental defects in the vasculature resulting from various genetic mutations are often resolved over time. We’ve made text changes to discuss viability of Sun1 global KO mice and lack of perduring effects in sun1 morphant fish, perhaps resulting from compensation by SUN2, which is partially functionally redundant with SUN1 in vivo (Lei et al., 2009; Zhang, et al., 2009) (p. 20).

4) The only readout after the rescue of the SUN1 knockdown by GEF-H1 depletion is the appearance of VE-cadherin+ junctions (Fig. 6G and H). This is insufficient evidence for a relatively strong conclusion. The authors should at least look at microtubules. They might also want to consider the activation status of RhoA as a good biochemical readout. It is argued that RhoA activity goes up (see Fig. 7C) but there is no data supporting this conclusion. It is also not clear whether "diffuse" GEF-H1 localization translates into increased Rho A activity, as is suggested by the Rho kinase inhibition experiment. GEF-H1 levels in the Western blot in (Fig. 6- supplement 2C) have not been quantitated.

We agree that analysis of RhoA activity and additional analysis of rescued junctions strengthens our conclusions, so we performed these experiments. New data (Figure 6IJ) shows that co-depletion of SUN1 and GEF-H1 rescues junction integrity as measured by biotin-matrix labeling. Interestingly, co-depletion of SUN1 and GEF-H1 does not rescue reduced microtubule density at the periphery (Figure 6-figure supplement 3BC), placing GEF-H1 downstream of aberrant microtubule dynamics in SUN1 depleted cells. This is consistent with our model (Figure 8) describing how loss of SUN1 leads to increased microtubule depolymerization, resulting in release and activation of GEF-H1 that goes on to affect actomyosin contractility and junction integrity. In addition, we include images of the junctions in GEF-H1 single KD (Figure 6-figure supplement 3BC) and quantify the western blot in Figure 6-figure supplement 3A.

We performed RhoA activity assays and new data shows that SUN1 depletion results in increased RhoA activation, while co-depletion of SUN1 and GEF-H1 ameliorates this increase (Figure 6-figure supplement 2D). This is consistent with our model in which loss of SUN1 leads to increased RhoA activity via release of GEF-H1 from microtubules. In addition, we now cite a recent study describing that GEF-H1 is activated when unbound to microtubules, with this activation resulting in increased RhoA activity (Azoitei et al., 2019).

5) The criticism raised for the GEF-H1 rescue also applies to the co-depletion of SUN1 and Nesprin-1. This mechanistic aspect is currently somewhat weak and should be strengthened. Again, Rho A activity might be a useful and quantitative biochemical readout.

We respectfully point out that we showed that co-depletion of nesprin-1 and SUN1 rescues SUN1 knockdown effects via several readouts, including rescue of junction morphology, biotin labeling, microtubule localization at the periphery, and GEFH1/microtubule localization. We’ve moved this data to the main figure (Figure 7B-C, E-F) to better highlight these mechanistic findings. These results are consistent with our model that nesprin-1 effects are upstream of GEF-H1 localization. We also added results showing that nesprin-1 knockdown alone does not affect junction integrity, microtubule density, or GEF-H1/microtubule localization (Figure 7-figure supplement 1B-G).

Reviewer #3 (Public Review):

Here, Buglak and coauthors describe the effect of Sun1 deficiency on endothelial junctions. Sun1 is a component of the LINC complex, connecting the inner nuclear membrane with the cytoskeleton. The authors show that in the absence of Sun1, the morphology of the endothelial adherens junction protein VE-cadherin is altered, indicative of increased internalization of VE-cadherin. The change in VE-cadherin dynamics correlates with decreased angiogenic sprouting as shown using in vivo and in vitro models. The study would benefit from a stricter presentation of the data and needs additional controls in certain analyses.

We thank the reviewer for their insightful comments, and in response we have performed the revisions described below.

1) The authors implicate the changes in VE-cadherin morphology to be of consequence for "barrier function" and mention barrier function frequently throughout the text, for example in the heading on page 12: "SUN1 stabilizes endothelial cell-cell junctions and regulates barrier function". The concept of "barrier" implies the ability of endothelial cells to restrict the passage of molecules and cells across the vessel wall. This is tested only marginally (Suppl Fig 1F) and these data are not quantified. Increased leakage of 10kDa dextran in a P6-7 Sun1-deficient retina as shown here probably reflects the increased immaturity of the Sun1-deficient retinal vasculature. From these data, the authors cannot state that Sun1 regulates the barrier or barrier function (unclear what exactly the authors refer to when they make a distinction between the barrier as such on the one hand and barrier function on the other). The authors can, if they do more experiments, state that loss of Sun1 leads to increased leakage in the early postnatal stages in the retina. However, if they wish to characterize the vascular barrier, there is a wide range of other tissue that should be tested, in the presence and absence of disease. Moreover, a regulatory role for Sun1 would imply that Sun1 normally, possibly through changes in its expression levels, would modulate the barrier properties to allow more or less leakage in different circumstances. However, no such data are shown. The authors would need to go through their paper and remove statements regarding the regulation of the barrier and barrier function since these are conclusions that lack foundation.

We thank the reviewer for pointing out that the language used regarding the function and integrity of the junctions is confusing, although we suggest that the endothelial cell properties measured by our assays are typically equated with “barrier function” in the literature. However, we have edited our language to precisely describe our results as suggested by the reviewer.

2) In Fig 6g, the authors show that "depletion of GEF-H1 in endothelial cells that were also depleted for SUN1 rescued the destabilized cell-cell junctions observed with SUN1 KD alone". However, it is quite clear that Sun1 depletion also affects cell shape and cell alignment and this is not rescued by GEF-H1 depletion (Fig 6g). This should be described and commented on. Moreover please show the effects of GEF-H1 alone.

We thank the reviewer for pointing out the effects on cell shape. SUN1 depletion typically leads to shape changes consistent with elevated contractility, but this is considered to be downstream of the effects quantified here. We updated the panel in Figure 6G to a more representative image showing cell shape rescue by co-depletion of SUN1 and GEF-H1. We present new data panels showing that GEF-H1 depletion alone does not affect junction integrity (Figure 6I-J). We also present new data showing that co-depletion of GEF-H1 and SUN1 does not rescue microtubule density at the periphery (Figure 6-figure supplement 3B-C), consistent with our model that GEF-H1 activation is downstream of microtubule perturbations induced by SUN1 loss.

3) In Fig. 6a, the authors show rescue of junction morphology in Sun1-depleted cells by deletion of Nesprin1. The effect of Nesprin1 KD alone is missing.

We thank the reviewer for this comment, and we now include new panels (Figure 7figure supplement 1B-G) demonstrating that Nesprin-1 depletion does not affect biotin-matrix labeling, peripheral microtubule density, or GEF-H1/microtubule localization absent co-depletion with SUN1. These findings are consistent with our model that Nesprin-1 loss does not affect cell junctions on its own because it is held in a non-functional complex with SUN1 that is not available in the absence of SUN1.

References

Azoitei, M. L., Noh, J., Marston, D. J., Roudot, P., Marshall, C. B., Daugird, T. A., Lisanza, S. L., Sandί, M., Ikura, M., Sondek, J., Rottapel, R., Hahn, K. M., Danuser, & Danuser, G. (2019). Spatiotemporal dynamics of GEF-H1 activation controlled by microtubule- and Src-mediated pathways. Journal of Cell Biology, 218(9), 3077-3097. https://doi.org/10.1083/jcb.201812073

Denis, K. B., Cabe, J. I., Danielsson, B. E., Tieu, K. V, Mayer, C. R., & Conway, D. E. (2021). The LINC complex is required for endothelial cell adhesion and adaptation to shear stress and cyclic stretch. Molecular Biology of the Cell, mbcE20110698. https://doi.org/10.1091/mbc.E20-11-0698

King, S. J., Nowak, K., Suryavanshi, N., Holt, I., Shanahan, C. M., & Ridley, A. J. (2014). Nesprin-1 and nesprin-2 regulate endothelial cell shape and migration. Cytoskeleton (Hoboken, N.J.), 71(7), 423–434. https://doi.org/10.1002/cm.21182

Lei, K., Zhang, X., Ding, X., Guo, X., Chen, M., Zhu, B., Xu, T., Zhuang, Y., Xu, R., & Han, M. (2009). SUN1 and SUN2 play critical but partially redundant roles in anchoring nuclei in skeletal muscle cells in mice. PNAS, 106(25), 10207–10212.

Muzumdar, M. D., Tasic, B., Miyamichi, K., Li, L., & Luo, L. (2007). A global doublefluorescent Cre reporter mouse. Genesis, 45(9), 593-605. https://doi.org/10.1002/dvg.20335

Ueda, N., Maekawa, M., Matsui, T. S., Deguchi, S., Takata, T., Katahira, J., Higashiyama, S., & Hieda, M. (2022). Inner Nuclear Membrane Protein, SUN1, is Required for Cytoskeletal Force Generation and Focal Adhesion Maturation. Frontiers in Cell and Developmental Biology, 10, 885859. https://doi.org/10.3389/fcell.2022.885859

Zhang, X., Lei, K., Yuan, X., Wu, X., Zhuang, Y., Xu, T., Xu, R., & Han, M. (2009). SUN1/2 and Syne/Nesprin-1/2 complexes connect centrosome to the nucleus during neurogenesis and neuronal migration in mice. Neuron, 64(2), 173–187. https://doi.org/10.1016/j.neuron.2009.08.018.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study by Teplenin and coworkers assesses the combined effects of localized depolarization and excitatory electrical stimulation in myocardial monolayers. They study the electrophysiological behaviour of cultured neonatal rat ventricular cardiomyocytes expressing the light-gated cation channel Cheriff, allowing them to induce local depolarization of varying area and amplitude, the latter titrated by the applied light intensity. In addition, they used computational modeling to screen for critical parameters determining state transitions and to dissect the underlying mechanisms. Two stable states, thus bistability, could be induced upon local depolarization and electrical stimulation, one state characterized by a constant membrane voltage and a second, spontaneously firing, thus oscillatory state. The resulting 'state' of the monolayer was dependent on the duration and frequency of electrical stimuli, as well as the size of the illuminated area and the applied light intensity, determining the degree of depolarization as well as the steepness of the local voltage gradient. In addition to the induction of oscillatory behaviour, they also tested frequency-dependent termination of induced oscillations.

Strengths:

The data from optogenetic experiments and computational modelling provide quantitative insights into the parameter space determining the induction of spontaneous excitation in the monolayer. The most important findings can also be reproduced using a strongly reduced computational model, suggesting that the observed phenomena might be more generally applicable.

Weaknesses:

While the study is thoroughly performed and provides interesting mechanistic insights into scenarios of ventricular arrhythmogenesis in the presence of localized depolarized tissue areas, the translational perspective of the study remains relatively vague. In addition, the chosen theoretical approach and the way the data are presented might make it difficult for the wider community of cardiac researchers to understand the significance of the study.

Reviewer #2 (Public review):

In the presented manuscript, Teplenin and colleagues use both electrical pacing and optogenetic stimulation to create a reproducible, controllable source of ectopy in cardiomyocyte monolayers. To accomplish this, they use a careful calibration of electrical pacing characteristics (i.e., frequency, number of pulses) and illumination characteristics (i.e., light intensity, surface area) to show that there exists a "sweet spot" where oscillatory excitations can emerge proximal to the optogenetically depolarized region following electrical pacing cessation, akin to pacemaker cells. Furthermore, the authors demonstrate that a high-frequency electrical wave-train can be used to terminate these oscillatory excitations. The authors observed this oscillatory phenomenon both in vitro (using neonatal rat ventricular cardiomyocyte monolayers) and in silico (using a computational action potential model of the same cell type). These are surprising findings and provide a novel approach for studying triggered activity in cardiac tissue.

The study is extremely thorough and one of the more memorable and grounded applications of cardiac optogenetics in the past decade. One of the benefits of the authors' "two-prong" approach of experimental preps and computational models is that they could probe the number of potential variable combinations much deeper than through in vitro experiments alone. The strong similarities between the real-life and computational findings suggest that these oscillatory excitations are consistent, reproducible, and controllable.

Triggered activity, which can lead to ventricular arrhythmias and cardiac sudden death, has been largely attributed to sub-cellular phenomena, such as early or delayed afterdepolarizations, and thus to date has largely been studied in isolated single cardiomyocytes. However, these findings have been difficult to translate to tissue and organ-scale experiments, as well-coupled cardiac tissue has notably different electrical properties. This underscores the significance of the study's methodological advances: the use of a constant depolarizing current in a subset of (illuminated) cells to reliably result in triggered activity could facilitate the more consistent evaluation of triggered activity at various scales. An experimental prep that is both repeatable and controllable (i.e., both initiated and terminated through the same means).

The authors also substantially explored phase space and single-cell analyses to document how this "hidden" bi-stable phenomenon can be uncovered during emergent collective tissue behavior. Calibration and testing of different aspects (e.g., light intensity, illuminated surface area, electrical pulse frequency, electrical pulse count) and other deeper analyses, as illustrated in Appendix 2, Figures 3-8, are significant and commendable.

Given that the study is computational, it is surprising that the authors did not replicate their findings using well-validated adult ventricular cardiomyocyte action potential models, such as ten Tusscher 2006 or O'Hara 2011. This may have felt out of scope, given the nice alignment of rat cardiomyocyte data between in vitro and in silico experiments. However, it would have been helpful peace-of-mind validation, given the significant ionic current differences between neonatal rat and adult ventricular tissue. It is not fully clear whether the pulse trains could have resulted in the same bi-stable oscillatory behavior, given the longer APD of humans relative to rats. The observed phenomenon certainly would be frequency-dependent and would have required tedious calibration for a new cell type, albeit partially mitigated by the relative ease of in silico experiments.

For all its strengths, there are likely significant mechanistic differences between this optogenetically tied oscillatory behavior and triggered activity observed in other studies. This is because the constant light-elicited depolarizing current is disrupting the typical resting cardiomyocyte state, thereby altering the balance between depolarizing ionic currents (such as Na+ and Ca2+) and repolarizing ionic currents (such as K+ and Ca2+). The oscillatory excitations appear to later emerge at the border of the illuminated region and non-stimulated surrounding tissue, which is likely an area of high source-sink mismatch. The authors appear to acknowledge differences in this oscillatory behavior and previous sub-cellular triggered activity research in their discussion of ectopic pacemaker activity, which is canonically expected more so from genetic or pathological conditions. Regardless, it is exciting to see new ground being broken in this difficult-to-characterize experimental space, even if the method illustrated here may not necessarily be broadly applicable.

We thank the reviewers for their thoughtful and constructive feedback, as well as for recognizing the conceptual and technical strengths of our work. We are especially pleased that our integrated use of optogenetics, electrical pacing, and computational modelling was seen as a rigorous and innovative approach to investigating spontaneous excitability in cardiac tissue.

At the core of our study was the decision to focus exclusively on neonatal rat ventricular cardiomyocytes. This ensured a tightly controlled and consistent environment across experimental and computational settings, allowing for direct comparison and deeper mechanistic insight. While extending our findings to adult or human cardiomyocytes would enhance translational relevance, such efforts are complicated by the distinct ionic properties and action potential dynamics of these cells, as also noted by Reviewer #2. For this foundational study, we chose to prioritize depth and clarity over breadth.

Our computational domain was designed to faithfully reflect the experimental system. The strong agreement between both domains is encouraging and supports the robustness of our framework. Although some degree of theoretical abstraction was necessary (thereby sometimes making it a bit harder to read), it reflects the intrinsic complexity of the collective behaviours we aimed to capture such as emergent bi-stability. To make these ideas more accessible, we included simplified illustrations, a reduced model, and extensive supplementary material.

A key insight from our work is the emergence of oscillatory behaviour through interaction of illuminated and non-illuminated regions. Rather than replicating classical sub-cellular triggered activity, this behaviour arises from systems-level dynamics shaped by the imposed depolarizing current and surrounding electrotonic environment. By tuning illumination and local pacing parameters, we could reproducibly induce and suppress these oscillations, thereby providing a controllable platform to study ectopy as a manifestation of spatial heterogeneity and collective dynamics.

Altogether, our aim was to build a clear and versatile model system for investigating how spatial structure and pacing influence the conditions under which bistability becomes apparent in cardiac tissue. We believe this platform lays strong groundwork for future extensions into more physiologically and clinically relevant contexts.

In revising the manuscript, we carefully addressed all points raised by the reviewers. We have also responded to each of their specific comments in detail, which are provided below.

Recommendations for the Authors:

Reviewer #1 (Recommendations for the authors):

Please find my specific comments and suggestions below:

(1) Line 64: When first introduced, the concept of 'emergent bi-stability' may not be clear to the reader.

We concur that the full breadth of the concept of emergent bi-stability may not be immediately clear upon first mention. Nonetheless, its components have been introduced separately: “emergent” was linked to multicellular behaviour in line 63, while “bi-stability” was described in detail in lines 39–56. We therefore believe that readers could form an intuitive understanding of the combined term, which will be further clarified as the manuscript develops. To further ease comprehension of the reader, we have added the following clarification to line 64:

“Within this dynamic system of cardiomyocytes, we investigated emergent bi-stability (a concept that will be explained more thoroughly later on) in cell monolayers under the influence of spatial depolarization patterns.”

(2) Lines 67-80: While the introduction until line 66 is extremely well written, the introduction of both cardiac arrhythmia and cardiac optogenetics could be improved. It is especially surprising that miniSOG is first mentioned as a tool for optogenetic depolarisation of cardiomyocytes, as the authors would probably agree that Channelrhodopsins are by far the most commonly applied tools for optogenetic depolarisation (please also refer to the literature by others in this respect). In addition, miniSOG has side effects other than depolarisation, and thus cannot be the tool of choice when not directly studying the effects of oxidative stress or damage.

The reviewer is absolutely correct in noting that channelrhodopsins are the most commonly applied tools for optogenetic depolarisation. We introduced miniSOG primarily for historical context: the effects of specific depolarization patterns on collective pacemaker activity were first observed with this tool (Teplenin et al., 2018). In that paper, we also reported ultralong action potentials, occurring as a side effect of cumulative miniSOG-induced ROS damage. In the following paragraph (starting at line 81), we emphasize that membrane potential can be controlled much better using channelrhodopsins, which is why we employed them in the present study.

(3) Line 78: I appreciate the concept of 'high curvature', but please always state which parameter(s) you are referring to (membrane voltage in space/time, etc?).

We corrected our statement to include the specification of space curvature of the depolarised region:

“In such a system, it was previously observed that spatiotemporal illumination can give rise to collective behaviour and ectopic waves (Teplenin et al. (2018)) originating from illuminated/depolarised regions (with high spatial curvature).”

(4) Line 79: 'bi-stable state' - not yet properly introduced in this context.

The bi-stability mentioned here refers back to single cell bistability introduced in Teplenin et al. (2018), which we cited again for clarity.

“These waves resulted from the interplay between the diffusion current and the single cell bi-stable state (Teplenin et al. (2018)) that was induced in the illuminated region.”

(5) Line 84-85: 'these ion channels allow the cells to respond' - please describe the channel used; and please correct: the channels respond to light, not the cells. Re-ordering this paragraph may help, because first you introduce channels for depolarization, then you go back to both de- and hyperpolarization. On the same note, which channels can be used for hyperpolarization of cardiomyocytes? I am not aware of any, even WiChR shows depolarizing effects in cardiomyocytes during prolonged activation (Vierock et al. 2022). Please delete: 'through a direct pathway' (Channelrhodopsins a directly light-gated channels, there are no pathways involved).

We realised that the confusion arose from our use of incorrect terminology: we mistakenly wrote hyperpolarisation instead of repolarisation. In addition to channelrhodopsins such as WiChR, other tools can also induce a repolarising effect, including light-activatable chloride pumps (e.g., JAWS). However, to improve clarity, we recognize that repolarisation is not relevant to our manuscript and therefore decided to remove its mention (see below). Regarding the reported depolarising effects of WiChR in Vierock et al. (2022), we speculate that these may arise either from the specific phenotype of the cardiomyocytes used in the study, i.e. human induced pluripotent stem cell-derived atrial myocytes (aCMs), or from the particular ionic conditions applied during patch-clamp recordings (e.g., a bath solution containing 1 mM KCl). Notably, even after prolonged WiChR activation, the aCMs maintained a strongly negative maximum diastolic potential of approximately –55 mV.

“Although effects of illuminating miniSOG with light might lead to formation of depolarised areas, it is difficult to control the process precisely since it depolarises cardiomyocytes indirectly. Therefore, in this manuscript, we used light-sensitive ion channels to obtain more refined control over cardiomyocyte depolarisation. These ion channels allow the cells to respond to specific wavelengths of light, facilitating direct depolarisation (Ördög et al. (2021, 2023)). By inducing cardiomyocyte depolarisation only in the illuminated areas, optogenetics enables precise spatiotemporal control of cardiac excitability, an attribute we exploit in this manuscript (Appendix 2 Figure 1).”

(6) Figure 1: What would be the y-axis of the 'energy-like curves' in B? What exactly did you plot here?

The graphs in Figure 1B are schematic representations intended to clarify the phenomenon for the reader. They do not depict actual data from any simulation or experiment. We clarified this misunderstanding by specifying that Figure 1B is a schematic representation of the effects at play in this paper.

“(B) Schematic representation showing how light intensity influences collective behaviour of excitable systems, transitioning between a stationary state (STA) at low illumination intensities and an oscillatory state (OSC) at high illumination intensities. Bi-stability occurs at intermediate light intensities, where transitions between states are dependent on periodic wave train properties. TR. OSC, transient oscillations.”

To expand slightly beyond the paper: our schematic representation was inspired by a common visualization in dynamical systems used to illustrate bi-stability (for an example, see Fig. 3 in Schleimer, J. H., Hesse, J., Contreras, S. A., & Schreiber, S. (2021). Firing statistics in the bistable regime of neurons with homoclinic spike generation. Physical Review E, 103(1), 012407.). In this framework, the y-axis can indeed be interpreted as an energy landscape, which is related to a probability measure through the Boltzmann distribution: . Here, p denotes the probability of occupying a particular state (STA or OSC). This probability can be estimated from the area (BCL × number of pulses) falling within each state, as shown in Fig. 4C. Since an attractor corresponds to a high-probability state, it naturally appears as a potential well in the landscape.

(7) Lines 92-93: 'this transition resulted for the interaction of an illuminated region with depolarized CM and an external wave train' - please consider rephrasing (it is not the region interacting with depolarized CM; and the external wave train could be explained more clearly).

We rephrased our unclear sentence as follows:

“This transition resulted from the interaction of depolarized cardiomyocytes in an illuminated region with an external wave train not originating from within the illuminated region.”

(8) Figure 2 and elsewhere: When mentioning 'frequency', please state frequency values and not cycle lengths. Please also reconsider your distinction between high and low frequencies; 200 ms (5 Hz) is actually the normal heart rate for neonatal rats (300 bpm).

In the revised version, we have clarified frequency values explicitly and included them alongside period values wherever frequency is mentioned, to avoid any ambiguity. We also emphasize that our use of "high" and "low" frequency is strictly a relative distinction within the context of our data, and not meant to imply a biological interpretation.

(9) Lines 129-131: Why not record optical maps? Voltage dynamics in the transition zone between depolarised and non-depolarised regions might be especially interesting to look at?

We would like to clarify that optical maps were recorded for every experiment, and all experimental traces of cardiac monolayer activity were derived from these maps. We agree with the reviewer that the voltage dynamics in the transition zone are particularly interesting. However, we selected the data representations that, in our view, best highlight the main mechanisms. When we analysed full voltage profiles, they didn’t add extra insights to this main mechanism. As the other reviewer noted, the manuscript already presents a wide range of regimes, so we decided not to introduce further complexity.

(10) Lines 156-157: Why was the model not adapted to match the biophysical properties (e.g., kinetics, ion selectivity, light sensitivity) of Cheriff?

The model was not adapted to the biophysical properties of Cheriff, because this would entail a whole new study involving extensive patch-clamping experiments, fitting, and calibration to model the correct properties of the ion channel. Beyond considerations of time efficiency, incorporating more specific modelling parameters would not change the essence of our findings. While numeric parameter ranges might shift, the core results would remain unchanged. This is a result of our experimental design where we applied constant illumination of long duration (6s or longer), thus making a difference in kinetical properties of an optogenetic tool irrelevant. In addition, we were able to observe qualitatively similar phenomena using many other depolarising optogenetic tools (e.g. ChR2, ReaChR, CatCh and more) in our in-vitro experiments. We ended up with Cheriff as our optotool-of-choice for the practical reasons of good light-sensitivity and a non-overlapping spectrum with our fluorescent dyes.

Therefore, computationally using a more general depolarising ion channel hints at the more general applicability of the observed phenomena, supporting our claim of a universal mechanism  (demonstrated experimentally with CheRiff and computationally with ChR2).

(11) Line 158: 1.7124 mW/mm^2 - While I understand that this is the specific intensity used as input in the model, I am convinced that the model is not as accurate to predict behaviour at this specific intensity (4 digits after the comma), especially given that the model has not been adapted to Cheriff (probably more light sensitive than ChR2). Can this be rephrased?

We did not aim for quantitative correspondence between the computational model and the biological experiments, but rather for qualitative agreement and mechanistic insight (see line 157). Qualitative comparisons are computationally obtained in a whole range of different intensities, as demonstrated in the 3D diagram of Fig. 4C. We wanted to demonstrate that at one fixed light intensity (chosen to be 1.7124 mW/mm^2 for the most clear effect), it was possible for all three states (STA, OSC. TR. OSC.) to coexist depending on the number of pulses and their period. Therefore the specific intensity used in the computational model is correct, and for reproducibility, we have left it unchanged while clarifying that it refers specifically to the in silico model:

“Simulating at a fixed constant illumination of 1.7124 𝑚𝑊∕𝑚𝑚² and a fixed number of 4 pulses, frequency dependency of collective bi-stability was reproduced in Figure 4A.”

(12) Lines 160, 165, and elsewhere: 'Once again, Once more' - please delete or rephrase.

We agree that we could have written these binding words better and reformulated them to:

“Similar to the experimental observations, only intermediate electrical pacing frequencies (500-𝑚𝑠 period) caused transitions from collective stationary behaviour to collective oscillatory behaviour and ectopic pacemaker activity had periods (710 𝑚𝑠) that were different from the stimulation train period (500 𝑚𝑠). Figure 4B shows the accumulation of pulses necessary to invoke a transition from the collective stationary state to the collective oscillatory state at a fixed stimulation period (600 𝑚𝑠). Also in the in silico simulations, ectopic pacemaker activity had periods (750 𝑚𝑠) that were different from the stimulation train period (600 𝑚𝑠). Also for the transient oscillatory state, the simulations show frequency selectivity (Appendix 2 Figure 4B).”

(13) Line 171: 'illumination strength': please refer to 'light intensity'.

We have revised our formulation to now refer specifically to “light intensity”:

“We previously identified three important parameters influencing such transitions: light intensity, number of pulses, and frequency of pulses.”

(14) Lines 187-188: 'the illuminated region settles into this period of sending out pulses' - please rephrase, the meaning is not clear.

We reformulated our sentence to make its content more clear to the reader:

“For the conditions that resulted in stable oscillations, the green vertical lines in the middle and right slices represent the natural pacemaker frequency in the oscillatory state. After the transition from the stationary towards the oscillatory state, oscillatory pulses emerging from the illuminated region gradually dampen and stabilize at this period, corresponding to the natural pacemaker frequency.”

(15) Figure 7: A)- please state in the legend which parameter is plotted on the y-axis (it is included in the main text, but should be provided here as well); C) The numbers provided in brackets are confusing. Why is (4) a high pulse number and (3) a low pulse number? Why not just state the number of pulses and add alpha, beta, gamma, and delta for the panels in brackets? I suggest providing the parameters (e.g., 800 ms cycle length, 2 pulses, etc) for all combinations, but not rate them with low, high, etc. (see also comment above).

We appreciate the reviewer’s comments and have revised the caption for figure 7, which now reads as follows:

“Figure 7. Phase plane projections of pulse-dependent collective state transitions. (A) Phase space trajectories (displayed in the Voltage – x_r plane) of the NRVM computational model show a limit cycle (OSC) that is not lying around a stable fixed point (STA). (B) Parameter space slice showing the relationship between stimulation period and number of pulses for a fixed illumination intensity (1.72 𝑚𝑊 ∕𝑚𝑚2) and size of the illuminated area (67 pixels edge length). Letters correspond to the graphs shown in C. (C) Phase space trajectories for different combinations of stimulus train period and number of pulses (α: 800 ms cycle length + 2 pulses, β: 800 ms cycle length + 4 pulses, γ: 250 ms cycle length + 3 pulses, δ: 250 ms cycle length + 8 pulses). α and δ do not result in a transition from the resting state to ectopic pacemaker activity, as under these circumstances the system moves towards the stationary stable fixed point from outside and inside the stable limit cycle, respectively. However, for β and γ, the stable limit cycle is approached from outside and inside, respectively, and ectopic pacemaker activity is induced.”

(16) Line 258: 'other dimensions by the electrotonic current' - not clear, please rephrase and explain.

We realized that our explanation was somewhat convoluted and have therefore changed the text as follows:

“Rather than producing oscillations, the system returns to the stationary state along dimensions other than those shown in Figure 7C (Voltage and x_r), as evidenced by the phase space trajectory crossing itself. This return is mediated by the electrotonic current.”

(17) Line 263: ‘increased too much’ – please rephrase using scientific terminology.

We rephrased our sentence to:

“However, this is not a Hopf bifurcation, because in that case the system would not return to the stationary state when the number of pulses exceeds a critical threshold.”

(18) Line 275: 'stronger diffusion/electrotonic influence from the non-illuminated region' - not sure diffusion is the correct term here. Please explain by taking into account the membrane potential. Please make sure to use proper terminology. The same applies to lines 281-282.

We appreciate this comment, which prompted us to revisit on our text. We realised that some sections could be worded more clearly, and we also identified an error in the legend of Supplementary Figure 7. The corresponding corrections are provided below:

“However, repolarisation reserve does have an influence, prolonging the transition when it is reduced (Appendix 2 Figure 7). This effect can be observed either by moving further from the boundary of the illuminated region, where the electrotonic influence from the non-illuminated region is weaker, or by introducing ionic changes, such as a reduction in I_Ks and/or I_to. For example, because the electrotonic influence is weaker in the center of the illuminated region, the voltage there is not pulled down toward the resting membrane potential as quickly as in cells at the border of the illuminated zone.”

“To add a multicellular component to our single cell model we introduced a current that replicates the effect of cell coupling and its associated electrotonic influence.”

“Figure 7. The effect of ionic changes on the termination of pacemaker activity. The mechanism that moves the oscillating illuminated tissue back to the stationary state after high frequency pacing is dependent on the ionic properties of the tissue, i.e. lower repolarisation reserves (20% 𝐼_𝐾𝑠 + 50% 𝐼_𝑡𝑜) are associated with longer transition times.”

(19) Line 289: -58 mV (to be corrected), -20 mV, and +50 mV - please justify the selection of parameters chosen. This also applies elsewhere- the selection of parameters seems quite arbitrary, please make sure the selection process is more transparent to the reader.

Our choice of parameters was guided by the dynamical properties of the illuminated cells as well as by illustrative purposes. The value of –58 mV corresponds to the stimulation threshold of the model. The values of 50 mV and –20 mV match those used for single-cell stimulation (Figure 8C2, right panel), producing excitable and bistable dynamics, respectively. We refer to this point in line 288 with the phrase “building on this result.” To maintain conciseness, we did not elaborate on the underlying reasoning within the manuscript and instead reported only the results.

We also corrected the previously missed minus sign: -58 mV.

(20) Figure 8 and corresponding text: I don't understand what stimulation with a voltage means. Is this an externally applied electric field? Or did you inject a current necessary to change the membrane voltage by this value? Please explain.

Stimulation with a specific voltage is a standard computational technique and can be likened to performing a voltage-clamp experiment on each individual cell. In this approach, the voltage of every cell in the tissue is briefly forced to a defined value.

(21) Figure 8C- panel 2: Traces at -20 mV and + 50 mV are identical. Is this correct? Please explain.

Yes, that is correct. The cell responds similarly to a voltage stimulus of -20 mV or one of 50 mV, because both values are well above the excitation threshold of a cardiomyocyte.

(22) Line 344 and elsewhere: 'diffusion current' - This is probably not the correct terminology for gap-junction mediated currents. Please rephrase.

A diffusion current is a mathematical formulation for a gap junction mediated current here, so , depending on the background of the reader, one of the terms might be used focusing on different aspects of the results. In a mathematical modelling context one often refers to a diffusion current because cardiomyocytes monolayers and tissues can be modelled using a reaction-diffusion equation. From the context of fine-grain biological and biophysical details, one uses the term gap-junction mediated current. Our choice is motivated by the main target audience we have in mind, namely interdisciplinary researchers with a core background in the mathematics/physics/computer science fields.

However, to not exclude our secondary target audience of biological and medical readers we now clarified the terminology, drawing the parallel between the different fields of study at line 79:

“These waves resulted from the interplay between the diffusion current (also known in biology/biophysics as the gap junction mediated current) and the bi-stable state that was induced in the illuminated region.”

(23) Lines 357-58: 'Such ectopic sources are typically initiated by high frequency pacing' - While this might be true during clinical testing, how would you explain this when not externally imposed? What could be biological high-frequency triggers?

Biological high-frequency triggers could include sudden increases in heart rates, such as those induced by physical activity or emotional stress. Another possibility is the occurrence of paroxysmal atrial or ventricular fibrillation, which could then give rise to an ectopic source.

(24) Lines 419-420: 'large ionic cell currents and small repolarising coupling currents'. Are coupling currents actually small in comparison to cellular currents? Can you provide relative numbers (~ratio)?

Coupling currents are indeed small compared to cellular currents. This can be inferred from the I-V curve shown in Figure 8C1, which dips below 0 and creates bi-stability only because of the small coupling current. If the coupling current were larger, the system would revert to a monostable regime. To make this more concrete, we have now provided the exact value of the coupling current used in Figure 8C1.

“Otherwise, if the hills and dips of the N-shaped steady-state IV curve were large (Figure 8C-1), they would have similar magnitudes as the large currents of fast ion channels, preventing the subtle interaction between these strong ionic cell currents and the small repolarising coupling currents (-0.103649 ≈ 0.1 pA).”

(25) Line 426: Please explain how ‘voltage shocks’ were modelled.

We would like to refer the reviewer to our response to comment (20) regarding how we model voltage shocks. In the context of line 426, a typical voltage shock corresponds to a tissue-wide stimulus of 50 mV. Independent of our computational model, line 426 also cites other publications showing that, in clinical settings, high-voltage shocks are unable to terminate ectopic sustained activity, consistent with our findings.

(26) Lines 429 ff: 0.2pA/pF would correspond to 20 pA for a small cardiomyocyte of 100 pF, this current should be measurable using patch-clamp recordings.

In trying to be succinct, we may have caused some confusion. The difference between the dips (≈-0.07 pA/pF) and hills (_≈_0.11 pA/pF) is approximately 0.18 pA/pF. For a small cardiomyocyte, this corresponds to deviations from zero of roughly ±10 pA. Considering that typical RMS noise levels in whole-cell patch-clamp recordings range from 2-10 pA , it is understandable that detecting these peaks and dips in an I-V curve (average current after holding a voltage for an extended period)  is difficult. Achieving statistical significance would therefore require patching a large number of cells.

Given the already extensive scope of our manuscript in terms of techniques and concepts, we decided not to pursue these additional patch-clamp experiments.

Reviewer #2 (Recommendations for the authors):

Given the deluge of conditions to consider, there are several areas of improvement possible in communicating the authors' findings. I have the following suggestions to improve the manuscript.

(1) Please change "pulse train" straight pink bar OR add stimulation marks (such as "*", or individual pulse icons) to provide better visual clarity that the applied stimuli are "short ON, long OFF" electrical pulses. I had significant initial difficulty understanding what the pulse bars represented in Figures 2, 3, 4A-B, etc. This may be partially because stimuli here could be either light (either continuous or pulsed) or electrical (likely pulsed only). To me, a solid & unbroken line intuitively denotes a continuous stimulation. I understand now that the pink bar represents the entire pulse-train duration, but I think readers would be better served with an improvement to this indicator in some fashion. For instance, the "phases" were much clearer in Figures 7C and 8D because of how colour was used on the Vm(t) traces. (How you implement this is up to you, though!)

We have addressed the reviewer’s concern and updated the figures by marking each external pulse with a small vertical line (see below).

(2) Please label the electrical stimulation location (akin to the labelled stimulation marker in circle 2 state in Figure 1A) in at least Figures 2 and 4A, and at most throughout the manuscript. It is unclear which "edge" or "pixel" the pulse-train is originating from, although I've assumed it's the left edge of the 2D tissue (both in vitro and silico). This would help readers compare the relative timing of dark blue vs. orange optical signal tracings and to understand how the activation wavefront transverses the tissue.

We indicated the pacing electrode in the optical voltage recordings with a grey asterisk. For the in silico simulations, the electrode was assumed to be far away, and the excitation was modelled as a parallel wave originating from the top boundary, indicated with a grey zone.

(3) Given the prevalence of computational experiments in this study, I suggest considering making a straightforward video demonstrating basic examples of STA, OSC, and TR.OSC states. I believe that a video visualizing these states would be visually clarifying to and greatly appreciated by readers. Appendix 2 Figure 3 would be the no-motion visualization of the examples I'm thinking of (i.e., a corresponding stitched video could be generated for this). However, this video-generation comment is a suggestion and not a request.

We have included a video showing all relevant states, which is now part of the Supplementary Material.

(4) Please fix several typos that I found in the manuscript:

(4A) Line 279: a comma is needed after i.e. when used in: "peculiar, i.e. a standard". However, this is possibly stylistic (discard suggestion if you are consistent in the manuscript).

(4B) Line 382: extra period before "(Figure 3C)".

(4C) Line 501: two periods at end of sentence "scientific purposes.." .

We would like to thank the reviewer for pointing out these typos. We have corrected them and conducted an additional check throughout the manuscript for minor errors.

Author response:

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

Reviewer #1 (Public review): 

Petrovic et al. investigate CCR5 endocytosis via arrestin2, with a particular focus on clathrin and AP2 contributions. The study is thorough and methodologically diverse. The NMR titration data are particularly compelling, clearly demonstrating chemical shift changes at the canonical clathrin-binding site (LIELD), present in both the 2S and 2L arrestin splice variants. 

To assess the effect of arrestin activation on clathrin binding, the authors compare: truncated arrestin (1-393), full-length arrestin, and 1-393 incubated with CCR5 phosphopeptides. All three bind clathrin comparably, whereas controls show no binding. These findings are consistent with prior crystal structures showing peptide-like binding of the LIELD motif, with disordered flanking regions. The manuscript also evaluates a non-canonical clathrin binding site specific to the 2L splice variant. Though this region has been shown to enhance beta2-adrenergic receptor binding, it appears not to affect CCR5 internalization. 

Similar analyses applied to AP2 show a different result. AP2 binding is activation-dependent and influenced by the presence and level of phosphorylation of CCR5-derived phosphopeptides. These findings are reinforced by cellular internalization assays. 

In sum, the results highlight splice-variant-dependent effects and phosphorylation-sensitive arrestin-partner interactions. The data argue against a (rapidly disappearing) one-size-fitsall model for GPCR-arrestin signaling and instead support a nuanced, receptor-specific view, with one example summarized effectively in the mechanistic figure. 

We thank the referee for this positive assessment of our manuscript. Indeed, by stepping away from the common receptor models for understanding internalization (b2AR and V2R), we revealed the phosphorylation level of the receptor as a key factor in driving the sequestration of the receptor from the plasma membrane. We hope that the proposed mechanistic model will aid further studies to obtain an even more detailed understanding of forces driving receptor internalization.

Reviewer #2 (Public review): 

Summary: 

Based on extensive live cell assays, SEC, and NMR studies of reconstituted complexes, these authors explore the roles of clathrin and the AP2 protein in facilitating clathrin-mediated endocytosis via activated arrestin-2. NMR, SEC, proteolysis, and live cell tracking confirm a strong interaction between AP2 and activated arrestin using a phosphorylated C-terminus of CCR5. At the same time, a weak interaction between clathrin and arrestin-2 is observed, irrespective of activation. 

These results contrast with previous observations of class A GPCRs and the more direct participation by clathrin. The results are discussed in terms of the importance of short and long phosphorylated bar codes in class A and class B endocytosis. 

Strengths: 

The 15N,1H, and 13C, methyl TROSY NMR and assignments represent a monumental amount of work on arrestin-2, clathrin, and AP2. Weak NMR interactions between arrestin-2 and clathrin are observed irrespective of the activation of arrestin. A second interface, proposed by crystallography, was suggested to be a possible crystal artifact. NMR establishes realistic information on the clathrin and AP2 affinities to activated arrestin, with both kD and description of the interfaces. 

We sincerely thank the referee for this encouraging evaluation of our work and appreciate the recognition of the NMR efforts and insights into the arrestin–clathrin–AP2 interactions.

Weaknesses: 

This reviewer has identified only minor weaknesses with the study.

(1) Arrestin-2 1-418 resonances all but disappear with CCR5pp6 addition. Are they recovered with Ap2Beta2 addition, and is this what is shown in Supplementary Figure 2D? 

We believe the reviewer is referring to Figure 3 - figure supplement 1. In this figure, the panels E and F show resonances of arrestin2^1-418 (apo state shown with black outline) disappear upon the addition of CCR5pp6 (arrestin2^1-418•CCR5pp6 complex spectrum in red). The panels C and D show resonances of arrestin2^1-418 (apo state shown with black outline), which remain unchanged upon addition of AP2b2^701-937 (orange), indicating no complex formation. We also recorded a spectrum of the arrestin2^1-418 •CCR5pp6 complex under addition of AP2b2 ^701-937(not shown), but the arrestin2 resonances in the arrestin2¹⁴¹⁸ •CCR5pp6 complex were already too broad for further analysis. This had been already explained in the text.

“In agreement with the AP2b2 NMR observations, no interaction was observed in the arrestin2 methyl and backbone NMR spectra upon addition of AP2b2 in the absence of phosphopeptide (Figure 3-figure supplement 1C, D). However, the significant line broadening of the arrestin2 resonances upon phosphopeptide addition (Figure 3-figure supplement 1E, F) precluded a meaningful assessment of the effect of the AP2b2 addition on arrestin2 in the presence of phosphopeptide””.

(2) I don't understand how methyl TROSY spectra of arrestin2 with phosphopeptide could look so broadened unless there are sample stability problems. 

We thank the referee for this comment. We would like to clarify that in general a broadened spectrum beyond what is expected from the rotational correlation time does not necessarily correlate with sample stability problems. It is rather evidence of conformational intermediate exchange on the micro- to millisecond time scale.

The displayed ¹H-¹⁵ N spectra of apo arrestin2 already suffer from line broadening due to such intrinsic mobility of the protein. These spectra were recorded with acquisition times of 50 ms (¹⁵N) and 55 ms (¹H) and resolution-enhanced by a 60˚-shifted sine-bell filter for ¹⁵N and a 60˚-shifted squared sine-bell filter for ¹H, respectively, which leads to the observed resolution with still reasonable sensitivity. The ¹H-¹⁵ resonances in Fig. 1b (arrestin2^1-393) look particularly narrow. However, this region contains a large number of flexible residues. The full spectrum, e.g. Figure 1-figure supplement 2, shows the entire situation with a clear variation of linewidths and intensities. The linewidth variation becomes stronger when omitting the resolution enhancement filters.

The addition of the CCR5pp6 phosphopeptide does not change protein stability, which we assessed by measuring the melting temperature of arrestin2^1-418 and arrestin2^1-418 •CCR5pp6 complex (Tm = 57°C in both cases). We believe that the explanation for the increased broadening of the arrestin2 resonances is that addition of the CCR5pp6, possibly due to the release of the arrestin2 strand b20, amplifies the mentioned intermediate timescale protein dynamics. This results in the disappearance of arrestin2 resonances. 

We have now included the assessment of arrestin2^1-418 and arrestin2^1-418 •CCR5pp6 stability in the manuscript:

“The observed line broadening of arrestin2 in the presence of phosphopeptide must be a result of increased protein motions and is not caused by a decrease in protein stability, since the melting temperature of arrestin2 in the absence and presence of phosphopeptide are identical (56.9 ± 0.1 °C)”.

(3) At one point, the authors added an excess fully phosphorylated CCR5 phosphopeptide (CCR5pp6). Does the phosphopeptide rescue resolution of arrestin2 (NH or methyl) to the point where interaction dynamics with clathrin (CLTC NTD) are now more evident on the arrestin2 surface? 

Unfortunately, when we titrate arrestin2 with CCR5pp6 (please see Isaikina & Petrovic et. al, Mol. Cell, 2023 for more details), the arrestin2 resonances undergo fast-to-intermediate exchange upon binding. In the presence of phosphopeptide excess, very few resonances remain, the majority of which are in the disordered region, including resonances from the clathrin-binding loop. Due to the peak overlap, we could not unambiguously assign arrestin2 resonances in the bound state, which precluded our assessment of the arrestin2-clathrin interaction in the presence of phosphopeptide. We have made this now clearer in the paragraph ‘The arrestin2-clathrin interaction is independent of arrestin2 activation’

“Due to significant line broadening and peak overlap of the arrestin2 resonances upon phosphopeptide addition, the influence of arrestin activation on the clathrin interaction could not be detected on either backbone or methyl resonances”.

(4) Once phosphopeptide activates arrestin-2 and AP2 binds, can phosphopeptide be exchanged off? In this case, would it be possible for the activated arrestin-2 AP2 complex to re-engage a new (phosphorylated) receptor?

This would be an interesting mechanism. In principle, this should be possible as long as the other (phosphorylated) receptor outcompetes the initial phosphopeptide with higher affinity towards the binding site. However, we do not have experiments to assess this process directly. Therefore, we rather wish not to further speculate.

(5) Did the authors ever try SEC measurements of arrestin-2 + AP2beta2+CCR5pp6 with and without PIP2, and with and without clathrin (CLTC NTD? The question becomes what the active complex is and how PIP2 modulates this cascade of complexation events in class B receptors. 

We thank the referee for this question. Indeed, we tested whether PIP2 can stabilize the arrestin2•CCR5pp6•AP2 complex by SEC experiments. Unfortunately, the addition of PIP2 increased the formation of arrestin2 dimers and higher oligomers, presumably due to the presence of additional charges. The resolution of SEC experiments was not sufficient to distinguish arrestin2 in oligomeric form or in arrestin2•CCR5pp6•AP2 complex. We now mention this in the text: 

“We also attempted to stabilize the arrestin2-AP2b2-phosphopetide complex through the addition of PIP2, which can stabilize arrestin complexes with the receptor (Janetzko et al., 2022). The addition of PIP2 increased the formation of arrestin2 dimers and higher oligomers, presumably due to the presence of additional charges. Unfortunately, the resolution of the SEC experiments was not sufficient to separate the arrestin2 oligomers from complexes with AP2b2”.

Reviewer #3 (Public review): 

Summary: 

Overall, this is a well-done study, and the conclusions are largely supported by the data, which will be of interest to the field. 

Strengths: 

(1) The strengths of this study include experiments with solution NMR that can resolve high-resolution interactions of the highly flexible C-terminal tail of arr2 with clathrin and AP2. Although mainly confirmatory in defining the arr2 CBL 376LIELD380 as the clathrin binding site, the use of the NMR is of high interest (Figure 1). The 15N-labeled CLTC-NTD experiment with arr2 titrations reveals a span from 39-108 that mediates an arr2 interaction, which corroborates previous crystal data, but does not reveal a second area in CLTC-NTD that in previous crystal structures was observed to interact with arr2.

(2) SEC and NMR data suggest that full-length arr2 (1-418) binding with the 2-adaptin subunit of AP2 is enhanced in the presence of CCR5 phospho-peptides (Figure 3). The pp6 peptide shows the highest degree of arr2 activation and 2-adaptin binding, compared to less phosphorylated peptides or not phosphorylated at all. It is interesting that the arr2 interaction with CLTC NTD and pp6 cannot be detected using the SEC approach, further suggesting that clathrin binding is not dependent on arrestin activation. Overall, the data suggest that receptor activation promotes arrestin binding to AP2, not clathrin, suggesting the AP2 interaction is necessary for CCR5 endocytosis. 

(3) To validate the solid biophysical data, the authors pursue validation experiments in a HeLa cell model by confocal microscopy. This requires transient transfection of tagged receptor (CCR5-Flag) and arr2 (arr2-YFP). CCR5 displays a "class B"-like behavior in that arr2 is rapidly recruited to the receptor at the plasma membrane upon agonist activation, which forms a stable complex that internalizes into endosomes (Figure 4). The data suggest that complex internalization is dependent on AP2 binding, not clathrin (Figure 5). 

We thank the referee for the careful and encouraging evaluation of our work. We appreciate the recognition of the solidity of our data and the support for our conclusions regarding the distinct roles of AP2 and clathrin in arrestin-mediated receptor internalization.

Weaknesses:

The interaction of truncated arr2 (1-393) was not impacted by CCR5 phospho-peptide pp6, suggesting the interaction with clathrin is not dependent on arrestin activation (Figure 2). This raises some questions.

We thank the referee for raising this concern, as we were also surprised by the discovery that the interaction does not depend on arrestin activation. However, the NMR data clearly show at atomic resolution that arrestin activation does not influence the interaction with clathrin in vitro. Evolutionary, the arrestin-clathrin interaction appears not to be conserved as the visual arrestin completely lacks a clathrin-binding motif. For that reason, we believe that the weak arrestin-clathrin interaction provides more of a supportive role during the internalization rather than the regulatory interaction with AP2, which requires and quantitatively depends on the arrestin2 activation. We have reflected on this in the Discussion:

“Although the generalization of this mechanism from CCR5 to other arr-class B receptors has to be explored further, it is indirectly corroborated in the visual rhodopsin-arrestin1 system. The arr-class B receptor rhodopsin (Isaikina et al., 2023) also undergoes CME (Moaven et al., 2013) with arrestin1 harboring the conserved AP2 binding motif, but missing the clathrinbinding motif (Figure 1-figure supplement 1A)”.

Overall, the data are solid, but for added rigor, can these experiments be repeated without tagged receptor and/or arr2? My concern stems from the fact that the stability of the interaction between arr2 and the receptor may be related to the position of the tags.

We thank the referee for this suggestion, which refers to the cellular experiments; the biophysical experiments were carried out without tags. To eliminate the possibility of tags contributing to receptor-arrestin2 binding in the cellular experiments, we also performed the experiments in the presence of CCR5 antagonist [5P12]CCL5 (Figure 4). These data show that in the case of inactive CCR5, arrestin2 is not recruited to CCR5, nor does it form internalization complexes, which would be the case if the tags were increasing the receptorarrestin interaction. In contrast, if the tags were decreasing the interaction, we would not expect such a strong internalization. As indicated below, we have also attempted to perform our cellular experiments using an N-terminally SNAP-tagged CCR5. Unfortunately, this construct did not express in HeLa cells indicating that SNAP-CCR5 was either toxic or degraded.

Reviewing Editor Comments: 

Overall, the reviewers did not suggest much by way of additional experiments. They do suggest several aspects of the manuscript that would benefit from further clarification. 

Reviewer #1 (Recommendations for the authors): 

(1) The distinction between arrestin 2S and arrestin 2L as relates to the canonical and non-canonical clathrin binding sites would benefit from clarification, particularly because the second binding site depends on the splice variant. This is something that some readers may not be familiar with (particularly young ones that are hopefully part of the intended readership).

We thank the referee for this suggestion. We would like to emphasize that in our work, only the long arrestin2 splice variant was used, which contains both binding sites. We have now introduced the splice variants and their relation to the clathrin binding sites in the text. 

In section ‘Localizing and quantifying the arrestin2-clathrin interaction by NMR spectroscopy’:

“Clathrin and arrestin interact in their basal state (Goodman et al., 1996), and a structure of a complex between arrestin2 and the clathrin heavy chain N-terminal domain (residues 1-363, named clathrin-N in the following) has been solved by X-ray crystallography (PDB:3GD1) in the absence of an arrestin2-activating phosphopeptide (Kang et al., 2009). This structure (Figure 1-figure supplement 1B) suggests a 2:1 binding model between arrestin2 and clathrinN. The first interaction (site I) is observed between the ³⁷⁶LIELD³⁸⁰ clathrin-binding motif of the arrestin2 CBL and the edge of the first two β-sheet blades of clathrin-N, whereas the second interaction (site II) occurs between arrestin2 residues ³³⁴LLGDLA³³⁹ and the 4th and 5th blade of clathrin-N. The latter arrestin interaction site is not present in the arrestin2 splice variant arrestin2S (for short) where an 8-amino acid insert (residues 334-341) between β-strands 18 and 19 is removed (Kang et al., 2009)”.

Section ‘The arrestin2-clathrin interaction is independent of arrestin2 activation’

“Figure 2A (left) shows the intensity changes (full spectra in Figure 2-figure supplement 1A) of the clathrin-N ¹H-¹⁵N TROSY resonances [assignments transferred from BMRB, ID:25403 (Zhuo et al., 2015)] upon addition of a one-molar equivalent of arrestin2^1-393. A significant intensity reduction due to line broadening is detected for clathrin-N residues 39-40, 48-50, 62-72, 83-90, 101-106, and 108. These residues form a clearly defined binding region at the edges of blade 1 and blade 2 of clathrin-N (Figure 2A, right), which corresponds to interaction site I in the 3GD1 crystal structure, involving the conserved arrestin2 ³⁷⁶LIELD³⁸⁰ motif. However, no significant signal attenuation was observed for clathrin-N residues in blade 4 and blade 5, which would correspond to the crystal interaction site II with arrestin2 residues ³³⁴LLGDLA³³⁹ that are absent in the arrestin2S splice variant. Thus only one arrestin2 binding site in clathrin-N is detected in solution, and site II of the crystal structure may be a result of crystal packing”.

(2) Acronym density is high throughout. While many are standard in the clathrin literature, this could hinder accessibility for readers with a GPCR or arrestin focus.

We agree with the referee. The acronyms were hard to avoid. The most non-obvious acronym seems ‘CLTC-NTD’ for the N-terminal domain of the clathrin heavy chain, which uses the non-obvious, but common gene name CLTC for the clathrin heavy chain. We have now replaced ‘CLTC-NTD’ by ‘clathrin-N’ and hope that this makes the text easier to follow.

(3) The NMR section, while impressive in scope, had writing that was more difficult to follow than the rest. I am curious what percentage of resonance could be assigned. 

We apologize if the NMR sections of this manuscript were unclear. We attempted to provide a very detailed description of the experimental setup and the spectral results. Being experienced NMR spectroscopists, we have tried very hard to obtain good 3D triple resonance spectra for assignments, but their sensitivity is very low. We believe that this is due to the microsecond dynamics present in the system, which makes the heteronuclear transfers inefficient. So far, we have been able to assign ~30% of the visible arrestin2 resonances. We are still validating the assignments and are working on the analysis and an explanation for this arrestin2 behavior. Therefore, at this point, we want to refrain from stronger statements besides that considerable intrinsic microsecond dynamics is impeding the assignment process.

(4) It may be worth noting in the main text that truncated arrestins have slightly higher basal activation. I was curious why the truncated arrestin was not chosen for the AP2 NMR titrations. Presumably, an effect would be more likely to be seen.

While some truncated arrestin2 variants (comprising residues 1-382 or 1-360) indeed show higher basal activity than the full-length arrestin2, they typically completely lack the b20 strand (residues 386-390), which is crucial for the formation of a parallel b-sheet with strand b1, and whose release governs arrestin activation. Our truncated arrestin2 construct comprises residues 1-393 and contains strand b20. In our experience, no significant difference in basal activity, as assessed by Fab30 binding, was detected for arrestin2^1-393 and arrestin2^1-418 (Author response image 1).

Author response image 1.

SEC profiles showing arrestin2^1–393 (left) and arrestin2^1-418 (right) activation by the CCR5pp6 phosphopeptide as assayed by Fab30 binding. The active ternary arrestin2-phosphopeptide-Fab30 complex elutes at a lower volume than the inactive apo arrestin2 or the binary arrestin2-phosphopeptide complex. Both arrestin2 constructs are activated by the phosphopeptide to a similar level as assessed by the integrated SEC volumes.

We want to emphasize that we used full-length arrestin2^1-418 in order to assess the AP2 interaction, as the crystal structure of arrestin2 peptide-AP2 (PDB:2IV8) shows residues past the residue 393 involved in binding.

PDB codes are currently not accompanied by corresponding literature citations throughout. Please add these. 

Thank you for this suggestion. In the manuscript, we were careful to provide the full literature citation the first time each PDB code is mentioned. To avoid redundancy and maintain clarity, we rather do not want to repeat the citations with every subsequent mentioning of the PDB code.

(5) The AlphaFold model could benefit from a more transparent discussion of prediction confidence and caveats. The younger crowd (part of the presumed intended readership) tends to be more certain that computational output is 'true'. Figure 1A shows long loops that are likely regions of low confidence in the prediction. Displaying expected disordered regions as transparent or color-coded would help highlight these as flexible rather than stable, especially for that same younger readership. 

We need to explain that the AlphaFold model of arrestin2 was only used to visualize the clathrin-binding loop and the 344-loop of the arrestin2 C-domain, which are not detected in the available apo bovine (PDB:1G4M) and apo human (PDB:8AS4) arrestin2 crystal structures. However, the AlphaFold model of arrestin2 is basically identical to the crystal structures in the regions that are visible in the crystal structures. We have clarified this now in the caption to Figure 1.

“The model was used to visualize the clathrin-binding loop and the 344-loop of the arrestin2 C-domain, which are not detected in the available crystal structures of apo arrestin2 [bovine: PDB 1G4M (Han et al., 2001), human: PDB 8AS4 (Isaikina et al., 2023)]. In the other structured regions, the model is virtually identical to the crystal structures”.

(6) Several figure panels were difficult to interpret due to their small size. Especially microscopy insets, where I needed to simply trust that the authors were accurately describing the data. Enlarging panels is essential, and this may require separating them into different figures.

We appreciate the referee’s concern regarding figure readability. However, we want to indicate that all our figures are provided as either high-resolution pixel or scalable vector graphics, which allow for zooming in to very fine detail, either electronically or in print. This ensures that microscopy insets and other small panels can be examined clearly when viewed appropriately. We believe the current layout of the figures is necessary to be able to efficiently compare the data between different conditions.

Many figure panels had text size that was too small. Font inconsistencies across figures also stand out. 

We apologize for this. We have now enlarged the font size in the figures and made the styles more consistent.

For Fig. 1F, consider adding individual data points and error bars.

Thank you for this suggestion. However, Figure 1F already contains the individual data points, with colored circles corresponding to the titration condition. As we did not have replicates of the titration, no error bars are shown. However, the close agreement of the theoretical fit with the individual measured data points stemming from different experiments shows that the statistical errors are indeed very small. We have estimated an overall error for the Kd (as indicated in panel F, right) by error propagation based on an estimate of the chemical shift error as obtained in the NMR software POKY (based on spectral noise). 

Reviewer #2 (Recommendations for the authors):

(1) I don't observe two overlapping spectra of Arrestin2 (1393) +/- CLTC NTD in Supplementary Figure 1.

As explained above all the spectra are shown as scalable vector graphics. The overlapping spectra are visible when zoomed in.

(2) I'd be tempted to move the discussion of class A and class B GPCRs and their presumed differences to the intro and then motivate the paper with specific questions.

We appreciate the referee’s suggestion and had a similar idea previously. However, as we do not have data on other class-A or class-B receptors, we rather don’t want to motivate the entire manuscript by this question.

Reviewer #3 (Recommendations for the authors): 

(1) What happens with full-length arr2 (1-418) when the phospho-peptide pp6 is added to the reaction? It's unclear to me that 1-418 would behave the same as 1-393 because the arr2 tail of 1-393 is likely sufficiently mobile to accommodate binding to CLTC NTD. I suggest attempting this experiment for added rigor.

We believe that there is a misunderstanding. The 1-393 and 1-418 constructs differ by the disordered C-terminal tail, which is not involved in the clathrin interaction with the arrestin2 376-380 (LIELD) residues. Accordingly, both 1-393 and 1-418 constructs show almost identical interactions with clathrin (Figure 2A and 2C). Moreover, the phospho-activated arrestin2^1-393 (Figure 2B) interacts identically with clathrin as inactive arrestin2^1-393 and inactive arrestin2^1-418. We believe that this comparison is sufficient for the conclusion that arrestin activation does not play a role in arrestin-clathrin binding.

(2) If the tags were moved to the N-terminus of the receptor and/or arr2, I wonder if the complex is as stable (Figure 4)? 

We thank the referee for their suggestion. We have indeed attempted to perform our experiments using an N-terminally SNAP-tagged CCR5. Unfortunately, this construct did not express in the HeLa cells indicating that SNAP-CCR5 was either toxic or degraded. Unfortunately, as the lab is closing due to the retirement of the PI, we are not able to repeat these experiments with further differently positioned tags. We refer also to our answer above that the experiments with the antagonist [5P12]CCL5 present a certain control.

(3) A biochemical assay to measure receptor internalization, in addition to the cell biological approach (Figure 5), would add additional rigor to the study and conclusions.

We tried to measure internalization using a biochemical approach. We tried to pull-down CCR5 from HeLa cells and assess arrestin binding. Unfortunately, even using different buffer conditions, we found that CCR5 was aggregating once solubilized from membranes, preventing us from doing this analysis. We had a similar problem when we exogenously expressed CCR5 in insect cells for purification purposes. We have long experience with CCR5, and this receptor is very aggregation-prone due to extended charged surfaces, which interact with the chemokines.

As an alternative, and in support of the cellular immunofluorescence assays, we also attempted to obtain internalization data via FACS using a CCR5 surface antibody (CD195 Monoclonal Antibody eBioT21/8). CD195 recognizes the N-terminus of the receptor. Unfortunately, the presence of the chemokine ligand (~ 8 kDa) interferes with antibody binding, precluding the quantitative biochemical assessment of the arrestin2 mutants on the CCR5 internalization.

For these reasons, we were particularly careful to quantify CCR5 internalization from the immunofluorescence microscopy data using colocalization coefficients as well as puncta counting (Figure 4+5).

Author response:

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

Reviewing Editor Comments:

(A) Revisions related to the first part, regarding data mining and curation:

(1) One question that arises with the part of the manuscript that discusses the identification and classification of ion channels is whether these will be made available to the wider public. For the 419 human sequences, making a small database to share this result so that these sequences can be easily searched and downloaded would be desirable. There are a variety of acceptable formats for this: GitHub/figshare/zenodo/university website that allows a wider community to access their hard work. Providing such a resource would greatly expand the impact of this paper. The same question can be asked of the 48,000+ ion channels from diverse organisms.

We thank the reviewer for providing this important feedback. While the long term plan is to provide access to these sequences and annotations through a knowledge base resource like Pharos, we agree with the comments that it would be beneficial to have these sequences made available with the manuscript as well. We have compiled 3 fasta files containing the following: 1) Full length sequences for the curated 419 ion channel sequences. 2) Pore containing domain sequences for the 343 pore domain containing human ion channel sequences. 3) All the identified orthologs for the human ion channels.

For each sequence in these files, we have extended the ID line to include the most pertinent annotation information to make it readily available. For example, the id>sp|P48995|TRPC1_HUMAN|TRP:VGIC--TRP-TRPC|pore-forming|dom:387-637 provides the classification, unit and domain bounds for the human TRPC1 in the fasta file itself.

These files have been uploaded to Zenodo and are available for download with doi 10.5281/zenodo.16232527. We have included this in the Data Availability statement of the manuscript as well.

(2) Regarding the 48,000+ sequences, what checks have been done to confirm that they all represent bona fide, full-length ion channel sequences? Uniprot contains a good deal of unreviewed sequences, especially from single-celled organisms. The process by which true orthologues were identified and extraneous hits discarded should be discussed in more detail, and all inclusion criteria should be described and justified, clearly illustrating that the risk of gene duplicates and fragments in this final set of ion channel orthologues has been avoided. Related to this, does this analysis include or exclude isoforms?

We thank the reviewer for raising this important point. Our selection of curated proteomes and the KinOrtho pipeline for orthology detection returns, up to an extent, reliable orthologous sequence sets. In brief, our database sequences are retrieved from full proteomes that only include proteins that are part of an official proteome release. Thus, they are mapped from a reference genome to ensure species-specific relevance and avoid redundancy. The >1500 proteomes in this analysis were selected based on their wider use in other orthology detection pipelines like OMA and InParanoid. Our orthology detection pipeline, KinOrtho, performs a fulllength and a domain-based orthology detection which ensures that the orthologous relationships are being defined based on the pore-domain sequence similarity. 

But we agree with the reviewer that this might leave room for extraneous, fragments or misannotated sequences to be included in our results. Taking this into careful consideration, we have expanded our sequence validation pipeline to include additional checks such as checking the uniport entry type, protein existence evidence and sequence level checks such as evaluating the compositional bias, non-standard codons and sequence lengths. These validation steps are now described in detail in the Methods section under orthology analysis (lines 768-808). All the originally listed orthologous sequences passed this validation pipeline and thus provide additional confidence that they are bona fide full length ion channel sequences.

We have also expanded this section (lines 758 – 766) to provide more details of the KinOrtho pipeline for orthology detection, which is a previously published method used for orthology detection in kinases by our lab.

Finally, our orthology analysis excludes isoforms and only spans the primary canonical sequences that are part of the UniProt Proteomes annotated sequence set. The isoforms that are generally available in UniProt Proteomes in a separate file named *_additional.fasta were not included in this analysis.

(3) The decision to show the families of ion channels in Figure 1 as pie charts within a UMAP embedding is intriguing but somewhat non-intuitive and difficult to understand. Illustrating these results with a standard tree-like visualization of the relationship of these channels to each other would be preferred.

We appreciate the feedback provided by the reviewer, and understand that a standard tree-like visualization would be much easier to interpret and familiar than a bubble chart based on UMAP embeddings. However, we opted to use the bubble chart for the following reasons:

Low sequence similarity: the 419 human ICs share very minimal sequence similarity, falling in the twilight zone or lower ( Dolittle, 1992; PMID:1339026). Thus, traditional multiple sequence alignment and phylogenetic reconstruction methods perform very poorly and generate unreliable or even misleading results. To explore the practicality of this option, we pursued performing a multiple sequence alignment of just 3 of the possibly related IC families as suggested by reviewer 2 (CALHM, Pannexins, and Connexins) using the state of the art structure based sequence alignment method Foldmason (doi: https://doi.org/10.1101/2024.08.01.606130). Even then, the sequence alignment and the resulting tree for just these 3 families were poor and unreliable, as illustrated in the attached Author response Image 2.

Protein embeddings based clustering: Novel LLM based approaches such as the protein language model embeddings offer ways to overcome these limitations by capturing sequence, structure, function and evolutionary properties in a high-dimensional space. Thus, we employed this model using DEDAL followed by UMAP for dimensionality reduction, which preserves biologically meaningful local and global relationships.

Abstraction at family level: In Figure 1, we aggregate individual channels into family bubbles with their positions representing the average UMAP coordinates of their members. This offers a balance between an intuitive view of how IC families are distributed in the embedding space and reflects potential functional and evolutionary proximities, while not being impeded by individual IC relationships across families.

We have revised the figure legend (lines 1221 – 1234) with additional description of the visualization and the process used to generate it, and the manuscript text (lines 248-270) provides the rationale behind the selection of this method.

(4) A strength of this paper is the visualization of 'dark' ion channels. However, throughout the paper, this could be emphasized more as the key advantage of this approach and how this or similar approaches could be used for other families of proteins. Specifically, in the initial statement describing 'light' vs 'dark channels', the importance of this distinction and the historical preference in science to study that which has already been studied can be discussed more, even including references to other studies that take this kind of approach. An example of a relevant reference here is to the Structural Genomics Consortium and its goals to achieve structures of proteins for which functions may not be well-characterized. Clarifying these motivations throughout the entire paper would strengthen it considerably.

We thank the reviewer for this constructive comment and agree that highlighting the strength of visualizing “dark” channels and prioritizing them for future studies would strengthen the paper. As suggested, we have revised the text throughout the paper (lines 84-89, 176-180) to contextualize and emphasize this distinction. We have also added a reference for the Structural Genomics Consortium, which, along with resources like IDG, has provided significant resources for prioritizing understudied proteins.

(5) Since the authors have generated the UMAP visualization of the channome, it would be interesting to understand how the human vs orthologue gene sets compare in this space.

We appreciate the reviewer’s input. It is an interesting idea to explore the UMAP embedding space for the human ICs along with their orthologs. The large number of orthologous sequences (>37,000) would certainly impose a computational challenge to generate embeddings-based pairwise alignments across all of them. Downstream dimensionality reduction from such a large set and the subsequent visualization would also suffer from accuracy and interpretability concerns. However, to follow up on the reviewer’s comments, we selected orthologous sequences from a subset of 12 model organisms spanning all taxa (such as mouse, zebrafish, fruit fly, C. elegans, A. thaliana, S. cerevisiae, E. coli, etc.).This increased the number of sequences for analysis to 1094 from 343, which is still manageable for UMAP. Using the exact same method, we generated the UMAP embeddings plot for this set as shown below. 

Author response image 1.

UMAP embeddings of the human ICs alongside orthologs from 12 model organisms

As shown above, we observed that each orthologous set forms tight, well-defined clusters, preserving local relationships among closely related sequences. For example, a large number of VGICs cluster more closely together compared to Supplementary Figure 1 (with only the human ICs). However, families that were previously distant from others now appear to be even more scattered or pushed further away, indicating a loss of global structure. This pattern suggests that while local distances are well preserved, the global topology of the embedding space could be compromised. Moreover, we find that the placement of ICs with respect to other families is highly sensitive to the parameter choices (e.g., n_neighbors and min_dist), an issue which we did not encounter when using only the human IC sequences. The inclusion of a large number of orthologous sequences that are highly similar to a single human IC but dissimilar to others skews the embedding space, emphasizing local structure at the expense of global relationships.

Since UMAP and similar dimensionality reduction methods prioritize local over global structure, the resulting embeddings accurately reflect strong ortholog clustering but obscure broader interfamily relationships. Consequently, interpreting the spatial arrangement of human IC families with respect to one another becomes unreliable. We have made this plot available as part of this response, and anyone interested can access this in the response document.   

(6) Figure 1 should say more clearly that this is an analysis of the human gene set and include more of the information in the text: 419 human ion channel sequences, 75 sequences previously unidentified, 4 major groups and 55 families, 62 outliers, etc. Clearer visualizations of these categories and numbers within the UMAP (and newly included tree) visualization would help guide the reader to better understand these results. Specifically, which are the 75 previously unidentified sequences?

We thank the reviewer for the comments. To address this, we have revised Figure 1 and added more information, including a clear header that states that these are only human IC sets, numbers showing the total number of ICs, and the number of ICs in each group. We have further included new Supplementary Figure 2 and Supplementary Table 2, which show the overlap of IC sequences across the different resources. Supplementary Figure 2 is an upset plot that provides a snapshot of the overlap between curated human ICs in this study compared to KEGG, GtoP, and Pharos. Supplementary Table 2 provides more details on this overlap by listing, for each human IC, whether they are curated as an IC in the 3 IC annotation resources. We believe these additions should provide all the information, including the unidentified sequences we are adding to this resource.

(7) Overall, the manuscript needs to provide a clearer description of the need for a better-curated sequence database of ion channels, as well as how existing resources fall short.

We thank the reviewer for pointing out this important gap in the description. As suggested, we have revised the text thoroughly in the Introduction section to address this comment. Specifically, we have added sections to describe existing resources at sequence and structure levels that currently provide details and/or classification of human ion channels. Then, we highlight the facts that these resources are missing some characterized pore-containing ICs, do not include any information on auxiliary channels, and lack a holistic evolutionary perspective, which raises the need for a better-curated database of ion channels. Please refer to lines 57-63, 73-79, and 95 – 119 for these changes and additions.

(8) Some of the analysis pipeline is unclear. Specifically, the RAG analysis seems critical, but it is unclear how this works - is it on top of the GPT framework and recursively inquires about the answer to prompts? Some example prompts would be useful to understand this.

We thank the reviewer for highlighting this gap in explanation. We understand that the details provided in the Methods and Supplementary Figure 1 may not have sufficiently explained the pipeline, and are missing some important details. The RAG pipeline leverages vector-based retrieval integrated with OpenAI’s GPT-4o model to systematically search literature and generate evidence-based answers. The process is as follows:

Literature sources (PubMed articles) relevant to the annotated ion channels were converted into vector representations stored in a Qdrant database.

Queries constructed from the annotated IC dataset were submitted to the vector database, retrieving contextually relevant literature segments.

Retrieved contexts served as inputs to the GPT-4o model, which produced structured JSON-formatted responses containing direct evidence regarding ion selectivity and gating mechanisms, along with associated confidence scores.

To clarify this further, we have rewritten the relevant subsection in lines 649 - 718. Now, this section provides a detailed description of the RAG pipeline. Also, we have improved Supplementary Figure 1 to provide a clearer description of the pipeline. We have also provided an example prompt template to illustrate the query. These additions clarify how the pipeline functions and demonstrate its practical utility for IC annotation.

(9) The existence of 76 auxiliary non-pore containing 'ion channel' genes in this analysis is a little confusing, as it seems a part of the pipeline is looking for pore-lining residues. Furthermore, how many of these are picked up in the larger orthologues search? Are these harder to perform checks on to ensure that they are indeed ion channel genes? A further discussion of the choice to include these auxiliary sequences would be relevant. This could just be further discussion of the literature that has decided to do this in the past.

We thank the reviewer for this comment, and agree that further clarification of our selection and definition of auxiliary IC sequences would be helpful. As the reviewer has pointed out, one of the annotation pipeline steps is indeed looking for the pore-lining residues. Any sequences that do not have a pore-containing domain are then considered to be auxiliary, and we search for additional evidence of their binding with one of the annotated pore-containing ICs. If such evidence is not found in the literature, we remove them from our curated IC list. 

In response to the above comment, we have revised the manuscript text to provide these details. In the Introduction section, we have added references to previous literature that have described auxiliary ICs and also pointed out that the existing ion channel resources do not account for such auxiliary channels (lines 73-79, 107-108,148-149). We have also expanded the Methods section to describe the selection and definition of auxiliary channels (lines 640-646).

With regards to the orthology analysis, since auxiliary channels do not have a pore domain, and our orthology pipeline requires a pore domain similarity search and hit, we did not include them in this part of the analysis. We have clarified the text in the Results section to ensure this is communicated properly throughout the manuscript (lines 212-215, 260-263). 

(10) Why are only evolutionary relationships between rat, mouse, and human shown in Figure 3A? These species are all close on the evolutionary timeline.

We thank the reviewer for this comment. Figure 3A currently provides a high-level evolutionary relationship across the 6 human CALHM members as a pretext for the pattern based Bayesian analysis. However, since this analysis is based on a wider set of orthologs that span taxa, we agree that a larger tree that includes more orthologs is warranted.

We have now revised Figure 3A to include an expanded tree that includes 83 orthologs from all 6 human CALHM members spanning 14 organisms from different taxa, ranging from mammals, fishes, birds, nematodes, and cnidarians. The overall structure of the tree is still consistent with 2 major clades as before, with CALHM 1 and 3 in the first clade and CALHM 2,4,5, and 6 in the second clade, with good branch support.

(B) Revisions related to the second part, regarding the analysis of CAHLM channel mutations:

(1) It would strengthen the manuscript if it included additional discussion and references to show that previous methods to analyze conserved residues in CALHM were significantly lacking. What results would previous methods give, and why was this not enough? Were there just not enough identified CALHM orthologues to give strong signals in conservation analysis? Also, the amino acid conservation between CLHM-1 and CALHM1 is extremely low. Thus, there are other CALHM orthologs that give strong signals in conservation analysis. There are ~6 papers that perform in-depth analysis of the role of conserved residues in the gating of CALHM channels (human and C. elegans) that were not cited (Ma et al, Am J Physiol Cell Physiol, 2025; Syrjanen et al, Nat Commun, 2023; Danielli et al, EMBO J, 2023; Kwon et al, Mol Cells, 2021; Tanis et al, Am J Physiol Cell Physiol, 2017; Tanis et al, J Neurosci, 2013; Ma et al, PNAS, 2013) - these data needs to be discussed in the context of the present work.

We thank the reviewer for the comment and agree that these are excellent studies that have advanced understanding of conserved residues in CALHM gating. While their analyses compared a limited set of sequences, focusing on residues conserved in specific CALHM homologs or species like C. elegans, our analysis encompasses thousands of sequences across the entire CALHM family, allowing us to identify residues conserved across all family members over evolution. We also coupled this sequence analysis with hypotheses derived from our published structural studies (Choi et al., Nature, 2019), which highlighted the NTH/S1 region as a critical element in channel gating. Based on this, we focused on evolutionarily conserved residues in the S1–S2 linker and at the interface of S1 with the rest of the TMD, reasoning that if S1 movement is essential for gating, these two structural elements (acting as a hinge and stabilizing interface, respectively) would be key determinants of the conformational dynamics of S1. These regions have been largely overlooked in previous studies. As a result, the residues highlighted in our study do not overlap with those previously reported but instead provide complementary insights into gating mechanisms in this unique channel family. Together, our study and the published literature suggest that many regions and residues in CALHM proteins are critical for gating: while some are conserved across the entire family evolutionarily, others appear conserved only within certain species or subfamilies.

To address the reviewer’s comment, and to highlight the points mentioned above, we have added a brief discussion of these studies and the relevant citations in the revised manuscript (lines 378– 385, 563–576).

(2) Whereas the current-voltage relations for WT channels are clearly displayed, the data that is shown for the mutants does not allow for determining if their gating properties are indeed different than WT.

First, the current amplitudes for the mutants were quantified at just one voltage, which makes it impossible to determine if their voltage-dependence was different than WT, which would be a strong indicator for an effect in gating. Current-voltage relations as done for the WT channels should be included for at least some key mutations, which should include additional relevant controls like the use of Gd3+ as an inhibitor to rule out the contribution of some endogenous currents.

We thank the reviewer for this comment. To address this, we performed additional experiments using a multi-step pulse protocol to obtain current-voltage relations for WT CALHM1, CALHM1(I109W), WT CALHM6, and CALHM6(W113A). Our initial two-step protocol (−80 mV and +120 mV) covers both the physiological voltage range and the extended range commonly used in biophysical characterization of ion channels. Most mutants did not exhibit channel activation even within this broad range. We therefore focused on the three mutants that did show substantial activation to perform full I–V analysis as suggested. In all groups, currents activated at 37 °C were significantly inhibited by Gd³⁺, consistent with published reports (Ma et al., AJP 2025; Danielli et al., EMBO J 2023; Syrjänen et al., Nat Commun 2023). Notably, for CALHM6(Y51A), while this mutation did not significantly alter current amplitudes at positive membrane potentials, it markedly reduced currents at negative potentials, rendering the channel outwardly rectifying and altering its voltage dependence. These new data are incorporated into Figure 5 (panels A–O) and discussed in the manuscript. Figure 5 now also shows current amplitudes at both +120 mV and −80 mV in 0 mM Ca²⁺ at 37 °C to facilitate direct comparison between WT and mutants. The previous data at 5 mM Ca²⁺ and 0 mM Ca²⁺ at 22 °C have been moved to Supplementary Figure 5 as requested.

Second, it is unclear whether the three experimental conditions (5 mM Ca²⁺, and 0 Ca²⁺, at 22 and 37C) were measured in the same cell in each experiment, or if they represent different experiments. This should be clarified. If measurements at each condition were done in the same experiment, direct comparison between the three conditions within each individual experiment could further help identify mutations with altered gating.

We thank the reviewer for pointing this out and apologize for the confusion. All three conditions (5 mM Ca²⁺ at 22 °C, 0 mM Ca²⁺ at 22 °C, and 0 mM Ca²⁺ at 37 °C) were sequentially measured in the same cell within each experiment. The currents were then averaged across cells and plotted for each group.

Third, in line 334, the authors state that "expression levels of wild-type proteins and mutants are comparable." However, Western blots showing CALHM protein abundance (Supplementary Fig. 3) are not of acceptable quality; in the top blot, WT CALHM1 appears too dim, representative blots were not shown for all mutants, and individual data points should be included on the group data quantitation of the blots, together with a statistical test comparing mutants with the WT control.

We thank the reviewer for the comment and agree that representative blots were not shown for all mutants. Supplementary Figure 4 (previously Supplementary Figure 3) has been updated to include representative blots for all mutants, individual data points in the quantification, and statistical tests comparing each mutant to the WT control.

A more serious concern is that the total protein quantitation is not very informative about the functional impact of mutations in ion channels, because mutations can severely impact channel localization in the plasma membrane without reducing the total protein that is translated. In mammalian cells, CALHM6 is localized to intracellular compartments and only translocates to the plasma membrane in response to an activating stimulus (Danielli et al, EMBO J, 2023). Thus, if CALHM6 is only intracellular, the protein amount would not change, but the measured current would. Abundant intracellular CALHM1 has also been observed in mammalian cells transfected with this protein (Dreses-Werringloer et al., Cell, 2008). Quantitation of surface-biotinylated channels would provide information on whether there are differences between the constructs in relation to surface expression rather than gating. An alternative approach to biotinylation would be to express GFP-tagged constructs in Xenopus oocytes and look for surface expression. This is what has been done in previous CALHM channel studies.

Without evidence for the absence of defects in localization or clear alterations in gating properties, it is not possible to conclude whether mutant channels have altered activity. Does the analysis of sequences provide any testable hypotheses about substitutions with different side chains at the same position in the sequence?

We thank the reviewer for this very important comment. We agree that total protein levels alone do not distinguish between intracellular retention and proper trafficking to the plasma membrane. To address this, we performed surface biotinylation assays for all WT and mutant CALHM1 and CALHM6 constructs to assess their plasma membrane localization. The results show that mutants have either comparable or substantially higher surface expression levels than WT, consistent with the Western blot data. Together, these findings support our original interpretation that the observed differences in electrophysiological currents are not due to trafficking defects but reflect functional effects. These new data are presented in Supplementary Figure 5.

(3) Line 303 - 13 aligned amino acids were conserved across all CALHM homologs - are these also aligned in related connexin and pannexin families? It is likely that cysteines and proline in TM2 are since CALHM channels overall share a lot of similarities with connexins and pannexins (Siebert et al, JBC, 2013). As in line 207, it would be expected that pannexins, connexins, and CALHM channel families would group together. Related to this, see Line 406 - in connexins, there is also a proline kink in TM2 that may play a role in mediating conformational changes between channel states (Ri et al, Biophysical Journal, 1999). This should be discussed.

We thank the reviewer for the suggestion. We attempted a structure based sequence alignment of representative structures from all 3 families (CALHM, connexins and pannexins), but the resulting alignments are very poor and have a lot of gapped regions, making it very difficult to comment on the similarities mentioned in this comment. This is actually expected, as although CALHM, connexins, and pannexins are all considered “large-pore” channels, the TMD arrangement and conformation of CALHM are distinct from those of connexins and pannexins. Below, we have included a snapshot of the alignment at the conserved cysteine regions of the CALHM homologs, along with the resulting tree, which has very low support values and has difficulty placing the connexins properly, making it difficult to interpret.

Author response image 2.

Structure based sequence alignment and phylogenetic analysis of available crystal structures of members from the CALHM, Pannexin and Connexin families. Top: The resulting sequence alignment is very sparse and does not show conservation of residues in the TM regions. The CPC motif with conserved cysteines in CALHM family is shown. Bottom: Phylogenetic tree based on the alignment has low support values making it difficult to interpret.

(4) Line 36 - This work does not have experimental evidence to show that the selected evolutionarily conserved residues alter gating functions.

Our electrophysiology data demonstrate that the selected evolutionarily conserved residues have a major impact on CALHM1 and CALHM6 gating. As shown in Figure 5, mutations at these residues produce two distinct phenotypes: (1) nonconductive channels, and (2) altered voltage dependence, resulting in outward rectification. Importantly, these functional changes occur despite normal total expression and surface trafficking, as confirmed by Western blotting and surface biotinylation (Supplementary Figure 4). These findings indicate that the affected residues are critical for the conformational dynamics underlying channel gating rather than for protein expression or localization.

(5) Line 296-297 - This could also be put in the context of what we already know about CALHM gating. While all cryo EM structures of CALHM channels are in the open state, we still do understand some things about gating mechanism (Tanis et al Am J Physiol Cell Physiol, Cell Physiol 2017; Ma et al Am J Physiol Cell Physiol, Cell Physiol 2025) with the NT modulating voltage dependence and stabilizing closed channel states and the voltage dependent gate being formed by proximal regions of TM1.

Thank you for providing this suggestion. As suggested, we have revised the text to place our findings in the context of current knowledge about CALHM gating and have added the relevant citations (lines 370-373).

(6) Lines 314-315 - Just because residues are conserved does not mean that they play a role in channel gating. These residues could also be important for structure, ion selectivity, etc.

We agree that evolutionary conservation alone does not imply a role in gating. However, our hypothesis derives from the positioning of these conserved residues, and previous studies that have indicated the importance of the NTH/S1 region for channel gating function. More importantly, our electrophysiology data indicate that these conserved residues specifically impact channel gating in CALHM1 and CALHM6. We have revised the text in lines 404-406 to clarify this further.

(7) Line 333 - while CALHM6 is less studied than CALHM1, there is knowledge of its function and gating properties. Should CALHM6 be considered a "dark" channel? The IDG development level in Pharos is Tbio. There have been multiple papers published on this channel (ex: Ebihara et al, J Exp Med, 2010; Kasamatsu et al, J Immunol 2014; Danielli et al, EMBO J, 2023).

We thank the reviewer for noting this important discrepancy. We have updated the text and labels related to CALHM6 to reflect its status as Tbio in the manuscript.

(8) Please cite Jeon et al., (Biochem Biophys Res Commun, 2021), who have already shown temperature-dependence of CALHM1.

Thank you for the comment. We have added the citation.  

(9) It would be helpful to have a schematic showing amino acid residues, TM domains, highlighted residues mutated, etc.

Thank you for the suggestion. We have revised the figure and added labels for the TM domains, and highlighted the mutated residues.

Reviewer #1 (Recommendations for the authors):

(1) Why in the title is 'ion-channels' hyphenated but in the text it is not?

This has been changed.

(2) Line 78: 'Cryo-EM' is not defined before the acronym is used.

This has been fixed.

(3) Typo in line 519: KinOrthto.

This has been fixed.

(4) Capitalizing 'Tree of Life' is a bit strange in section 2 of the results and the Discussion.

We have removed the capitalization as suggested.

(5) In Figure 3 and Supplementary Figure 4A, the gene names in the tree are CAHM and not CALHM - I assume this is an error.

This has been made consistent to CALHM.

(6) Font sizes throughout all figures, with the exception of Figure 1, need to be more legible. The X-axis labels in Figure 2A are hard to read, for example (though I can see that there is also the CAHM/CALHM typo here...). A good rule of thumb is that they should be the same size as the manuscript text. Furthermore, the grey backgrounds of Figure 4 and Figure 5 are off-putting; just having a white background here should be sufficient.

This has been addressed. We have increased the font size in all figures with these revisions. The styling for Figure 4 and 5 has also been made consistent with other figures.

Reviewer #2 (Recommendations for the authors):

(1) Line 36 - This work does not have experimental evidence to show that the selected evolutionarily conserved residues alter gating functions.

Addressed in comment #4 for Part B Revisions related to the second part, regarding the analysis of CAHLM channel mutations above.

(2) Line 168 - should also be Supplemental Table 1.

This has been addressed.

(3) Line 170 - 419 human ion channel sequences were identified and this was an increase of 75 sequences over previous number. Which 75 proteins are these?

This is now shown in Supplementary Figure 2 and Supplementary Table 2. Supplementary Figure 2 shows an Upset plot with the number of sequences that overlap across databases and the novel sequences that we have added as part of this study. The 75 specifically refers to the sequences that were not included in Pharos, which was chosen to refer to this number since it has the highest number of ICs listed out of all the other resources. Further, Supplementary Table 2 now provides a list of individual ICs and whether they were present in each of the 3 databases compared.

(4) Line 289 - Ca2+ (not Ca); other similar mistakes throughout the manuscript

These have been fixed.

(5) Line 291-292 - Please include more about functions for CALHM channels; ex. CALHM1 regulates cortical neuron excitability (Ma et al, PNAS 2012), CLHM-1 regulates locomotion and induces neurodegeneration in C. elegans (Tanis et al. Journal of Neuroscience 2013); see above for references on CALHM6 function.

We have added the functions as suggested.

(6) Line 296-297 - This could also be put in the context of what we already know about CALHM gating. While all cryo EM structures of CALHM channels are in the open state, we still do understand some things about gating mechanism (Tanis et al Am J Physiol Cell Physiol, Cell Physiol 2017; Ma et al Am J Physiol Cell Physiol, Cell Physiol 2025) with the NT modulating voltage dependence and stabilizing closed channel states and the voltage dependent gate being formed by proximal regions of TM1.

Addressed in comment #5 for Part B Revisions related to the second part, regarding the analysis of CAHLM channel mutations above.

(7) Lines 314-315 - Just because residues are conserved does not mean that they play a role in channel gating. These residues could also be important for structure, ion selectivity, etc.

Addressed in comment #6 for Part B Revisions related to the second part, regarding the analysis of CAHLM channel mutations above.

(8) Line 333 - While CALHM6 is less studied than CALHM1, there is knowledge of its function and gating properties. Should CALHM6 be considered a "dark" channel? The IDG development level in Pharos is Tbio. There have been multiple papers published on this channel (ex: Ebihara et al, J Exp Med, 2010; Kasamatsu et al, J Immunol 2014; Danielli et al, EMBO J, 2023).

Addressed in comment #7 for Part B Revisions related to the second part, regarding the analysis of CAHLM channel mutations above.

(9) Line 627 - Do you mean that 5 mM CaCl2 was replaced with 5 mM EGTA in 0 Ca2+ solution?

This is correct.  

(10) Why are only evolutionary relationships between rat, mouse, and human shown in Figure 3A? These species are all close on the evolutionary timeline.

Addressed in comment #10 for Part A Revisions related to the first part, regarding data mining and curation above.

(11) Figure 5 - no need to show the currents at room temperature in the main text since there are robust currents at 37 degrees; this could go into the supplement. Also, please cite Jeon et al. (Biochem Biophys Res Commun, 2021), who have already shown temperature-dependence of CALHM1.

Addressed in comment #8 for Part B Revisions related to the second part, regarding the analysis of CAHLM channel mutations above.

(12) It would be helpful to have a schematic showing amino acid residues, TM domains, highlighted residues mutated etc.

Addressed in comment #9 for Part B Revisions related to the second part, regarding the analysis of CAHLM channel mutations above.

(13) Use of S1-S4 to refer to the transmembrane "segments" is not standard; rather, TM1-TM4 would generally be used to refer to transmembrane domains.

We have used the S1–S4 helix notation to maintain consistency with the nomenclature employed in our previous study (Choi et al., Nature, 2019).

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review): 

The manuscript by Ivan et al aimed to identify epitopes on the Abeta peptide for a large set of anti-Abeta antibodies, including clinically relevant antibodies. The experimental work was well done and required a major experimental effort, including peptide mutational scanning, affinity determinations, molecular dynamics simulations, IP-MS, WB, and IHC. Therefore, it is of clear interest to the field. The first part of the work is mainly based on an assay in which peptides (15-18-mers) based on the human Abeta sequence, including some containing known PTMs, are immobilized, thus preventing aggregation. Although some results are in agreement with previous experimental structural data (e.g. for 3D6), and some responses to diseaseassociated mutations were different when compared to wild-type sequences (e.g. in the case of Aducanumab) - which may have implications for personalized treatment - I have concerns about the lack of consideration of the contribution of conformation (as in small oligomers and large aggregates) in antibody recognition patterns. The second part of the study used fulllength Abeta in monomeric or aggregated forms to further investigate the differential epitope interaction between Aducanumab, Donanemab, and Lecanemab (Figures 5-7). Interestingly, these results confirmed the expected preference of these antibodies for aggregated Abeta, thus reinforcing my concerns about the conclusions drawn from the results obtained using shorter and immobilized forms of Abeta. Overall, I understand that the work is of interest to the field and should be published without the need for additional experimental data. However, I recommend a thorough revision of the structure of the manuscript in order to make it more focused on the results with the highest impact (second part).

We thank the reviewer for highlighting this critical aspect. Our rationale for beginning with the high-resolution, aggregation-independent peptide microarray was to systematically dissect sequence requirements, including PTMs, truncations, and elongations, at single–amino acid resolution. This platform defines linear epitope preferences without the confounding influence of aggregation and enabled analyses that would not have been technically feasible with fulllength Aβ. This rationale is now clarified in the Introduction (lines 72–77).

At the same time, the physiological relevance of antibody binding can only be assessed in the context of aggregation. Prompted by the reviewer’s comments, we restructured the manuscript to foreground the full-length, aggregation-dependent data (Figures 5–7). These assays demonstrate that Aducanumab preferentially recognizes aggregated peptide over monomers and that pre-adsorption with fibrils, but not monomers, blocks tissue reactivity (lines 585–599; Fig. 5B). They also show that Lecanemab can capture soluble Aβ in CSF by IP-MS (lines 544–547; Fig. 4B, Fig. 6–Supplement 1), and that Donanemab strongly binds low-molecular-weight pyroGlu-Aβ while also recognizing highly aggregated Aβ1-42 (lines 668–684; Fig. 7).

The revised Conclusion now explicitly states the complementarity of the two approaches: microarrays for precise sequence and modification mapping, and full-length aggregation assays for context and physiological relevance (lines 705–714).

Finally, prompted by the reviewer’s feedback, we refined the discussion of therapeutic antibodies to move beyond a descriptive dataset and provide mechanistic clarity. Specifically, the dimerization-supported, valency-dependent binding mode of Aducanumab and the additional structural contributions required for Lecanemab binding to aggregated Aβ are now integrated into the reworked Conclusion (lines 725–741).

Reviewer #2 (Public review):  

This paper investigates binding epitopes of different anti-Abeta antibodies. Background information on the clinical outcome of some of the antibodies in the paper, which might be important for readers to know, is lacking. There are no references to clinical outcomes from antibodies that have been in clinical trials. This paper would be much more complete if the status of the antibodies were included. The binding characteristics of aducanumab, donanemab, and Lecanemab should be compared with data from clinical phase 3 studies. 

Aducanumab was identified at Neurimmune in Switzerland and licensed to Biogen and Eisai. Aducanumab was retracted from the market due to a very high frequency of the side-effect amyloid-related imaging abnormalities-edema (ARIA-E). Gantenerumab was developed by Roche and had two failed phase 3 studies, mainly due to a high frequency of ARIA-E and low efficacy of Abeta clearance. Lecanemab was identified at Uppsala University, humanized by BioArctic, and licensed to Eisai, who performed the clinical studies. Eisai and Biogen are now marketing Lecanemab as Leqembi on the world market. Donanemab was developed by Ely Lilly and is sold in the US as Kisunla. 

We thank the reviewer for this valuable suggestion. In the revised manuscript, we have included a concise overview of the clinical status and outcomes of the therapeutic antibodies in the Introduction. This new section (lines 81–99) summarizes the origins, phase 3 trial outcomes, and current regulatory status of Aducanumab, Lecanemab, and Donanemab, as well as mentioning Gantenerumab as a comparator. Key aspects such as ARIA-E incidence, amyloid clearance efficacy, and regulatory decisions are now referenced to provide the necessary clinical context.

These additions directly link our epitope mapping data with the clinical performance and safety profiles of the antibodies, thereby making the translational implications of our results clearer for both research and therapeutic applications.

Limitations: 

(1) Conclusions are based on Abeta antigens that may not be the primary targets for some conformational antibodies like aducanumab and Lecanemab. There is an absence of binding data for soluble aggregated species.

We thank the reviewer for raising this important point. To address the absence of data on soluble aggregated species, we added IP-MS experiments using pooled human CSF as a physiologically relevant source of endogenous Aβ. Lecanemab enriched several endogenous soluble Aβ variants (Aβ1–40, Aβ1–38, Aβ1–37, Aβ1–39, and Aβ1–42), whereas Aducanumab did not yield detectable signals (Figure 4B; lines 544–547). These results directly distinguish between synthetic and patient-derived Aβ and highlight Lecanemab’s capacity to capture soluble Aβ species under biologically relevant conditions.

(2) Quality controls and characterization of different Abeta species are missing. The authors need to verify if monomers remain monomeric in the blocking studies for Figures 5 and 6. 

We thank the reviewer for this comment. In Figure 5 we show that pre-adsorption with monomeric Aβ1–42 does not prevent Aducanumab binding, whereas fibrillar Aβ1–42 completely abolishes staining, consistent with Aducanumab’s avidity-driven preference for higher-order aggregates.

For Lecanemab (Figure 6), we observed a partial preference for aggregated Aβ1–42 over HFIP-treated monomeric and low-n oligomeric forms. We note, as now stated in the revised manuscript (lines 622–623), that monomeric preparations may partially re-aggregate under blocking conditions, which represents an inherent limitation of such experiments.

To further address this, we performed additional blocking experiments using shorter Aβ peptides, which are less prone to aggregation. These peptides did not block immunohistochemical staining (Figure 6 – Supplement 1), underscoring that both epitope length and conformational state contribute to Lecanemab binding. This conclusion is also consistent with recent data presented at AAIC 2023.

(3) The authors should discuss the limitations of studying synthetic Abeta species and how aggregation might hide or reveal different epitopes. 

We thank the reviewer for this important comment. We now explicitly discuss the limitations of using synthetic Aβ peptides, including that aggregation state can mask or expose epitopes in ways that differ from endogenous species. This discussion has been added in the revised manuscript (lines 737–742).

As noted in our replies to Points (2) and (4) here, and to Reviewer #1, we addressed this experimentally by complementing the high-resolution, aggregation-independent mapping with blocking studies using aggregated and monomeric Aβ preparations, and by validating key findings with IP-MS of human CSF as a physiologically relevant source of soluble Aβ. Together, these complementary approaches mitigate the limitations of synthetic peptides and provide a more comprehensive picture of antibody–Aβ interactions

(4) The authors should elaborate on the differences between synthetic Abeta and patientderived Abeta. There is a potential for different epitopes to be available. 

We thank the reviewer for this comment. In the revised manuscript we now discuss how comparisons between synthetic and patient-derived Aβ species reveal additional, likely conformational epitopes that are not accessible in short or monomeric synthetic forms. To address this directly, we performed IP-MS with pooled human CSF. Lecanemab enriched a diverse set of endogenous soluble Aβ1–X species (Aβ1–40, Aβ1–38, Aβ1–37, Aβ1–39, and Aβ1–42), whereas Aducanumab did not yield measurable pull-down (Figure 4B; lines 544– 547). These results emphasize that patient-derived Aβ displays distinct aggregation dynamics and epitope accessibility.

We have expanded on this point in the Conclusion (lines 737–742), underscoring the

importance of integrating both synthetic and native Aβ sources to capture the full range of antibody targets. 

Reviewer #1 (Recommendations for the authors): 

This revision should prioritize the presentation of results obtained using the full-length Abeta peptide, given its more direct relevance to expected antibody recognition patterns in physiological contexts, and discuss the evidence for using synthetic Abeta. 

We thank the reviewer for this recommendation. The revised manuscript now places stronger emphasis on results obtained with full-length Aβ peptides, particularly in Figures 5–7, which analyze binding preferences across monomeric, oligomeric, and fibrillar states (lines 585–599, 609–623, 668–684). We also expanded the Discussion to outline both the rationale and the limitations of using synthetic Aβ. The microarray approach provides high-resolution, aggregation-independent sequence and modification mapping, but must be complemented by experiments with full-length Aβ1–42 under physiologically relevant conditions, such as IP-MS from CSF (lines 544–547) and blocking in IHC (lines 585–599, 622–623, 684), to capture conformational epitopes and validate functional relevance.

Figure 6. = Please review/better explain the following statement "Lecanemab recognized Aβ140, Aβ1-42, Aβ3-40, Aβ-3-40 and phosphorylated pSer8-Aβ1-40 on CIEF-immunoassay and Bicine-Tris SDS-PAGE/ Western blot, indicating that the Lecanemabbs epitope is located in the N-terminal region of the Aβ sequence". Is it possible that N-truncated peptides do not form aggregates as efficiently as (or conformationally distinct from) full-length ones? 

In the revised text we now clarify that Lecanemab recognized Aβ1-40, Aβ1-42, Aβ3-40, Aβ-340, and phosphorylated pSer8-Aβ1-40 on CIEF-immunoassay (Figure 6A; lines 612–619) and Bicine-Tris SDS-PAGE/Western blot (Figure 6C; lines 639–640). In contrast, shorter Ntruncated variants such as Aβ4-40 and Aβ5-40 did not generate detectable signals under the tested conditions. This is consistent with our initial microarray data (Figure 1), which indicated that Lecanemab binding depends on residues 3–7 of the N-terminus.

On gradient Bistris SDS-PAGE/Western blot, Lecanemab showed a partial but not exclusive preference for aggregated Aβ1-42 over monomeric or low-n oligomeric forms in the HFIPtreated preparation (Figure 6B; lines 632–633). Immunohistochemical detection of Aβ deposits in AD brain sections was efficiently blocked by pre-adsorption with monomerized, oligomeric, or fibrillar Aβ1-42 (Figure 6E; lines 643–645), but not by shorter synthetic peptides such as Aβ1-16, Aβ1-34, or Aβ1-38 (Figure 6 – Supplement 1; lines 654–663).

We also note, as now stated in the Results, that re-aggregation of HFIP-treated Aβ1-42 monomers during incubation cannot be entirely excluded (lines 622–623). Taken together, these experiments indicate that both N-terminal sequence length and conformational context are critical for Lecanemab binding, and that truncated peptides may indeed fail to reproduce the aggregate-associated conformations required for full recognition.

Reviewer #2 (Recommendations for the authors): 

Introduction: 

(1) Include examples of Lecanemab, donanemab, and gantenerumab, along with relevant references. 

We expanded the clinical-context paragraph that already covers Aducanumab, Lecanemab, and Donanemab (lines 81–96) and added Gantenerumab. 

(2) Address why gantenerumab was not included in the study. 

Due to the focus of our current study on antibodies with recently approved or late-stage clinical use (Aducanumab, Donanemab, Lecanemab), Gantenerumab was not included. 

(3) Table 1: Correct the reference for Lecanemab, should be reference 44. 

Table 1 has been updated to correct the Lecanemab reference.

(4) Line 84: Add Uppsala University and Eisai alongside Biogen for Lecanemab. 

Line 84 has been revised to acknowledge Uppsala University and Eisai alongside Biogen for the development of Lecanemab (lines 90–96).

(5) Line 539: Include the reference: "Lecanemab, Aducanumab, and Gantenerumab - Binding Profiles to Different Forms of Amyloid-Beta Might Explain Efficacy and Side Effects in Clinical Trials for Alzheimer's Disease. doi: 10.1007/s13311-022-01308-6. 

We thank the reviewer for drawing attention to this important reference (now cited as Ref. 83) provides a state-of-the-art comparison of binding profiles of Lecanemab, Aducanumab, and Gantenerumab, and we have now properly incorporated it into our manuscript. 

(6) Line 657-659: State that the findings are also applicable to Lecanemab. 

Discrepancies between analysis of the short synthetic fragments and the full-length Abeta are now resolved for Aducanumab and Lecanemab and put into context in the results section and the conclusion lines 725-740. 

(7) Figures 5 and 6: Discuss how to ensure that monomers remain monomers under the study conditions, considering the aggregation-prone nature of Abeta1-42. This aggregation could impact Lecanemab's binding to "monomers." To our knowledge, Lecanemab does not bind to monomers. The binding properties observed diverge from previously described properties for Lecanemab. Explore reasons for these discrepancies and suggest conducting complementary experiments using a solution-based assay, as per Söderberg et al, 2023. In Figure 6, note that Lecanemab is strongly avidity-driven, potentially causing densely packed monomers to expose Abeta as aggregated, affecting binding interpretation on SDS-PAGE. 

We thank the reviewer for this important point. In the revised Results and Discussion we explicitly note that HFIP-treated Aβ1–42 monomers may partially re-aggregate during incubation, which cannot be fully excluded (lines 622–623).

To complement these data, we show that Lecanemab successfully enriched soluble endogenous Aβ species (Aβ1–40, Aβ1–38, Aβ1–37, Aβ1–39, and Aβ1–42) in IP-MS from pooled CSF (lines 544–547; Fig. 4B), demonstrating its ability to bind soluble Aβ under physiologically relevant conditions.

We also now cite the Söderberg et al. (2023, PMID: 36253511) study, which reported weak but detectable binding of Lecanemab to monomeric Aβ (their Fig. 1 and Table 6). This supports our interpretation that Lecanemab is aggregation-sensitive rather than strictly aggregationdependent, in contrast to Aducanumab.

To further address sequence and conformational contributions, we performed blocking experiments with shorter, non-HFIP-treated Aβ peptides (Aβ1–16, Aβ1–34, Aβ1–38). These peptides did not block Lecanemab staining in IHC (lines 654–657; Fig. 6 – Supplement 1), indicating that both extended sequence and conformational context are necessary for recognition.

Finally, our findings are in line with preliminary data by Yamauchi et al. (AAIC 2023, DOI: 10.1002/alz.065104), who proposed that Lecanemab recognizes either a conformational epitope spanning the N-terminus and mid-region, or a structural change in the mid-region induced by the N-terminus.

Author response:

We thank you for your efforts in reviewing our manuscript.  We sincerely appreciate that the reviewers were all enthusiastic about our comparison of native chemical ligation (NCL) and non-canonical amino acid (ncAA) mutagenesis methods for installing acetyl lysine (AcK) in alpha-synuclein, as well as the wide variety of biochemical experiments enabled by our ncAA approach.  We respond to the critiques specific to each reviewer here.

Reviewer #1:

Expressed concern that in vitro studies of effects on membrane binding were not followed up with neurotransmitter trafficking experiments.  While we certainly think that such studies would be interesting, they would presumably require the use of acetylation mimic mutants (Lys-to-Gln mutations), which we would want to validate by comparison to our semi-synthetic proteins with authentic AcK.  Such experiments are planned for a follow-up manuscript, and we will investigate the reviewer’s suggested experiment at that time.

Reviewer #1 Noted that the method of in vitro seeding really reports on the impact of acetylation on the elongation phase of aggregation.  We will clarify this in our revisions.  They also expressed concern that this was different than the role that acetylation would play in seeding cellular aggregation with pre-acetylated fibrils.  We will also acknowledge and clarify this in our revisions.  Having the monomer population acetylated in cells presents technical challenges that might also be addressed with Gln mutant mimics, and we plan to pursue such experiments in the follow-up manuscript noted above.

Reviewer #1 Criticized the fact that the pre-formed fibrils used in seeding would not have the same polymorph as PD or MSA fibrils derived from patient material.  They were also critical of how our cryo-EM structure of AcK80 fibrils related to the PD and MSA polymorphs.  Finally, while the reviewer liked the MS experiments used to quantify acetylation levels from patient samples, they felt that our findings then threw the physiological relevance of our structural and biochemical experiments into question.  We believe that all of these critiques can be addressed by clarifying our purpose.  We are not necessarily trying to claim that our AcK80 fold is populated in health or disease, but that by driving Lys80 acetylation, one could push fibrils to adopt this conformation, which is less aggregation-prone.  A similar argument has been made in investigations of alpha-synuclein glycosylation and phosphorylation.  Our results in Figure 9 imply that this could be done with HDAC8 inhibition.  We will revise the manuscript to make these ideas clearer, while being sure to acknowledge the limitations noted by Reviewer #1.

Reviewer #2:

Expressed concern over our use of SDS micelles for initial investigation of the 12 AcK variants, rather than the phospholipid vesicles used in later FCS and NMR experiments.  We will note this shortcoming in revisions of our manuscript, but we do not believe that using vesicles instead would change the conclusions of these experiments (that only AcK43 produces an effect, and a modest one at that).

We will add additional detail to the figure captions, as requested by Reviewer #2.

Reviewer #2 shared some of the concerns of Reviewer #1 regarding the distinctions of which phase of aggregation we were investigating in our in vitro experiments.  As noted above, we will clarify this language.

Finally, Reviewer #2 stated that “It is not clear from the EM data that the structures of the different lysine acetylated variants are different.”  We feel that it is quite clear from structures in Figure 8 and the EM density maps in Figure S38 that the AcK80 fold is indeed different.  Although the overall polymorphs are somewhat similar to WT, the position of K80 clearly changes upon acetylation, altering the local fold significantly and the global fold more moderately.

Reviewer #3:

Found the results convincing, including the potential therapeutic implications.  The only concern noted was that they found the difficulties in semi-synthesis of AcK-modified alpha-synuclein surprising given that it has been made many times before through NCL.  Indeed, our own laboratory has made alpha-synuclein through NCL, and the yields reported here are in keeping with our own previous results.  However, since NCL did not give higher yields than ncAA methods, and it is significantly easier to scan AcK positions using ncAAs, we felt that ncAAs are the method of choice in this case.  We will clarify this position in the revised manuscript.

In conclusion, on behalf of all authors, I again thank the reviewers for both their positive and negative observations in helping us to improve our manuscript.  We will revise it to strive for greater clarity as we have noted in this letter.

Author response:

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

Joint Public Review:

Summary:

The major issues are the need for more information concerning WNK expression in brain regions and additional confirmation of the role of sortilin on WNT signaling. There is a lack of sufficient evidence supporting sortilin's involvement in insulin- and WNK-dependent GLUT4 regulation. The recommendation is to examine what WNK kinase is selectively expressed in the region of interest and then explore its engagement with the sortilin and GLUT4 pathways. Further identification of components of the WNK/OSr1/SPAK-sortilin pathway that regulate GLUT4 in brain slices or primary neurons will be helpful in confirming the results. The use of knock-down or knock-out models would be helpful to explore the direct interaction of the pathways. Immortalized and primary cells also represent useful models.

Together our results indicate that one or more WNK family members regulate insulin sensitivity.  As all WNK family members are expressed in relevant brain regions, whether the results are due to actions of a single WNK family member or more likely due to their combined impact will be an important question to ask in the future.  

There are multiple publications describing how sortilin is involved in insulin-dependent Glut4 trafficking; thus, we did not further address that issue.  We have added data on an additional action of WNK463 which indicates that it can block association of OSR1 with sortilin.  While these results do not delve further into how sortilin works, they support the conclusion that WNK/OSR1/SPAK can influence insulin-dependent glucose transport via distinct cellular events (AS160, sortilin, Akt) which are WNK463 sensitive.  

Altogether we added 12 new panels of data from new and previously performed experiments and we modified 3 existing subfigures in response to comments.

Weaknesses:

(1) The study used a WNK643 inhibitor as the only tool to manipulate WNK1-4 activity. This inhibitor seems selective; however, it has been reported that it exhibits different efficiency in inhibiting the individual WNK kinases among each other (e.g. PMID: 31017050, PMID: 36712947). Additionally, the authors do not analyze nor report the expression profiles or activity levels of WNK1, WNK2, WNK3, and WNK4 within the relevant brain regions (i.e. hippocampus, cortex, amygdala). Combined, these weaknesses raise concerns about the direct involvement of WNK kinases within the selected brain regions and behavior circuits. It would be beneficial if the authors provided gene profiling for WNK1, 2, 3, and -4 (e.g. using Allen brain atlas). To confirm the observations, the authors should either add results from using other WNK inhibitors or, preferentially, analyze knock-down or knock-out animals/tissue targeting the single kinases.

Thank you for the excellent suggestion to include mRNA data for the four WNKs. We have included a supplementary figure showing expression of WNK1-4 mRNAs in prefrontal cortex and the hippocampus curated from the Allen Brain Atlas. As per the Allen Brain Atlas, all four WNKs are detected in these regions with WNK4 mRNA the most highly expressed followed by WNK2, WNK3 and then WNK1 (Figure S1A).   

With regard to the use of WNK463, we continue to use WNK463 because we have examined its actions in cell lines that only express WNK1, e.g. A549 (Haman Center lung cancer RNA-seq data), and in A549 with WNK1 deleted using CRISPR in which we saw no effects of WNK463 on several assays we use for WNK1 including suppression of autophagy.  WNK463 was reported in the literature to inhibit only the four WNKs out of more than 400 kinases tested, indicating more selectivity than many small molecules used to target other enzymes.  In other cell lines, we also use WNK1 knockdown which replicates the effect of WNK463 (Figure S7A-D). However, in SHSY5Y cells, WNK1 knockdown did not replicate the effect of WNK463 on pAKT levels (Figure S7E-F), suggesting a cooperativity among other WNK family members in neuronal cells. This makes WNK463 an ideal tool to test our hypotheses in this study as it targets all 4 WNKs (WNK1-4).  

(2) The authors do not report any data on whether the global inhibition of WNKs affects insulin levels. Since the authors wish to demonstrate the synergistic effect of simultaneous insulin treatment and WNK1-4 inhibition, such data are missing.

Thank you for this comment. To obtain this information, we treated C57BL/6J mice with WNK463 for 3 days once daily at a dose of 6 mg/kg and then fasted overnight. Plasma insulin levels were measured. Results showed that the plasma insulin levels trended upwards in the WNK463 treated animals compared to the vehicle treated groups but failed to reach any statistical significance. We have now included these data in supplementary figure S5A.

The study discovered that the Sortilin receptor binds to OSR1, leading the authors to speculate that Sortilin may be involved in the insulin-dependent GLUT4 surface trafficking. However, the authors do not provide any evidence supporting Sortilin's involvement in insulin- or WNKdependent GLUT4 trafficking. Thus, this conclusion should be qualified, rephrased, or additional data included.

Work from several groups have shown that sortilin is involved in insulin-dependent GLUT4 trafficking, for example [9-11,135-139] as we noted in the manuscript. We now show that WNK463 blocks co-immunoprecipitation of Flag-tagged sortilin with endogenous OSR1 in HEK293T cells. This result supports our model for WNK/OSR1/SPAK- insulin mediated regulation of sortilin.  We included these data in figures 5M, 5N.

Minor issues:

(1) The method and result sections lack information regarding the gender and age of mice used in the behavioral experiments. This information should be added.

Thank you for pointing this out. We apologize for the omission. The requested information has now been added in the methods section.

(2) The authors present an analysis of relative protein levels in Figure 1B and Figure 4B, however, the original immunoblots (?) are not included in the study. These data should be added to provide complete and transparent evidence for the analysis.

Thank you for this request. The blots have now been included in the supplementary figure S2A and Figure 4B, respectively.  

(3) The basis for Figure 3A needs to be explained and supported with suitable references either in the background or in the result section.

Thank you for pointing this out. Figure 3A has been moved to Figure 3H as it represents the model summary of the data presented in Figure 3. Other figure numbers have been changed accordingly.  This figure 3A (now 3H) and the model diagram of Figure 5 (now Figure 5O) are now cited in the Discussion, where the results are considered in detail.      

(4) Figure 4E should be labeled as 'Primary cortical neurons' for clarity, as the major focus is on the hippocampus. To increase consistency, the authors should consider performing the same experiment on hippocampal cultures or explaining using cortical neurons.

Thank you for the suggestion. Figure 4E (now 4F) has been labelled as Primary cortical neurons for clarity. The major focus of this study is to understand the regulation of WNKmediated regulation of insulin signaling in the areas of the brain that are insulin sensitive such as the hippocampus and the prefrontal cortex. Therefore, we included cortical neurons to test this hypothesis.  

(5) Figure 5B: The use of whole brain extracts is inconsistent with the rest of the study, especially considering the indication of differing insulin activity in selected brain regions. The authors should explain why they could not use only hippocampal tissue.

In this manuscript, we are trying to test our hypothesis in insulin-sensitive neuronal cells which includes, but not limited to, the hippocampus. Figure 5B used whole brain extracts, which contain brain regions that are insulin-sensitive as well as insulin-insensitive regions, to show the association between OSR1 and AS160. However, this observation was replicated in the insulin-sensitive SH-SY5Y cell model suggesting that association of OSR1 and AS160 is modulated in the presence of insulin as shown in Figure 5B, 5C. We added data from SH-SY5Y cells showing effects of WNK463. These data support the concept that this is an interaction that is modulated by WNKs and will occur as long as both OSR1/SPAK and AS160 are expressed.

(6) Figure 5B-C - Knock-out or knock-down condition should be included in the co-IP experiment. This is especially straightforward to generate in the SH-SY5Y cells. Moreover, these figures lack loading controls.

If we understand correctly, the issue with regard to including knockdown conditions stems from the issues raised regarding specificity of the antibody which we have addressed in point 10 below. We have now included input blots for both AS160 and OSR1 which serve as the loading control for the IP experiment in figure 5B and 5C.

(7) Figure 5C-D - A condition with WNK463 inhibition alone is missing. This condition is necessary for evaluating the effects of WNK643 inhibition with and without insulin stimulation.

Thank you for this observation. We have now added the data for that condition.  The aim of this experiment in Figure 5C (now 5B and 5C) is to show that insulin is important to facilitate interaction between OSR1 and AS160 in differentiated SHSY5Y cells and the effect of WNK463 to diminish this insulin-dependent interaction. With only WNK463, there was minimal interaction between AS160 and OSR1 as now shown in Figure 5B, 5C.

(8) Figure 5G - This figure shows the overexpression of plasmids in HEK cells, however, it lacks samples that overexpress the plasmid individually (single expression). Such data should be added, especially when the addition of the blocking peptide does not fully disable the interaction between AS160 and SPAK. Additionally, this figure also lacks a loading control, which is essential for validating the results.

Thank you for this comment. Figure 5G (now Figure 5F, 5G) is an in vitro IP in which we have mixed a purified Flag-SPAK fragment residues 50-545 with a lysate from cells expressing Myc-AS160 (residues 193-446). This is essentially an in vitro IP; because it is not an IP experiment from cell lysates where we overexpressed these plasmids which would require a loading control. The lysates were divided in half and one half did not receive the blocking peptide while the other half did, creating a control. From our experience, this blocking peptide does not completely block interactions between SPAK/OSR1 and NKCC2 fragments which are well-characterized interacting partners [a]. The reason for the partial block in interactions could also be attributed to the multivalent nature of interaction between these proteins. This confusion in our methodology used has been noted and we have tried to explain it with more clarity in the methods, results and the figure legend section. Our Commun. Biol. paper [134] that describes this assay and uses it extensively is now available online.

(a) Piechotta K, Lu J, Delpire E. Cation chloride cotransporters interact with the stressrelated kinases Ste20-related proline-alanine-rich kinase (SPAK) and oxidative stress response 1 (OSR1) J Biol Chem. 2002;277:50812–50819. doi: 10.1074/jbc.M208108200.

(9) Figure 5J, L - These figures are missing negative controls. The authors should add Sortilin knock-down or knock-out conditions for the immunoprecipitation experiments. Also, the figures lack loading controls. Moreover, the labeling "Control" should be specified, as it is unclear what this condition represents.

Thank you for noting the lack of clarity in the controls provided. Controls in Figure 5J and 5L refer to IgG Control which serves as the negative control in this case. This has now been specified in the figures (and added Figures 5M and 5N, as well). The issue with OSR1 and sortilin antibody specificity and cross-reaction has been addressed in point 10.

(10) Figure 5I - The fluorescent signals for the individual channels of OSR1 and Sortilin appear identical (even within the background signal). This raises concerns about potential antibody cross-reaction. One potential solution would be to include additional stainings with different antibodies and perform staining of each protein alone to ensure the specificity of the colocalization.

Thank you for pointing this out and giving us an opportunity to provide better images that will address the issues raised regarding antibody cross-reaction and antibody specificity. We realize that the images that we originally provided appeared to show all the puncta colocalize which could give rise to the concern about potential antibody cross-reaction. We have replaced them with more appropriate representative images that clearly show some selected regions of common staining as well as regions where there is no overlap.  

(11) Figures 5D, 5F, 5H, 5L, 5M: These analyses should be first normalized to the loading control such as GAPDH.

In Figure 5F (now 5E), the analysis has been normalized to the total AS160 protein levels. Because we are reporting changes in pAS160 protein, normalizing it to the total AS160 gives a better idea about the changes in the phosphorylated AS160 form compared to the whole protein and this is more appropriate compared to other loading controls such as GAPDH.  

In Figure 5H (now Figure 5G), the analysis is an in vitro IP assay using purified protein fragments. Therefore, using GAPDH as a control is not applicable in this case. Please refer to our response to comment 8 for details.

In Figures 5L, 5M and 5D (now 5K, 5L, 5C) shown, the IP proteins have been normalized to the input protein levels serving as a loading control for the IP experiment. 

(12) Figure 5K: The significance/meaning of the red star is unclear. It should be explained in the figure legend.

Thank you for the opportunity to enhance the readability of our manuscript. The meaning of red star denotes the condition in the yeast two-hybrid assay which shows the binding of CCT of OSR1 with C-terminus of sortilin. This has now been clarified in the figure legend.

(13) Differences in WNK643 dosage and administration periods can affect the results. There is a lack of explanation with regard to the divergent WNK643 treatments of mice across different behavior conditions of fear conditioning, the novel object test, and the elevated plus maze test. This should be considered.

Thank you for pointing out that the explanation regarding the WNK463 dosage and times are unclear. WNK463 was dosed 3 days before the start of the behavior experiment daily at a dose of 6 mg/kg and continued throughout the test protocol. This is the same protocol used for all experiments.  The text describing the protocol has been reworded with more clarity on dosage and times in methods and result section.

Author Response:

We thank all reviewers for their time and effort to carefully review our paper and for the constructive comments on our manuscript. Below we outline our planned revisions to the public reviews of the three reviewers.

In our revision, we will include more details regarding our ABR measurements (including temperature, animal metadata), analysis (including filter settings) and lay out a much more detailed motivation for our ABR signal design. Furthermore, we will provide a more detailed discussion on the caveats of the technique and the interpretation of ABR data in general and our data specifically. Furthermore, we will add more discussion on differences between ABR based audiograms and behavioural data. The authors have extensive experience with the ABR technique and are well aware of its limitations, but also its strengths for use in animals that cannot be trained on behavioural tasks such as the very young zebra finches in this study. These additions will strengthen our paper. We think our conclusions remain justified by our data.

Reviewer #1 and #2:

We thank both reviewers for their positive words and suggested improvements. The planned general improvements listed above will take care of all suggestions and comments in the public review.

Reviewer #3:

We thank the reviewer for the detailed critique of our manuscript and many suggestions for improvement. The planned general improvements listed above will take care of many of the suggestions and comments listed in the public review. Here we will highlight a few first responses that we will address in detail in our resubmission.

The reviewer’s major critiques can be condensed to the following four points.

(1) ABR cannot be done in such small animals.

This critique is unfounded. ABR measures the summed activity in the auditory pathway, and with smaller distance from brainstem to electrodes in small animals, the ABR signals are expected to have higher amplitude and consequently better SNR.  Thus, smaller animals should lead to higher amplitude ABR signals. We have successfully recorded ABR in animals smaller than 2 DPH zebra finches to support this claim (zebrafish (Jørgensen et al., 2012), 10 mm froglets (Goutte et al., 2017) and 5 mm salamanders (Capshaw et al., 2020). It is more surprising the technique still provides robust signals even in very large animals such as Minke whales (Houser et al., 2024).

(2) The ABR methods used does not follow protocol for other published work in birds. Particularly the 25 ms long duration tone bursts may have underestimated high frequency hearing.

There is no fixed protocol for ABR measurements, and several studies of bird ABR have used as long or even longer durations. Longer-duration signals were chosen deliberately and are necessary to have a sufficient number of cycles and avoid frequency splatter at our lowest frequencies used (see Lauridsen et al., 2021).

(3) Sensitivity data should be corrected from ABR to behavioural data.

We present the results of our measurements on hearing sensitivity using ABR, and ABR based thresholds are generally less sensitive than thresholds based on behavioural studies (presented in Fig 2c). Correcting for these measurements to behavioural thresholds is of course possible, but presenting only the corrected thresholds would be a misrepresentation of our sensitivity data. Even so it should be done only within species and age group and such data is currently not available. In our revision, we will include elaborate discussion on this topic.

(4) Results are inconsistent with papers in developing songbirds.

We agree that our results do not support and even question the claims in earlier work. These papers however do either 1) not measure hearing physiology or 2) do so in different species. To our best knowledge there is presently no data published on the auditory physiology development in songbird embryos. Our data are consistent with what is known about the physiology of auditory development in all birds studied so far. We will provide a detailed discussion on this topic in our revision.

References

Capshaw et al. (2020) J Exp Biol 223: jeb236489

Goutte et al. (2017) Sci Rep 7: 12121, doi 10.1038/s41598-017-12145-5

Houser et al. (2024) Science 386, 902-906. DOI:10.1126/science.ado7580).

Jørgensen et al. (2012) Adv Exp Med Biol 730: 117-119

Lauridsen et al (2021) J Exp Biol 224: jeb237313. https://doi.org/10.1242/jeb.237313

Author response:

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

Reviewer #1 (Public review):

This Reviewer was positive about the study, stating ‘The findings are interesting and important to increase the understanding both of the synaptic transmissions in the main olfactory bulb and the DA neuron diversity.’ They provided a number of helpful suggestions for improving the paper, which we have incorporated as follows:

(1) It is known that there are two types of DA neurons in the glomerular layer with different diameters and capacitances (Kosaka and Kosaka, 2008; Pignatelli et al., 2005; Angela Pignatelli and Ottorino Belluzzi, 2017). In this manuscript, the authors need to articulate better which layer the imaging and ephys recordings took place, all glomerular layers or with an exception. Meanwhile, they have to report the electrophysiological properties of their recordings, including capacitances, input resistance, etc.

We thank the Reviewer for this clarification. Indeed, the two dopaminergic cell types we study here correspond directly to the subtypes previously identified based on cell size. Our previous work showed that axon-bearing OB DA neurons have significantly larger somas than their anaxonic neighbours (Galliano et al. 2018), and we replicate this important result in the present study (Figure 3D). In terms of electrophysiological correlates of cell size, we now provide full details of passive membrane properties in the new Supplementary Figure 4, as requested. Axon-bearing DA neurons have significantly lower input resistance and show a non-significant trend towards higher cell capacitance. Both features are entirely consistent with the larger soma size in this subtype. We apologise for the oversight in not fully describing previous categorisations of OB DA neurons, and have now added this information and the appropriate citations to the Introduction (lines 56 to 59 of the revised manuscript). 

In terms of cell location, all cells in this study were located in the OB glomerular layer. We sampled the entire glomerular layer in all experiments, including the glomerular/EPL border where the majority of axon-bearing neurons are located (Galliano et al. 2018). This is now clarified in the Materials and Methods section (lines 535 to 537 and 614 to 616 of the revised manuscript).

(2) It is understandable that recording the DA neurons in the glomerular layer is not easy. However, the authors still need to increase their n's and repeat the experiments at least three times to make their conclusion more solid. For example (but not limited to), Fig 3B, n=2 cells from 1 mouse. Fig.4G, the recording only has 3 cells.

Despite the acknowledged difficulty of these experiments, we have now added substantial extra data to the study as requested. We have increased the number of cells and animals to further support the following findings:

Fig 3B: we now have n=5 cells from N=3 mice. We have created a new Supplementary Figure 1 to show all the examples.

Figure 4G: we now have n=6 cells from N=4 mice.

Figure 5G: we now have n=3 cells from N=3 mice.

The new data now provide stronger support for our original conclusions. In the case of auto-evoked inhibition after the application of D1 and D2 receptor antagonists, a nonsignificant trend in the data suggests that, while dopamine is clearly not necessary for the response, it may play a small part in its strength. We have now included this consideration in the Results section (lines 256 to 264 of the revised manuscript).

(3) The statistics also use pseudoreplicates. It might be better to present the biology replicates, too.

Indeed, in a study focused on the structural and functional properties of individual neurons, we performed all comparisons with cell as the unit of analysis. This did often (though not always) involve obtaining multiple data points from individual mice, but in these low-throughput experiments n was never hugely bigger than N. The potential impact of pseudoreplicates and their associated within-animal correlations was therefore low. We checked this in response to the Reviewer’s comment by running parallel nested analyses for all comparisons that returned significant differences in the original submission. These are the cases in which we would be most concerned about potential false positive results arising from intra-animal correlations, which nested tests specifically take into account (Aarts et al., 2013). In every instance we found that the nested tests also reported significant differences between anaxonic and axonbearing cell types, thus fully validating our original statistical approach. We now report this in the relevant section of the Materials and Methods (lines 686 to 691 of the revised manuscript).

(4) In Figure 4D, the authors report the values in the manuscript. It is recommended to make a bar graph to be more intuitive.

This plot does already exist in the original manuscript. We originally describe these data to support the observation that an auto-evoked inhibition effect exists in anaxonic neurons (corresponding to now lines 240 to 245 of the revised manuscript). We then show them visually in their entirety when we compare them to the lack of response in axon-bearing neurons, depicted in Figure 5C. We still believe that this order of presentation is most appropriate for the flow of information in the paper, so have maintained it in our revised submission.

(5) In Figure 4F and G, although the data with three cells suggest no phenotype, the kinetics looked different. So, the authors might need to explore that aside from increasing the n.

We thank the Reviewer for this suggestion. To quantify potential changes in the autoevoked inhibition response kinetics, we fitted single exponential functions and compared changes in the rate constant (k; Methods, lines 650 to 652 of the revised manuscript). Overall, we observed no consistent or significant change in rate constant values after adding DA receptor antagonists. This finding is now reported in the Results section (lines 260 to 263 of the revised manuscript) and shown in a new Supplementary Figure 3.

(6) Similarly, for Figure 4I and J, L and M, it is better to present and analyze it like F and G, instead of showing only the after-antagonist effect.

We agree that the ideal scenario would have been to perform the experiments in Figure 4J and 4M the same way as those in Figure 4G, with a before vs after comparison. Unfortunately, however, this was not practically possible. 

When attempting to apply carbenoxelone to already-patched cells, we found that this drug highly disrupted the overall health and stability of our recordings immediately after its application. This is consistent with previous reports of similar issues with this compound (e.g. Connors 2012, Epilepsy Currents; Tovar et al., 2009, Journal of Neurophysiology). After many such attempts, the total yield of this experiment was one single cell from one animal. Even so, as shown in the traces below, we were able to show that the auto-evoked inhibition response was not eliminated in this specific case:

Author response image 1.

Traces of an AEI response recorded before (magenta) and after (green) the application of carbenoxolone (n=1 cell from N=1 mouse).

In light of these issues, we instead followed published protocols in applying the carbenoxolone directly in the bath without prior recording for 20 minutes (following Samailova et al., 2003, Journal of Neurochemistry) and ran the protocol after that time. Given that our main question was to ask whether gap junctions were strictly necessary for the presence of any auto-evoked inhibition response, our positive findings in these experiments still allowed us to draw clear conclusions.

In contrast, the issue with the NKCC1 antagonist bumetanide was time. As acknowledged by this Reviewer, obtaining and maintaining high-quality patch recordings from OB DA neurons is technically challenging. Bumetanide is a slow-acting drug when used to modify neuronal chloride concentrations, because in addition to the time it takes to reach the neurons and effectively block NKCC1, the intracellular levels of chloride subsequently change slowly. Studies using this drug in slice physiology experiments typically use an incubation time of at least 20 minutes (e.g. Huberfeld et al., 2007, Journal of Neuroscience), which was incompatible with productive data collection in OB DA neurons. Again, after many unsuccessful efforts, we were forced instead to include bumetanide in the bath without prior recording for 20-30 minutes. As with the carbenoxolone experiment, our goal here was to establish whether autoevoked inhibition was in any way retained in the presence of this drug, so our positive result again allowed us to draw clear conclusions.

Reviewer #1 (Recommendations for the authors):

(1) I suggest the authors reconsider the terminology. For example, they use "strikingly" in their title. The manuscript reported two different transmitter release strategies but not the mechanisms, and the word "strikingly" is not professional, either.

We appreciate the Reviewer’s attention to clarity and tone in the manuscript title, and have nevertheless decided to retain the original wording. The almost all-or-nothing differences between closely related cell types shown in structural and functional properties here (Figures 3F & 5C) are pronounced, extremely clear and easily spotted – all properties appropriate for the word ‘striking.’ In addition, we note that the use of this term is not at all unprofessional, with a PubMed search for ‘strikingly’ in the title of publications returning over 200 hits.

(2) Similarly, almost all confocal scopes are 3D because images can be taken at stacks. So "3D confocal" is misleading.

We understand that this is misleading. We have now replaced the sentence ‘Example snapshot of a 3D confocal stack of…’ by ‘Example confocal images of…’ in all the figure legends that apply.

(3) It is recommended to present the data in bar graphs with data dots instead of showing the numbers in the manuscript directly.

We agree entirely, and now present data plots for all comparisons reported in the study (Supplementary Figures 2, 4 and 5).

Reviewer #2 (Recommendations for the authors):

(1) Several experiments report notably small sample sizes, such as in Figures 3B and 5G, where data from only 2 cells derived from 1-2 mice are presented. Figures 4E-G also report the experimental result only from 3 cells derived from 3 mice. To enhance the statistical robustness and reliability of the findings, these experiments should be replicated with larger sample sizes.

As per our response to Reviewer 1’s comment #2 above, and to directly address the concern that some evidence was ‘incomplete’, we have now added significant extra data and analysis to this revised submission (Figures 4 and 5; and Supplementary Figure 1). We believe that this has further enhanced the robustness and reliability of our findings, as requested.

(2) The authors utilize vGAT-Cre for Figures 1-3 and DAT-tdTomato for Figures 4-5, raising concerns about consistency in targeting the same population of dopaminergic neurons. It remains unclear whether all OB DA neurons express vGAT and release GABA. Clarification and additional evidence are needed to confirm whether the same neuronal population was studied across these experiments.

Although we indeed used different mouse lines to investigate structural and functional aspects of transmitter release, we can be very confident that both approaches allowed us to study the same two distinct DA cell types being compared in this paper. Existing data to support this position are already clear and strong, so in this revision we have focused on the Reviewer’s suggestion to clarify the approaches we chose.

First, it is well characterised that in mouse and many other species all OB DA neurons are also GABAergic. This has been demonstrated comprehensively at the level of neurochemical identity and in terms of dopamine/GABA co-release, and is true across both small-soma/anaxonic and large-soma/axon-bearing subclasses (Kosaka & Kosaka 2008; 2016; Maher & Westbrook 2008; Borisovska et al., 2013; Vaaga et al., 2016; Liu et al. 2013). To specifically confirm vGAT expression, we have also now provided additional single-cell RNAseq data and immunohistochemical label in a revised Figure 1 (see also Panzanelli et al., 2007, now referenced in the paper, who confirmed endogenous vGAT colocalisation in TH-positive OB neurons). Most importantly, by using vGAT-cre mice here we were able to obtain sufficient numbers of both anaxonic and axon-bearing DA neurons among the vGAT-cre-expressing OB population. We could unambiguously identify these cells as dopaminergic because of their expression of TH protein which, due to the absence of noradrenergic neurons in the OB, is a specific and comprehensive marker for dopaminergic cells in this brain region (Hokfelt et al., 1975; Rosser et al., 1986; Kosaka & Kosaka 2016). Crucially, both axon-bearing and anaxonic OB DA subtypes strongly express TH (Galliano et al., 2018, 2021). We have now added additional text to the relevant Results section (lines 99 to 108 of the revised manuscript) to clarify these reasons for studying vGAT-cre mice here.

We were also able to clearly identify and sample both subtypes of OB DA neuron using DAT-tdT mice. Our previous published work has thoroughly characterised this exact mouse line at the exact ages studied in the present paper (Galliano et al., 2018; Byrne et al., 2022). We know that DAT-tdT mice provide rather specific label for TH-expressing OB DA neurons (75% co-localisation; Byrne et al., 2022), but most importantly we know which non-DA neurons are labelled in this mouse line and how to avoid them. All nonTH-expressing but tdT-positive cells in juvenile DAT-tdT mice are small, dimly fluorescent and weakly spiking neurons of the calretinin-expressing glomerular subtype (Byrne et al., 2022). These cells are easily detected during physiological recordings, and were excluded from our study here. This information is now provided in the relevant Methods section (lines 616 to 619 of the revised manuscript, also referenced in lines 236 to 240 of the results section), and we apologise for its previous omission. Finally, we have shown both structurally and functionally that both axon-bearing and anaxonic OB DA subtypes are labelled in DAT-tdT mice (Galliano et al., 2018, Tufo et al., 2025; present study). Overall, these additional clarifications firmly establish that the same neuronal populations were indeed studied across our experiments.

(3) The low TH+ signal in Figure 1D raises questions regarding the successful targeting of OB DA neurons. Further validation, such as additional staining, is required to ensure that the targeted neurons are accurately identified.

As noted in our response to the previous comment, TH is a specific marker for dopaminergic neurons in the mouse OB, and is widely used for this purpose. Labelling for TH in our tissue is extremely reliable, and in fact gives such strong signal that we were forced to reduce the primary antibody concentration to 1:50,000 to prevent bleedthrough into other acquisition channels. Even at this concentration it was extremely straightforward to unambiguously identify TH-positive cells based on somatic immunofluorescence. We recognise, however, that the original example image in Figure 1D was not sufficiently clear, and have now provided a new example which illustrates the TH-based identification of these cells much more effectively. 

(4) Estimating the total number of dopaminergic neurons in the olfactory bulb, along with the relative proportions of anaxonic and axon-bearing neuron subtypes, would provide valuable context for the study. Presenting such data is crucial to underscore the biological significance of the findings.

This information has already been well characterised in previous studies. Total dopaminergic cell number in the OB is ~90,000 (Maclean & Shipley, 1988; Panzanelli et al., 2007; Parrish-Aungst et al., 2007). In terms of proportions, anaxonic neurons make up the vast majority of these cells, with axon-bearing neurons representing only ~2.5% of all OB dopaminergic neurons at P28 (Galliano et al., 2018). Of course, the relatively low number of the axon-bearing subtype does not preclude its having a potentially large influence on glomerular networks and sensory processing, as demonstrated by multiple studies showing the functional effects of inter-glomerular inhibition (Kosaka & Kosaka, 2008; Liu et al., 2013; Whitesell et al., 2013; Banerjee et al., 2015). This information has now been added to the Introduction (line 47 and lines 59 to 62 of the revised manuscript).

(5) The authors report that in-utero injection was performed based on the premise that the two subclasses of dopaminergic neurons in the olfactory bulb are generated during embryonic development. However, it remains unclear whether in-utero injection is essential for distinguishing between these two subclasses. While the manuscript references a relevant study, the explanation provided is insufficient. A more detailed justification for employing in-utero injection would enhance the manuscript's clarity and methodological rigor.

We apologise for the lack of clarity in explaining the approach. In utero injection is not absolutely essential for distinguishing between the two subclasses, but it does have two major advantages. 1) Because infection happens before cells migrate to their final positions, it produces sparse labelling which permits later unambiguous identification of individual cells’ processes; and 2) Because both subclasses are generated embryonically (compared to the postnatal production of only anaxonic DA neurons), it allows effective targeting of both cell types. We have now expanded the relevant section of the Results to explain the rationale for our approach in more detail (lines 109 to 116 of the revised manuscript).

(6) In Figures 1A and 4A, it appears that data from previously published studies were utilized to illustrate the differential mRNA expression in dopaminergic neurons of the olfactory bulb. However, the Methods section and the manuscript lack a detailed description of how these dopaminergic neurons were classified or analyzed. Given that these figures contribute to the primary dataset, providing additional explanation and context is essential to ensure clarity of the findings.

We apologise for the lack of clarity. We have now extended the part of the methods referring to the RNAseq data analysis (lines 666 to 678 of the revised manuscript). 

(7) In Figure 2C, anaxonic dopamine neurons display considerable variability in the number of neurotransmitter release sites, with some neurons exhibiting sparse sites while others exhibit numerous sites. The authors should address the potential biological or methodological reasons for this variability and discuss its significance.

We thank the Reviewer for highlighting this feature of our data. We have now outlined potential methodological reasons for the variability, whilst also acknowledging that it is consistent with previous reports of presynaptic site distributions in these cells (Kiyokage et al., 2017; Results, lines 169 to 172 of the revised manuscript). We have also added a brief discussion of the potential biological significance (Discussion, lines 446 to 450).

(8) In the images used to differentiate anaxonic and axon-bearing neurons, the soma, axons, and dendrites are intermixed, making it difficult to distinguish structures specific to each subclass. Employing subclass-specific labeling or sparse labeling techniques could enhance clarity and accuracy in identifying these structures.

Distinguishing these structures is indeed difficult, and was the main reason we used viral label to produce sparse labelling (see response to comment #5 above). In all cases we were extremely careful, including cells only when we could be absolutely certain of their anaxonic or axon-bearing identity, and could also be certain of the continuity of all processes. Crucially, while the 2D representations we show in our figures may suggest a degree of intermixing, we performed all analyses on 3D image stacks, significantly improving our ability to accurately assign structures to individual cells. We have now added extra descriptions of this approach in the relevant Methods section (lines 546 to 548 of the revised manuscript).

(9) In Figure 3, the soma area and synaptophysin puncta density are compared between axon-bearing and anaxonic neurons. However, the figure only presents representative images of axon-bearing neurons. To ensure a fair and accurate comparison, representative images of both neuron subtypes should be included.

The original figures did include example images of puncta density (or lack of puncta) in both cell types (Figure 2B and Figure 3E). For soma area, we have now included representative images of axon-bearing and anaxonic neurons with an indication of soma area measurement in a new Supplementary Figure 2A.

(10) In Figure 4B, the authors state that gephyrin and synaptophysin puncta are in 'very close proximity.' However, it is unclear whether this proximity is sufficient to suggest the possibility of self-inhibition. Quantifying the distance between gephyrin and synaptophysin puncta would provide critical evidence to support this claim. Additionally, analyzing the distribution and proportion of gephyrinsynaptophysin pairs in close proximity would offer further clarity and strengthen the interpretation of these findings.

We thank the Reviewer for raising this issue. We entirely agree that the example image previously shown did not constitute sufficient evidence to claim either close proximity of gephyrin and synaptophysin puncta, nor the possibility of self-inhibition. We are not in a position to perform a full quantitative analysis of these spatial distributions, nor do we think this is necessary given previous direct evidence for auto-evoked inhibition in OB dopaminergic cells (Smith and Jahr, 2002; Murphy et al., 2005; Maher and Westbrook, 2008; Borisovska et al., 2013) and our own demonstration of this phenomenon in anaxonic neurons (Figure 4). We have therefore removed the image and the reference to it in the text. 

(11) In Figures 4J and 4M, the effects of the drugs are presented without a direct comparison to the control group (baseline control?). Including these baseline control data is essential to provide a clear context for interpreting the drug effects and to validate the conclusions drawn from these experiments.

We appreciate the Reviewer’s attention to this important point. As this concern was also raised by Reviewer 1 (their point #6), we have provided a detailed response fully addressing it in our replies to Reviewer 1 above. 

(12) In Lines 342-344, the authors claim that VMAT2 staining is notoriously difficult. However, several studies (e.g., Weihe et al., 2006; Cliburn et al., 2017) have successfully utilized VMAT2 staining. Moreover, Zhang et al., 2015 - a reference cited by the authors - demonstrates that a specific VMAT2 antibody effectively detects VMAT2. Providing evidence of VMAT2 expression in OB DA neurons would substantiate the claim that these neurons are GABA-co-releasing DA neurons and strengthen the study's conclusions.

As noted in response to this Reviewer’s comment #2 above, there is clear published evidence that OB DA neurons are GABA- and dopamine-releasing cells. These cells are also known to express VMAT2 (Cave et al., 2010; Borisovska et al., 2013; Vergaña-Vera et al., 2015). We do not therefore believe that additional evidence of VMAT2 expression is necessary to strengthen our study’s conclusions. We did make every effort to label VMAT2-positive release sites in our neurons, but unfortunately all commercially available antibodies were ineffective. The successful staining highlighted by the Reviewer was either performed in the context of virally driven overexpression (Zhang et al., 2015) or was obtained using custom-produced antibodies (Weihe et al., 2006; Cliburn et al., 2017). We have now modified the Discussion text to provide more clarification of these points (lines 393 to 395 of the revised manuscript).

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

This paper investigates the physical mechanisms underlying cell intercalation, which then enables collective cell flows in confluent epithelia. The authors show that T1 transitions (the topological transitions responsible for cell intercalation) correspond to the unbinding of groups of hexatic topological defects. Defect unbinding, and hence cell intercalation and collective cell flows, are possible when active stresses in the tissue are extensile. This result helps to rationalize the observation that many epithelial cell layers have been found to exhibit extensile active nematic behavior.

Strengths

The authors obtain their results based on a combination of active hexanematic hydrodynamics and a multiphase field (MPF) model for epithelial layers, whose connection is a strength of the paper. With the hydrodynamic approach, the authors find the active flow fields produced around hexatic topological defects, which can drive defect unbinding. Using the MPF simulations, the authors show that T1 transitions tend to localize close to hexatic topological defects.

We are grateful to Reviewer #1, for appreciating and highlighting the strengths of work.

Weaknesses

Citations are sometimes not comprehensive. Cases of contractile behavior found in collective cell flows, which would seemingly contradict some of the authors’ conclusions, are not discussed.

I encourage the authors to address the comments and questions below.

We are thankful to Reviewer #1, for their questions and comments. We have addressed them point by point below, and have amended the manuscript accordingly.

(1) In Equation 1, what do the authors mean by the cluster’s size ℓ? How is this quantity defined? The calculations in the Methods suggest that ℓ indicates the distance between the p-atic defects and the center of the T1 cell cluster, but this is not clearly defined.

We are thank Reviewer #1 for their question. We define the cluster size as the initial distance between the center of the quadrupole and any defect (see Methods). In a primary cell cluster, where cells themselves are the defects, the cluster’s size is the distance between the center of the central junction and the center of any cell in the cluster. Hence, this is half the diameter of an cell which, for example in a typical, confluent MDCK epithelial monolayer, would be about 10µm. We have added this clarification in the definition of the cluster size, above Eq. (1).

(2) The multiphase field model was developed and reviewed already, before the Loewe et al. 2020 paper that the authors cite. Earlier papers include Camley et al. PNAS 2014, Palmieri et al. Sci. Rep. 2015, Mueller et al. PRL 2019, and Peyret et al. Biophys. J. 2019, as reviewed in Alert and Trepat. Annu. Rev. Condens. Matter Phys. 2020.

We thank the referee for their suggestion to incorporate further MPF literature. We have done so in the amended manuscript.

(3) At what time lag is the mean-squared displacement in Figure 3f calculated? How does the choice of a lag time affect these data and the resulting conclusions?

The scatter plot in Fig. 3f was constructed by dividing the system into square subregions of size ∆ℓ = 35 l.u., each containing approximately 4 cells. For each subregion, we analyzed a time window of ∆t = 25 × 10³ iterations, measuring both the normalized mean square displacement of cells (relative to the subregion area ∆ℓ²) and the average defect density. The normalized displacement is calculated as m.s.d. , where t∗ denotes the start time of the observation window. We chose the time window ∆t used to compute the mean square displacement to match the characteristic duration of T1 events and defect lifetimes in our simulations. Observation times much longer (∆t > 35 × 10³) than the typical T1 event duration would cause the two sets of data points to merge into a single group, suggesting no correlation between cell motility and defect density beyond defect life-time.

(4) The authors argue that their results provide an explanation for the extensile behavior of cell layers. However, there are also examples of contractile behavior, such as in Duclos et al., Nat. Phys., 2017 and in P´erez-Gonz´alez et al., Nat. Phys., 2019. In both cases, collective cell flows were observed, which in principle require cell intercalations. How would these observations be rationalized with the theory proposed in this paper? Can these experiments and the theory be reconciled?

The contractile or extensile nature of stress in epithelia depends crucially on the specific tissue type and its biological context. Different cell populations, depending on their position along the epithelial/mesenchymal spectrum, can exhibit either contractile or extensile behaviors. Our theory applies to tissues where hexatic order dominates at the cellular scale, particularly in confluent systems where neighbor exchanges occur primarily through T1 transitions. In contrast, the systems studied by Duclos et al., Nat. Phys. (2018) and Perez-Gonzalez et al. (Nat. Phys., 2019) exhibit nematic order at the cellular level, meaning their dynamics are governed by fundamentally different mechanisms. Since our framework is derived for hexatic-dominated tissues, it does not directly apply to those cases, though a hybrid hexanematic descriptions previously developed by some of the authors in Armengol-Collado et al. eLife 13:e86400 (2024) could help reconcile these observations. In general, a key distinction must be made between the contractility of individual cells and the extensile/contractile nature of the collective force network. To illustrate this, consider a cell exerting a 6- fold symmetric force distribution: each vertex force arises from an imbalance in junctional tensions with neighboring cells, which are themselves contractile due to actomyosin activity. However, the resulting vertex forces can be either contractile or extensile depending on network geometry and tension distribution. This is captured in our coarse-grained description [see Armengol-Collado et al. eLife 13:e86400 (2024)], where the active stress emerges from higher-order moments of cellular forces. Specifically, the deviatoric part of the hexatic active stress tensor , where is the cell radius, the number cell density and the intensity of cellular tension. The negative sign of the coefficient of the active stress shows that the active stress is extensile—consistently with observations in various epithelial systems (e.g., Saw et al., Nature 2017; Blanch-Mercader et al., Phys. Rev. Lett. 2018). Finally, we note that the connection between cellular-scale forces and large-scale extensility has been rationalized in other contexts, such as active nematics (Balasubramaniam et al., Nat. Mater. 2021).

Reviewer #2 (Public Review):

This paper studies the role of hexatic defects in the collective migration of epithelia. The authors emphasize that epithelial migration is driven by cell intercalation events and not just isolated T1 events, and analyze this through the lens of hexatic topological defects. Finally, the authors study the effect of active and passive forces on the dynamics of hexatic defects using analytical results, and numerical results in both continuum and phase-field models.

The results are very interesting and highlight new ways of studying epithelial cell migration through the analysis of the binding and unbinding of hexatic defects.

We are grateful to Reviewer #2, for their interest and for emphasizing the novelty of our work.

Strengths

(1) The authors convincingly argue that intercalation events are responsible for collective cell migration, and that these events are accompanied by the formation and unbinding of hexatic topological defects.

(2) The authors clearly explain the dynamics of hexatic defects during T1 transitions, and demonstrate the importance of active and passive forces during cell migration.

(3) The paper thoroughly studies the T1 transition through the viewpoint of hexatic defects. A continuum model approach to study T1 transitions in cell layers is novel and can lead to valuable new insights.

We thank the Reviewer for their kind and supporting words, and for highlighting the clarity, persuasiveness, and thoroughness.

Weaknesses

(1) The authors could expand on the dynamics of existing hexatic defects during epithelial cell migration, in addition to how they are created during T1 transitions.

We thank the referee for their comment. The detailed analysis of dislocation-pair unbinding modes and their statistical impact on the transition to collective migration is comprehensively addressed in our subsequent work Puggioni et al., arXiv:2502.09554. In the present study, we focus specifically on the fundamental mechanism enabling dislocation unbinding: active extensile stresses generate flows that drive dislocation pairs apart, while passive elastic stresses tend to pull them together (Krommydas et al., Phys. Rev. Lett. 2023; Armengol- Collado et al., arXiv:2502.13104). When active forces dominate over passive restoring forces, the dislocations unbind. This represents a crucial distinction from classical Berezinskii–Kosterlitz–Thouless or Kosterlitz–Thouless–Halperin–Nelson–Youn transitions, where thermal fluctuations drive defect unbinding. In our system, the process is fundamentally activity-driven. Nevertheless, the resulting state - characterized by unbound defects and collective migration - bears strong analogy to the melting transition in equilibrium systems. We emphasize that the dynamics of passive defects has been previously examined in Krommydas et al., Phys. Rev. Lett. 2023. A discussion of these aspects can be found in the Appendix “Numerical simulations of defect annihilation and unbinding”.

(2) The different terms in the MPF model used to study cell layer dynamics are not fully justified. In particular, it is not clear why the model includes self-propulsion and rotational diffusion in addition to nematic and hexatic stresses, and how these quantities are related to each other.

We thank the referee for their comment. The MPF model’s terms (e.g., self-propulsion, rotational diffusion), reflect the stochastic, deformable nature of cells as active droplets migrating with near-constant speed. We emphasize that self-propulsion is the only non-equilibrium mechanism in our model — no additional active stresses (nematic or hexatic) are imposed. We have clarified this point in the revised manuscript and expanded our discussion of the MPF model.

(3) The authors could provide some physical intuition on what an active extensile or contractile term in the hexatic order parameter means, and how this is related to extensility and contractility in active nematics and/or for cell layers.

We thank the referee for their comment. As we explain in the reply to comment [4] of Reviewer #1, the contractile or extensile nature of stress in epithelia depends crucially on the specific tissue type and its biological context. Different cell populations, depending on their position along the epithelial/mesenchymal spectrum, can exhibit either contractile or extensile behaviors. Our theory applies to tissues where hexatic order dominates at the cellular scale, particularly in confluent systems where neighbor exchanges occur primarily through T1 transitions. In contrast, the systems studied by Duclos et al., Nat. Phys. (2018) and Perez-Gonzalez et al. (Nat. Phys., 2019) exhibit nematic order at the cellular level, meaning their dynamics are governed by fundamentally different mechanisms. Since our framework is derived for hexatic-dominated tissues, it does not directly apply to those cases, though a hybrid hexanematic descriptions previously developed by some of the authors in Armengol-Collado et al. eLife 13:e86400 (2024) could help reconcile these observations. In general, a key distinction must be made between the contractility of individual cells and the extensile/contractile nature of the collective force network. To illustrate this, consider a cell exerting a 6-fold symmetric force distribution: each vertex force arises from an imbalance in junctional tensions with neighboring cells, which are themselves contractile due to actomyosin activity. However, the resulting vertex forces can be either contractile or extensile depending on network geometry and tension distribution. This is captured in our coarse-grained description [see Armengol-Collado et al. eLife 13:e86400 (2024)], where the active stress emerges from higher-order moments of cellular forces. Specifically, the deviatoric part of the hexatic active stress tensor , where is the cell radius, the number cell density and the intensity of cellular tension. The negative sign of the coefficient of the active stress shows that the active stress is extensile—consistently with observations in various epithelial systems (e.g., Saw et al., Nature 2017; Blanch-Mercader et al., Phys. Rev. Lett. 2018). Finally, we note that the connection between cellular-scale forces and large-scale extensility has been rationalized in other contexts, such as active nematics (Balasubramaniam et al., Nat. Mater. 2021).

Recommendations for the Authors: Reviewer #2 (Recommendations for the Authors):

(1) The authors point out that hexatic topological defects are produced in quadrupoles (L109). Does this also mean that these defects can be annihilated only in quadrupoles as well? In the same vein, are hexatic defects always bound in pairs, as suggested by the schematics, or is it possible to observe an isolated hexatic defect?

We thank the referee for their question. Hexatic disclinations (the defect monopoles discussed in this work), much like electrons and positrons, can annihilate in any number of neutral charge configuration (dipole, quadrupole, octupole, etc.). Unbinding a pair of hexatic disinclination, however, costs much more energy than unbinding a quadrupole to dipoles. Hence isolated defects appear in abundance only in late, fully disordered phase, where the system has completely “melted”. For more details on how defect unbinding modes affect tissue dynamics, please see our subsequent work Puggioni et al., arXiv:2502.09554.

(2) Could you clarify if the flows described in Figures 2(a)-(b), panel (i) are driven by a passive backflow term without activity? Could you compare the magnitudes of these flows compared to the typical active terms?

We thank the referee for their question. In panel 2(b) there is only passive backflow. In 2(a) instead, both terms are included, and are in a regime of parameters where the active flow overcomes the active flow (and hence the active force overcomes the passive force as delineated in the discussions section). In turn, the magnitude of the passive flows, is studied in detail in our previous work Krommydas et al., (Phys. Rev. Lett. 2023).

(3) Could you clarify how the continuum hexatic model and MPF model are related to each other? What are the similarities and differences in the dynamics of these models?

We thank the referee for this insightful question. A key point of our work is precisely that the continuum hexatic model and the MPF (Multi-Phase Field) model are distinct in nature.

The MPF model is an established agent-based framework used to simulate tissue dynamics at the cellular level. It captures individual cell behaviors and interactions through phase-field variables. In our work, we use the MPF model as a benchmark to extract statistical features of tissue dynamics, such as defect motion and orientational correlations. In contrast, our continuum hexatic model is a coarse-grained hydrodynamic theory that describes the dynamics of orientational order in active tissues. It is built on symmetry principles and conservation laws, and it does not rely on microscopic cell-level details. Instead, it captures the collective behavior of the system through a hexatic order parameter and its coupling to flow and activity.

Despite their conceptual differences, the MPF model and our hydrodynamic theory exhibit similar statistical features. This agreement—also observed in the independent study by Jain et al. (Phys. Rev. Res. 2024)—provides strong support for the validity and generality of our continuum description.

(4) When multiple references by the same author and year are cited using alphabets, the second alphabet is not in bold e.g. Giomi et al., 2022b, a in Line 75, and others.

We are grateful to the referee carefully going through the manuscript and pointing out these typos. We have corrected them in the amended manuscript.

Reviewer #3 (Public Review):

In this manuscript, the authors discuss epithelial tissue fluidity from a theoretical perspective. They focus on the description of topological transitions whereby cells change neighbors (T1 transitions). They explain how such transitions can be described by following the fate of hexatic defects. They first focus on a single T1 transition and the surrounding cells using a hydrodynamic model of active hexatics. They show that successful T1 intercalations, which promote tissue fluidity, require a sufficiently large extensile hexatic activity in the neighborhood of the cells attempting a T1 transition. If such activity is contractile or not sufficiently extensile, the T1 is reversed, hexatic defects annihilate, and the epithelial network configuration is unchanged. They then describe a large epithelium, using a phase field model to describe cells. They show a correlation between T1 events and hexatic defects unbinding, and identify two populations of T1 cells: one performing T1 cycles (failed T1), and not contributing to tissue migration, and one performing T1 intercalation (successful T1) and leading to the collective cell migration.

Strengths

The manuscript is scientifically sound, and the variety of numerical and analytical tools they use is impressive. The approach and results are very interesting and highlight the relevance of hexatic order parameters and their defects in describing tissue dynamics.

We thank the Reviewer for recognizing the scientific soundness of the manuscript, the breadth of numerical and analytical tools employed, as well as their interest in our work.

Weaknesses

(1) Goal and message of the paper. (a) In my opinion, the article is mainly theoretical and should be presented as such. For instance, their conclusions and the consequences of their analysis in terms of biology are not extremely convincing, although they would be sufficient for a theory paper oriented to physicists or biophysicists. The choice of journal and potential readership should be considered, and I am wondering whether the paper structure should be re-organized, in order to have side-by-side the methods and the results, for instance (see also below).

We thank the referee for their criticism. In response, we have made an effort to reword certain parts of the manuscript. As with any theoretical study, the biological implications of our work can only be fully assessed through experimental validation — a prospect we look forward to. Nevertheless, we have submitted our work to the subsection of Physics of Life, which we believe is perfectly suited to our content.

(b) Currently, the two main results sections are somewhat disconnected, because they use different numerical models, and because the second section only marginally uses the results from the first section to identify/distinguish T1.

We thank the referee, for their comment. In the second section we are using statistics from the MPF model, to support the analytical and numerical findings of our hydrodynamic theory of cell intercalation. In the time between our submission, further qualitative evidence have been brought to light in the work of Jain et al. (Phys. Rev. Res. 2024).

(2) Quite surprisingly, the authors use a cell-based model to describe the macroscopic tissuescale behavior, and a hydrodynamic model to describe the cell-based events. In particular, their hydrodynamic description (the active hexatic model) is supposed to be a coarse-grained description, valid to capture the mesoscopic physics, and yet, they use it to describe cellscale events (T1 transitions). For instance, what is the meaning of the velocity field they are discussing in Figure 2? This makes me question the validity of the results of their first part.

We thank the referee for their comment. There are many excellent discrete models of epithelial tissues in the literature (e.g., Bi et al., Phys. Rev. X 2016; Pasupalak et al., Soft Matter 2020; Graner et al., Phys. Rev. Lett. 1992), each capturing essential biological features such as cell division, apoptosis and sorting. While these models have provided invaluable insights, our work takes a different approach by developing a continuum theory aimed at describing epithelial dynamics at two levels: (1) mesoscopic intercalation events and (2) macroscopic collective migration. Crucially, our goal is not to replicate a specific discrete model — which would risk constructing a “model of a model” — but rather to derive a hydrodynamic description of tissue dynamics grounded in symmetry principles and conservation laws. Along this logic, the velocity field in our theory should be interpreted as an Eulerian (continuum) velocity, representing the coarse-grained flow of the tissue rather than the Lagrangian motion of individual cells. This distinction is central to our framework, which operates at scales where cellular details are averaged out, yet retains the essential physics of hexatic order and active stresses. We validate our predictions against the Multiphase Field (MPF) model. [We thank Reviewer 1 for their suggestion to incorporate further MPF literature.] Furthermore, Jain et al. (Phys. Rev. Res. 2024) have used the MPF to predict flow patterns around T1 transitions and obtained results compatible with those of our hydrodynamic theory. From this comparison we can conclude that both the MPF and our theory are able to capture the same aspect of cell intercalation in epithelial layer. This, however, does not imply that other discrete models of epithelia can reproduce this aspect too, nor that our theory is specifically tailored to the MPF model. We have clarified these points in the revised manuscript and expanded our discussion of the MPF model.

(3) The quality of the numerical results presented in the second part (phase field model) could be improved. (a) In terms of analysis of the defects. It seems that they have all the tools to compare their cell-resolved simulations and their predictions about how a T1 event translates into defects unbinding. However, their analysis in Figure 3e is relatively minimal: it shows a correlation between T1 cells and defects. But it says nothing about the structure and evolution of the defects, which, according to their first section, should be quite precise.

We thank the referee for their comment. Further qualitative evidence have been brought to light in the work of Jain et al. (Phys. Rev. Res. 2024), were the exact flow pattern predicted by our hydrodynamic theory is obtained, in the MPF, around cells undergoing T1 rearrangements.

(b) In terms of clarity of the presentation. For instance, in Figure 3f, they plot the mean-square displacement as a function of a defect density. I thought that MSD was a time-dependent quantity: they must therefore consider MSD at a given time, or averaged over time. They should be explicit about what their definition of this quantity is.

We thank the referee for raising this point. As clarified in our response to Reviewer 1, point 3, the mean square displacement (MSD) plotted in Fig. 3f is computed over a fixed time window of ∆t = 25×103 iterations, chosen to match the typical duration of T1 events and defect lifetimes. [See also reply to Reviewer #1, point (3).] The MSD is normalized by the subregion area and averaged over time within each window. We have now made this explicit in the amended version of the manuscript.

(c) In terms of statistics. For instance, Figure 3g is used to study the role of rotational diffusion on the average time between T1s. The error bars in this figure are huge and make their claims hardly supported. Their claim of a ”monotonic decay” of the average time between intercalations is also not fully supported given their statistics.

We appreciate the Reviewer’s comment regarding the statistical robustness of Fig. 3g. While we acknowledge that the error bars are substantial – reflecting the inherent variability in cell intercalation dynamics – the yellow curve does exhibit a consistent downward trend in the average time between T1 transitions as rotational diffusion increases. This monotonic decrease is visible across the entire range of variation of the rotational diffusion Dr, and is statistically supported when considering the trend over independent simulations. To address this concern, we have revised the main text to adjusted the wording: instead of stating that “the former is a monotonically decreasing function of Dr,” we now write that “the former displays a decreasing trend with Dr,” which better reflects the statistical variability while preserving the observed behavior.

Reviewer #3 (Recommendations for the Authors):

(1) Section 1 is difficult to follow due to multiple reasons: early but delayed definitions, unclear use of T1 intercalation vs. T1 cycles, disconnected figures and unclear simulation descriptions. We recommend including simulation setup details earlier and restructuring the flow of arguments.

We thank the referee for their comment. We have made an effort in rewording and clarifying things in our amended manuscript. We are slightly confused by what they mean by “early but delayed definitions”, if they could clarify, we would be happy to amend the position and phrasing of these definitions accordingly.

(2) It could be useful to have an additional figure early on defining schematically hexatic defects and an illustration showing an epithelium (or a simulation), similar to what the authors have produced in some of their other publications on this topic.

We thank the referee for their comment. Figures 3c and 3d show what a hexatic defect looks like in a simulation of the epithelium. Following the referee’s recommendation, we have added a note in the caption of figure 3, citing our work were we show the same defects in MDCK epithelial monolayers (Armengol et al., Nat. Phys. 2023).

(3) Minor points and typos:

Line 88: the bond between vertices shrinks, not the vertices.

Figure 1: the 1/6 is displayed as 1 6 (fraction bar missing).

Line 232: “and order” → “one/an order”.

Line 237: Fig. 3g) → Fig. 3g

Line 298: ”nu” and ”v” hard to distinguish in eLife font.

Methods: define all notation clearly (e.g., tensor product exponent, D/Dt in Eq. 3c).

Methods: ”cell orientation, coarse-graining and topological defects” section is difficult to follow, schematic would help.

Line 457 onward: unclear how panels (ii-iv) of Fig. 2ab are obtained.

Line 480 onward: not referenced in main text.

Figure 2: “avalancHe” typo.

Figure 2 caption: “cell intercalaTION” typo.

Movies are neither referenced nor explained.

Figure 5 and 6 are not referenced in the main text.

We thank the referee for their detailed read of the paper. We have corrected all typos.

Author response:

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

Reviewer #1 (Public review)

Summary:

This study by Park and colleagues uses longitudinal saliva viral load data from two cohorts (one in the US and one in Japan from a clinical trial) in the pre-vaccine era to subset viral shedding kinetics and then use machine learning to attempt to identify clinical correlates of different shedding patterns. The stratification method identifies three separate shedding patterns discriminated by peak viral load, shedding duration, and clearance slope. The authors also assess micro-RNAs as potential biomarkers of severity but do not identify any clear relationships with viral kinetics.

Strengths:

The cohorts are well developed, the mathematical model appears to capture shedding kinetics fairly well, the clustering seems generally appropriate, and the machine learning analysis is a sensible, albeit exploratory approach. The micro-RNA analysis is interesting and novel.

Weaknesses:

The conclusions of the paper are somewhat supported by the data but there are certain limitations that are notable and make the study's findings of only limited relevance to current COVID-19 epidemiology and clinical conditions.

We sincerely appreciate the reviewer’s thoughtful and constructive comments, which have been invaluable in improving the quality of our study. We have carefully revised the manuscript to address all points raised.

(1) The study only included previously uninfected, unvaccinated individuals without the omicron variant. It has been well documented that vaccination and prior infection both predict shorter duration shedding. Therefore, the study results are no longer relevant to current COVID-19 conditions. This is not at all the authors' fault but rather a difficult reality of much retrospective COVID research.

Thank you for your comment. We agree with the review’s comment that some of our results could not provide insight into the current COVID-19 conditions since most people have either already been infected with COVID-19 or have been vaccinated. We revised our manuscript to discuss this (page 22, lines 364-368). Nevertheless, we believe it is novel that we have extensively investigated the relationship between viral shedding patterns in saliva and a wide range of clinical and microRNA data, and that developing a method to do so remains important. This is important for providing insight into early responses to novel emerging viral diseases in the future. Therefore, we still believe that our findings are valuable.

(2) The target cell model, which appears to fit the data fairly well, has clear mechanistic limitations. Specifically, if such a high proportion of cells were to get infected, then the disease would be extremely severe in all cases. The authors could specify that this model was selected for ease of use and to allow clustering, rather than to provide mechanistic insight. It would be useful to list the AIC scores of this model when compared to the model by Ke.

Thank you for your feedback and suggestion regarding our mathematical model. As the reviewer pointed out, in this study, we adopted a simple model (target cell-limited model) to focus on reconstruction of viral dynamics and stratification of shedding patterns rather than exploring the mechanism of viral infection in detail. Nevertheless, we believe that the target cell-limited model provides reasonable reconstructed viral dynamics as it has been used in many previous studies. We revised manuscript to clarify this point (page 10, lines 139-144). Also, we revised our manuscript to provide more detailed description of the model comparison along with information about AIC (page 10, lines 130-135).

(3) Line 104: I don't follow why including both datasets would allow one model to work better than the other. This requires more explanation. I am also not convinced that non-linear mixed effects approaches can really be used to infer early model kinetics in individuals from one cohort by using late viral load kinetics in another (and vice versa). The approach seems better for making populationlevel estimates when there is such a high amount of missing data.

Thank you for your feedback. We recognized that our explanation was insufficient by your comment. We intended to describe that, rather than comparing performance of the two models, data fitting can be performed with same level for both models by including both datasets. We revised the manuscript to clarify this point (page 10, lines 135-139).

Additionally, we agree that nonlinear mixed effects models are a useful approach for performing population-level estimates of missing data. On the other hand, in addition, the nonlinear mixed effects model has the advantage of making the reasonable parameter estimation for each individual with not enough data points by considering the distribution of parameters of other individuals. Paying attention to these advantages, we adopted a nonlinear mixed effects model in our study. We also revised the manuscript to clarify this (page 27, lines 472-483).

(4) Along these lines, the three clusters appear to show uniform expansion slopes whereas the NBA cohort, a much larger cohort that captured early and late viral loads in most individuals, shows substantial variability in viral expansion slopes. In Figure 2D: the upslope seems extraordinarily rapid relative to other cohorts. I calculate a viral doubling time of roughly 1.5 hours. It would be helpful to understand how reliable of an estimate this is and also how much variability was observed among individuals.

We appreciate your detailed feedback on the estimated up-slope of viral dynamics. As the reviewer noted, the pattern differs from that observed in the NBA cohort, which may be due to their measurement of viral load from upper respiratory tract swabs. In our estimation, the mean and standard deviation of the doubling time (defined as ln2/(𝛽𝑇₀𝑝𝑐⁻¹ − 𝛿)) were 1.44 hours and 0.49 hours, respectively. Although direct validation of these values is challenging, several previous studies, including our own, have reported that viral loads in saliva increase more rapidly than in the upper respiratory tract swabs, reaching their peak sooner. Thus, we believe that our findings are consistent with those of previous studies. We revised our manuscript to discuss this point with additional references (page 20, lines 303-311).

(5) A key issue is that a lack of heterogeneity in the cohort may be driving a lack of differences between the groups. Table 1 shows that Sp02 values and lab values that all look normal. All infections were mild. This may make identifying biomarkers quite challenging.

Thank you for your comment regarding heterogeneity in the cohort. Although the NFV cohort was designed for COVID-19 patients who were either mild or asymptomatic, we have addressed this point and revised the manuscript to discuss it (page 21, lines 334-337).

(6) Figure 3A: many of the clinical variables such as basophil count, Cl, and protein have very low pre-test probability of correlating with virologic outcome.

Thank you for your comment regarding some clinical information we used in our study. We revised our manuscript to discuss this point (page 21, lines 337-338).

(7) A key omission appears to be micoRNA from pre and early-infection time points. It would be helpful to understand whether microRNA levels at least differed between the two collection timepoints and whether certain microRNAs are dynamic during infection.

Thank you for your comment regarding the collection of micro-RNA data. As suggested by the reviewer, we compared micro-RNA levels between two time points using pairwise t-tests and Mann-Whitney U tests with FDR correction. As a result, no micro-RNA showed a statistically significant difference. This suggests that micro-RNA levels remain relatively stable during the course of infection, at least for mild or asymptomatic infection, and may therefore serve as a biomarker independent of sampling time. We have revised the manuscript to include this information (page 17, lines 259-262).

(8) The discussion could use a more thorough description of how viral kinetics differ in saliva versus nasal swabs and how this work complements other modeling studies in the field.

We appreciate the reviewer’s thoughtful feedback. As suggested, we have added a discussion comparing our findings with studies that analyzed viral dynamics using nasal swabs, thereby highlighting the differences between viral dynamics in saliva and in the upper respiratory tract. To ensure a fair and rigorous comparison, we referred to studies that employed the same mathematical model (i.e., Eqs.(1-2)). Accordingly, we revised the manuscript and included additional references (page 20, lines 303-311).

Furthermore, we clarified the significance of our study in two key aspects. First, it provides a detailed analysis of viral dynamics in saliva, reinforcing our previous findings from a single cohort by extending them across multiple cohorts. Second, this study uniquely examines whether viral dynamics in saliva can be directly predicted by exploring diverse clinical data and micro-RNAs. Notably, cohorts that have simultaneously collected and reported both viral load and a broad spectrum of clinical data from the same individuals, as in our study, are exceedingly rare. We revised the manuscript to clarify this point (page 20, lines 302-311).

(9) The most predictive potential variables of shedding heterogeneity which pertain to the innate and adaptive immune responses (virus-specific antibody and T cell levels) are not measured or modeled.

Thank you for your comment. We agree that antibody and T cell related markers may serve as the most powerful predictors, as supported by our own study [S. Miyamoto et al., PNAS (2023), ref. 24] as well as previous reports. While this point was already discussed in the manuscript, we have revised the text to make it more explicit (page 21, lines 327-328).

(10) I am curious whether the models infer different peak viral loads, duration, expansion, and clearance slopes between the 2 cohorts based on fitting to different infection stage data.

Thank you for your comment. We compared features between 2 cohorts as reviewer suggested. As a result, a statistically significant difference between the two cohorts (i.e., p-value ≤ 0.05 from the t-test) was observed only at the peak viral load, with overall trends being largely similar. At the peak, the mean value was 7.5 log₁₀ (copies/mL) in the Japan cohort and 8.1 log₁₀ (copies/mL) in the Illinois cohort, with variances of 0.88 and 0.87, respectively, indicating comparable variability.

Reviewer #2 (Public review)

Summary:

This study argues it has found that it has stratified viral kinetics for saliva specimens into three groups by the duration of "viral shedding"; the authors could not identify clinical data or microRNAs that correlate with these three groups.

Strengths:

The question of whether there is a stratification of viral kinetics is interesting.

Weaknesses:

The data underlying this work are not treated rigorously. The work in this manuscript is based on PCR data from two studies, with most of the data coming from a trial of nelfinavir (NFV) that showed no effect on the duration of SARS-CoV-2 PCR positivity. This study had no PCR data before symptom onset, and thus exclusively evaluated viral kinetics at or after peak viral loads. The second study is from the University of Illinois; this data set had sampling prior to infection, so has some ability to report the rate of "upswing." Problems in the analysis here include:

We are grateful to the reviewer for the constructive feedback, which has greatly enhanced the quality of our study. In response, we have carefully revised the manuscript to address all comments.

The PCR Ct data from each study is treated as equivalent and referred to as viral load, without any reports of calibration of platforms or across platforms. Can the authors provide calibration data and justify the direct comparison as well as the use of "viral load" rather than "Ct value"? Can the authors also explain on what basis they treat Ct values in the two studies as identical?

Thank you for your comment regarding description of viral load data. We recognized the lack of explanation for the integration of viral load data by reviewer's comment. We calculated viral load from Ct value using linear regression equations between Ct and viral load for each study's measurement method, respectively. We revised the manuscript to clarify this point in the section of Saliva viral load data in Methods.

The limit of detection for the NFV PCR data was unclear, so the authors assumed it was the same as the University of Illinois study. This seems a big assumption, as PCR platforms can differ substantially. Could the authors do sensitivity analyses around this assumption?

Thank you for your comment regarding the detection limit for viral load data. As reviewer suggested, we conducted sensitivity analysis for assumption of detection limit for the NFV dataset. Specifically, we performed data fitting in the same manner for two scenarios: when the detection limit of NFV PCR was lower (0 log₁₀ copies/mL) or higher (2 log₁₀ copies/mL) than that of the Illinois data (1.08 log₁₀ copies/mL), and compared the results.

As a result, we obtained largely comparable viral dynamics in most cases (Supplementary Fig 6). When comparing the AIC values, we observed that the AIC for the same censoring threshold was 6836, whereas it increased to 7403 under the low censoring threshold and decreased to 6353 under the higher censoring threshold. However, this difference may be attributable to the varying number of data points treated as below the detection limit. Specifically, when the threshold is set higher, more data are treated as below the detection limit, which may result in a more favorable error calculation. To discuss this point, we have added a new figure (Supplementary Fig 6) and revised the manuscript accordingly (page 25, lines 415-418).

The authors refer to PCR positivity as viral shedding, but it is viral RNA detection (very different from shedding live/culturable virus, as shown in the Ke et al. paper). I suggest updating the language throughout the manuscript to be precise on this point.

We appreciate the reviewer’s feedback regarding the terminology used for viral shedding. In response, we have revised all instances of “viral shedding” to “viral RNA detection” throughout the manuscript as suggested.

Eyeballing extended data in Figure 1, a number of the putative long-duration infections appear to be likely cases of viral RNA rebound (for examples, see S01-16 and S01-27). What happens if all the samples that look like rebound are reanalyzed to exclude the late PCR detectable time points that appear after negative PCRs?

We sincerely thank the reviewer for the valuable suggestion. In response, we established a criterion to remove data that appeared to exhibit rebound and subsequently performed data fitting

(see Author response image 1 below). The criterion was defined as: “any data that increase again after reaching the detection limit in two measurements are considered rebound and removed.” As a result, 15 out of 144 cases were excluded due to insufficient usable data, leaving 129 cases for analysis. Using a single detection limit as the criterion would have excluded too many data points, while defining the criterion solely based on the magnitude of increase made it difficult to establish an appropriate “threshold for increase.”

The fitting result indicates that the removal of rebound data may influence the fitting results; however, direct comparison of subsequent analyses, such as clustering, is challenging due to the reduced sample size. Moreover, the results can vary substantially depending on the criterion used to define rebound, and establishing a consistent standard remains difficult. Accordingly, we retained the current analysis and have added a discussion of rebound phenomena in the Discussion section as a limitation (page 22, lines 355-359). We once again sincerely appreciate the reviewer’s insightful and constructive suggestion.

Author response image 1.

Comparison of model fits before and after removing data suspected of rebound. Black dots represent observed measurements, and the black and yellow curves show the fitted viral dynamics for the full dataset and the dataset with rebound data removed, respectively.

There's no report of uncertainty in the model fits. Given the paucity of data for the upslope, there must be large uncertainty in the up-slope and likely in the peak, too, for the NFV data. This uncertainty is ignored in the subsequent analyses. This calls into question the efforts to stratify by the components of the viral kinetics. Could the authors please include analyses of uncertainty in their model fits and propagate this uncertainty through their analyses?

We sincerely appreciate the reviewer’s detailed feedback on model uncertainty. To address this point, we revised Extended Fig 1 (now renumbered as Supplementary Fig 1) to include 95% credible intervals computed using a bootstrap approach. In addition, to examine the potential impact of model uncertainty on stratified analyses, we reconstructed the distance matrix underlying stratification by incorporating feature uncertainty. Specifically, for each individual, we sampled viral dynamics within the credible interval and averaged the resulting feature, and build the distance matrix using it. We then compared this uncertainty-adjusted matrix with the original one using the Mantel test, which showed a strong correlation (r = 0.72, p < 0.001). Given this result, we did not replace the current stratification but revised the manuscript to provide this information through Result and Methods sections (page 11, lines 159-162 and page 28, lines 512-519). Once again, we are deeply grateful for this insightful comment.

The clinical data are reported as a mean across the course of an infection; presumably vital signs and blood test results vary substantially, too, over this duration, so taking a mean without considering the timing of the tests or the dynamics of their results is perplexing. I'm not sure what to recommend here, as the timing and variation in the acquisition of these clinical data are not clear, and I do not have a strong understanding of the basis for the hypothesis the authors are testing.

We appreciate the reviewers' feedback on the clinical data. We recognized that the manuscript lacked description of the handling of clinical data by your comment. In this research, we focused on finding “early predictors” which could provide insight into viral shedding patterns. Thus, we used clinical data measured in the earliest time (date of admission) for each patient. Another reason is that the date of admission is the almost only time point at which complete clinical data without any missing values are available for all participants. We revised our manuscript to clarify this point (page 5, lines 90-95).

It's unclear why microRNAs matter. It would be helpful if the authors could provide more support for their claims that (1) microRNAs play such a substantial role in determining the kinetics of other viruses and (2) they play such an important role in modulating COVID-19 that it's worth exploring the impact of microRNAs on SARS-CoV-2 kinetics. A link to a single review paper seems insufficient justification. What strong experimental evidence is there to support this line of research?

We appreciate the reviewer’s comments regarding microRNA. Based on this feedback, we recognized the need to clarify our rationale for selecting microRNAs as the analyte. The primary reason was that our available specimens were saliva, and microRNAs are among the biomarkers that can be reliably measured in saliva. At the same time, previous studies have reported associations between microRNAs and various diseases, which led us to consider the potential relevance of microRNAs to viral dynamics, beyond their role as general health indicators. To better reflect this context, we have added supporting references (page 17, lines 240-243).

Reviewer #3 (Public review)

The article presents a comprehensive study on the stratification of viral shedding patterns in saliva among COVID-19 patients. The authors analyze longitudinal viral load data from 144 mildly symptomatic patients using a mathematical model, identifying three distinct groups based on the duration of viral shedding. Despite analyzing a wide range of clinical data and micro-RNA expression levels, the study could not find significant predictors for the stratified shedding patterns, highlighting the complexity of SARS-CoV-2 dynamics in saliva. The research underscores the need for identifying biomarkers to improve public health interventions and acknowledges several limitations, including the lack of consideration of recent variants, the sparsity of information before symptom onset, and the focus on symptomatic infections. 

The manuscript is well-written, with the potential for enhanced clarity in explaining statistical methodologies. This work could inform public health strategies and diagnostic testing approaches. However, there is a thorough development of new statistical analysis needed, with major revisions to address the following points:

We sincerely appreciate the thoughtful feedback provided by Reviewer #3, particularly regarding our methodology. In response, we conducted additional analyses and revised the manuscript accordingly. Below, we address the reviewer’s comments point by point.

(1) Patient characterization & selection: Patient immunological status at inclusion (and if it was accessible at the time of infection) may be the strongest predictor for viral shedding in saliva. The authors state that the patients were not previously infected by SARS-COV-2. Was Anti-N antibody testing performed? Were other humoral measurements performed or did everything rely on declaration? From Figure 1A, I do not understand the rationale for excluding asymptomatic patients. Moreover, the mechanistic model can handle patients with only three observations, why are they not included? Finally, the 54 patients without clinical data can be used for the viral dynamics fitting and then discarded for the descriptive analysis. Excluding them can create a bias. All the discarded patients can help the virus dynamics analysis as it is a population approach. Please clarify. In Table 1 the absence of sex covariate is surprising.

We appreciate the detailed feedback from the reviewer regarding patient selection. We relied on the patient's self-declaration to determine the patient's history of COVID-19 infection and revised the manuscript to specify this (page 6, lines 83-84).

In parameter estimation, we used the date of symptom onset for each patient so that we establish a baseline of the time axis as clearly as possible, as we did in our previous works. Accordingly, asymptomatic patients who do not have information on the date of symptom onset were excluded from the analysis. Additionally, in the cohort we analyzed, for patients excluded due to limited number of observations (i.e., less than 3 points), most patients already had a viral load close to the detection limit at the time of the first measurement. This is due to the design of clinical trial, as if a negative result was obtained twice in a row, no further follow-up sampling was performed. These patients were excluded from the analysis because it hard to get reasonable fitting results. Also, we used 54 patients for the viral dynamics fitting and then only used the NFV cohort for clinical data analysis. We acknowledge that our description may have confused readers. We revised our manuscript to clarify these points regarding patient selecting for data fitting (page 6, lines 96-102, page 24, lines 406-407, and page 7, lines 410-412). In addition, we realized, thanks to the reviewer’s comment, that gender information was missing in Table 1. We appreciate this observation and have revised the table to include gender (we used gender in our analysis). 

(2) Exact study timeline for explanatory covariates: I understand the idea of finding « early predictors » of long-lasting viral shedding. I believe it is key and a great question. However, some samples (Figure 4A) seem to be taken at the end of the viral shedding. I am not sure it is really easier to micro-RNA saliva samples than a PCR. So I need to be better convinced of the impact of the possible findings. Generally, the timeline of explanatory covariate is not described in a satisfactory manner in the actual manuscript. Also, the evaluation and inclusion of the daily symptoms in the analysis are unclear to me.

We appreciate the reviewer’s feedback regarding the collection of explanatory variables. As noted, of the two microRNA samples collected from each patient, one was obtained near the end of viral shedding. This was intended to examine potential differences in microRNA levels between the early and late phases of infection. No significant differences were observed between the two time points, and using microRNA from either phase alone or both together did not substantially affect predictive accuracy for stratified groups. Furthermore, microRNA collection was motivated primarily by the expectation that it would be more sensitive to immune responses, rather than by ease of sampling. We have revised the manuscript to clarify these points regarding microRNA (page 17, lines 243-245 and 259-262).

Furthermore, as suggested by the reviewer, we have also strengthened the explanation regarding the collection schedule of clinical information and the use of daily symptoms in the analysis (page 6, lines 90-95, page 14, lines 218-220,).

(3) Early Trajectory Differentiation: The model struggles to differentiate between patients' viral load trajectories in the early phase, with overlapping slopes and indistinguishable viral load peaks observed in Figures 2B, 2C, and 2D. The question arises whether this issue stems from the data, the nature of Covid-19, or the model itself. The authors discuss the scarcity of pre-symptom data, primarily relying on Illinois patients who underwent testing before symptom onset. This contrasts earlier statements on pages 5-6 & 23, where they claim the data captures the full infection dynamics, suggesting sufficient early data for pre-symptom kinetics estimation. The authors need to provide detailed information on the number or timing of patient sample collections during each period.

Thank you for the reviewer’s thoughtful comments. The model used in this study [Eqs.(1-2)] has been employed in numerous prior studies and has successfully identified viral dynamics at the individual level. In this context, we interpret the rapid viral increase observed across participants as attributable to characteristics of SARS-CoV-2 in saliva, an interpretation that has also been reported by multiple previous studies. We have added the relevant references and strengthened the corresponding discussion in the manuscript (page 20, lines 303-311).

We acknowledge that our explanation of how the complementary relationship between the two cohorts contributes to capturing infection dynamics was not sufficiently clear. As described in the manuscript, the Illinois cohort provides pre-symptomatic data, whereas the NFV cohort offers abundant end-phase data, thereby compensating for each other’s missing phases. By jointly analyzing the two cohorts with a nonlinear mixed-effects model, we estimated viral dynamics at the individual-level. This approach first estimates population-level parameters (fixed effects) using data from all participants and then incorporates random effects to account for individual variability, yielding the most plausible parameter values.

Thus, even when early-phase data are lacking in the NFV cohort, information from the Illinois cohort allows us to infer most reasonable dynamics, and the reverse holds true for the end phase. In this context, we argued that combining the two cohorts enables mathematical modeling to capture infection dynamics at the individual level. Recognizing that our earlier description could be misleading, we have carefully reinforced the relevant description (page 27, lines 472-483). In addition, as suggested by the reviewer, we have added information on the number of data samples available for each phase in both cohorts (page 7, lines 106-109).

(4) Conditioning on the future: Conditioning on the future in statistics refers to the problematic situation where an analysis inadvertently relies on information that would not have been available at the time decisions were made or data were collected. This seems to be the case when the authors create micro-RNA data (Figure 4A). First, when the sampling times are is something that needs to be clarified by the authors (for clinical outcomes as well). Second, proper causal inference relies on the assumption that the cause precedes the effect. This conditioning on the future may result in overestimating the model's accuracy. This happens because the model has been exposed to the outcome it's supposed to predict. This could question the - already weak - relation with mir-1846 level.

We appreciate the reviewer’s detailed feedback. As noted in Reply to Comments 2, we collected micro-RNA samples at two time points, near the peak of infection dynamics and at the end stage, and found no significant differences between them. This suggests that micro-RNA levels are not substantially affected by sampling time. Indeed, analyses conducted using samples from the peak, late stage, or both yielded nearly identical results in relation to infection dynamics. To clarify this point, we revised the manuscript by integrating this explanation with our response in Reply to Comments 2 (page 17, lines 259-262). In addition, now we also revised manuscript to clarify sampling times of clinical information and micro-RNA (page 6, lines 90-95).

(5) Mathematical Model Choice Justification and Performance: The paper lacks mention of the practical identifiability of the model (especially for tau regarding the lack of early data information). Moreover, it is expected that the immune effector model will be more useful at the beginning of the infection (for which data are the more parsimonious). Please provide AIC for comparison, saying that they have "equal performance" is not enough. Can you provide at least in a point-by-point response the VPC & convergence assessments?

We appreciate the reviewer’s detailed feedback regarding the mathematical model. We acknowledge the potential concern regarding the practical identifiability of tau (incubation period), particularly given the limited early-phase data. In our analysis, however, the nonlinear mixed-effects model yielded a population-level estimate of 4.13 days, which is similar with previously reported incubation periods for COVID-19. This concordance suggests that our estimate of tau is reasonable despite the scarcity of early data.

For model comparison, first, we have added information on the AIC of the two models to the manuscript as suggested by the reviewer (page 10, lines 130-135). One point we would like to emphasize is that we adopted a simple target cell-limited model in this study, aiming to focus on reconstruction of viral dynamics and stratification of shedding patterns rather than exploring the mechanism of viral infection in detail. Nevertheless, we believe that the target cell-limited model provides reasonable reconstructed viral dynamics as it has been used in many previous studies. We revised manuscript to clarify this (page 10, lines 135-144). 

Furthermore, as suggested, we have added the VPC and convergence assessment results for both models, together with explanatory text, to the manuscript (Supplementary Fig 2, Supplementary Fig 3, and page 10, lines 130-135). In the VPC, the observed 5th, 50th, and 95th percentiles were generally within the corresponding simulated prediction intervals across most time points. Although minor deviations were noted in certain intervals, the overall distribution of the observed data was well captured by the models, supporting their predictive performance (Supplementary Fig 2). In addition, the log-likelihood and SAEM parameter trajectories stabilized after the burn-in phase, confirming appropriate convergence (Supplementary Fig 3).

(6) Selected features of viral shedding: I wonder to what extent the viral shedding area under the curve (AUC) and normalized AUC should be added as selected features.

We sincerely appreciate the reviewer’s valuable suggestion regarding the inclusion of additional features. Following this recommendation, we considered AUC (or normalized AUC) as an additional feature when constructing the distance matrix used for stratification. We then evaluated the similarity between the resulting distance matrix and the original one using the Mantel test, which showed a very high correlation (r = 0.92, p < 0.001). This indicates that incorporating AUC as an additional feature does not substantially alter the distance matrix. Accordingly, we have decided to retain the current stratification analysis, and we sincerely thank the reviewer once again for this interesting suggestion.

(7) Two-step nature of the analysis: First you fit a mechanistic model, then you use the predictions of this model to perform clustering and prediction of groups (unsupervised then supervised). Thus you do not propagate the uncertainty intrinsic to your first estimation through the second step, ie. all the viral load selected features actually have a confidence bound which is ignored. Did you consider a one-step analysis in which your covariates of interest play a direct role in the parameters of the mechanistic model as covariates? To pursue this type of analysis SCM (Johnson et al. Pharm. Res. 1998), COSSAC (Ayral et al. 2021 CPT PsP), or SAMBA ( Prague et al. CPT PsP 2021) methods can be used. Did you consider sampling on the posterior distribution rather than using EBE to avoid shrinkage?

Thank you for the reviewer’s detailed suggestions regarding our analysis. We agree that the current approach does not adequately account for the impact of uncertainty in viral dynamics on the stratified analyses. As a first step, we have revised Extended Data Fig 1 (now renumbered as Supplementary Fig 1) to include 95% credible intervals computed using a bootstrap approach, to present the model-fitting uncertainty more explicitly. Then, to examine the potential impact of model uncertainty on stratified analyses, we reconstructed the distance matrix underlying stratification by incorporating feature uncertainty. Specifically, for each individual, we sampled viral dynamics within the credible interval and averaged the resulting feature, and build the distance matrix using it. We then compared this uncertainty-adjusted matrix with the original one using the Mantel test, which showed a strong correlation (r = 0.72, p < 0.001). Given this result, we did not replace the current stratification but revised the manuscript to provide this information (page 11, lines 159-162 and page 28, 512-519).

Furthermore, we carefully considered the reviewer’s proposed one-step analysis. However, implementation was constrained by data-fitting limitations. Concretely, clinical information is available only in the NFV cohort. Thus, if these variables are to be entered directly as covariates on the parameters, the Illinois cohort cannot be included in the data-fitting process. Yet the NFV cohort lacks any pre-symptomatic observations, so fitting the model to that cohort alone does not permit a reasonable (well-identified/robust) fitting result. While we were unable to implement the suggestion under the current data constraints, we sincerely appreciate the reviewer’s thoughtful and stimulating proposal.

(8) Need for advanced statistical methods: The analysis is characterized by a lack of power. This can indeed come from the sample size that is characterized by the number of data available in the study. However, I believe the power could be increased using more advanced statistical methods. At least it is worth a try. First considering the unsupervised clustering, summarizing the viral shedding trajectories with features collapses longitudinal information. I wonder if the R package « LongituRF » (and associated method) could help, see Capitaine et al. 2020 SMMR. Another interesting tool to investigate could be latent class models R package « lcmm » (and associated method), see ProustLima et al. 2017 J. Stat. Softwares. But the latter may be more far-reached.

Thank you for the reviewer’s thoughtful suggestions regarding our unsupervised clustering approach. The R package “LongitiRF” is designed for supervised analysis, requiring a target outcome to guide the calculation of distances between individuals (i.e., between viral dynamics). In our study, however, the goal was purely unsupervised clustering, without any outcome variable, making direct application of “LongitiRF” challenging.

Our current approach (summarizing each dynamic into several interpretable features and then using Random Forest proximities) allows us to construct a distance matrix in an unsupervised manner. Here, the Random Forest is applied in “proximity mode,” focusing on how often dynamics are grouped together in the trees, independent of any target variable. This provides a practical and principled way to capture overall patterns of dynamics while keeping the analysis fully unsupervised.

Regarding the suggestion to use latent class mixed models (R package “lcmm”), we also considered this approach. In our dataset, each subject has dense longitudinal measurements, and at many time points, trajectories are very similar across subjects, resulting in minimal inter-individual differences. Consequently, fitting multi-class latent class mixed models (ng ≥ 2) with random effects or mixture terms is numerically unstable, often producing errors such as non-positive definite covariance matrices or failure to generate valid initial values. Although one could consider using only the time points with the largest differences, this effectively reduces the analysis to a feature-based summary of dynamics. Such an approach closely resembles our current method and contradicts the goal of clustering based on full longitudinal information.

Taken together, although we acknowledge that incorporating more longitudinal information is important, we believe that our current approach provides a practical, stable, and informative solution for capturing heterogeneity in viral dynamics. We would like to once again express our sincere gratitude to the reviewer for this insightful suggestion.

(9) Study intrinsic limitation: All the results cannot be extended to asymptomatic patients and patients infected with recent VOCs. It definitively limits the impact of results and their applicability to public health. However, for me, the novelty of the data analysis techniques used should also be taken into consideration.

We appreciate your positive evaluation of our research approach and acknowledge that, as noted in the Discussion section as our first limitation, our analysis may not provide valid insights into recent VOCs or all populations, including asymptomatic individuals. Nonetheless, we believe it is novel that we extensively investigated the relationship between viral shedding patterns in saliva and a wide range of clinical and micro-RNA data. Our findings contribute to a deeper and more quantitative understanding of heterogeneity in viral dynamics, particularly in saliva samples. To discuss this point, we revised our manuscript (page 22, lines 364-368).

Strengths are:

Unique data and comprehensive analysis.

Novel results on viral shedding.

Weaknesses are:

Limitation of study design.

The need for advanced statistical methodology.

Reviewer #1 (Recommendations For The Authors):

Line 8: In the abstract, it would be helpful to state how stratification occurred.

We thank the reviewer for the feedback, and have revised the manuscript accordingly (page 2, lines 8-11).

Line 31 and discussion: It is important to mention the challenges of using saliva as a specimen type for lab personnel.

We thank the reviewer for the feedback, and have revised the manuscript accordingly (page 3, lines 36-41).

Line 35: change to "upper respiratory tract".

We thank the reviewer for the feedback, and have revised the manuscript accordingly (page 3, line 35).

Line 37: "Saliva" is not a tissue. Please hazard a guess as to which tissue is responsible for saliva shedding and if it overlaps with oral and nasal swabs.

We thank the reviewer for the feedback, and have revised the manuscript accordingly (page 3, lines 42-45).

Line 42, 68: Please explain how understanding saliva shedding dynamics would impact isolation & screening, diagnostics, and treatments. This is not immediately intuitive to me.

We thank the reviewer for the feedback, and have revised the manuscript accordingly (page 3, lines 48-50).

Line 50: It would be helpful to explain why shedding duration is the best stratification variable.

We thank the reviewer for the feedback. We acknowledge that our wording was ambiguous. The clear differences in the viral dynamics patterns pertain to findings observed following the stratification, and we have revised the manuscript to make this explicit (page 4, lines 59-61).

Line 71: Dates should be listed for these studies.

We thank the reviewer for the feedback, and have revised the manuscript accordingly (page 6, lines 85-86).

Reviewer #2 (Recommendations For The Authors):

Please make all code and data available for replication of the analyses.

We appreciate the suggestion. Due to ethical considerations, it is not possible to make all data and code publicly available. We have clearly stated in the manuscript about it (Data availability section in Methods).

Reviewer #3 (Recommendations For The Authors):

Here are minor comments / technical details:

(1) Figure 1B is difficult to understand.

Thank you for the comment. We updated Fig 1B to incorporate more information to aid interpretation.

(2) Did you analyse viral load or the log10 of viral load? The latter is more common. You should consider it. SI Figure 1 please plot in log10 and use a different point shape for censored data. The file quality of this figure should be improved. State in the material and methods if SE with moonlit are computed with linearization or importance sampling.

Thank you for the comment. We conducted our analyses using log10-transformed viral load. Also, we revised Supplementary Fig 1 (now renumbered as Supplementary Fig 4) as suggested. We also added Supplementary Fig 3 and clarified in the Methods that standard errors (SE) were obtained in Monolix from the Fisher information matrix using the linearization method (page 28, lines 498-499).

(3) Table 1 and Figure 3A could be collapsed.

Thank you for the comment, and we carefully considered this suggestion. Table 1 summarizes clinical variables by category, whereas Fig 3A visualizes them ordered by p-value of statistical analysis. Collapsing these into a single table would make it difficult to apprehend both the categorical summaries and the statistical ranking at a glance, thereby reducing readability. We therefore decided to retain the current layout. We appreciate the constructive feedback again. 

(4) Figure 3 legend could be clarified to understand what is 3B and 3C.

We thank the reviewer for the feedback and have reinforced the description accordingly.

(5) Why use AIC instead of BICc?

Thank you for your comment. We also think BICc is a reasonable alternative. However, because our objective is predictive adequacy (reconstruction of viral dynamics), we judged AIC more appropriate. In NLMEM settings, the effective sample size required by BICc is ambiguous, making the penalty somewhat arbitrary. Moreover, since the two models reconstruct very similar dynamics, our conclusions are not sensitive to the choice of criterion.

(6) Bibliography. Most articles are with et al. (which is not standard) and some are with an extended list of names. Provide DOI for all.

We thank the reviewer for the feedback, and have revised the manuscript accordingly.

(7) Extended Table 1&2 - maybe provide a color code to better highlight some lower p-values (if you find any interesting).

We thank the reviewer for the feedback. Since no clinical information and micro-RNAs other than mir-1846 showed low p-values, we highlighted only mir-1846 with color to make it easier to locate.

(8) Please make the replication code available.

We appreciate the suggestion. Due to ethical considerations, it is not possible to make all data and code publicly available. We have clearly stated in the manuscript about it (Data availability section in Methods).

Author response:

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

Reviewer #1 (Public review): 

Summary: 

In this work, van Paassen et al. have studied how CD8 T cell functionality and levels predict HIV DNA decline. The article touches on interesting facets of HIV DNA decay, but ultimately comes across as somewhat hastily done and not convincing due to the major issues. 

(1) The use of only 2 time points to make many claims about longitudinal dynamics is not convincing. For instance, the fact that raw data do not show decay in intact, but do for defective/total, suggests that the present data is underpowered. The authors speculate that rising intact levels could be due to patients who have reservoirs with many proviruses with survival advantages, but this is not the parsimonious explanation vs the data simply being noisy without sufficient longitudinal follow-up. n=12 is fine, or even reasonably good for HIV reservoir studies, but to mitigate these issues would likely require more time points measured per person. 

(1b) Relatedly, the timing of the first time point (6 months) could be causing a number of issues because this is in the ballpark for when the HIV DNA decay decelerates, as shown by many papers. This unfortunate study design means some of these participants may already have stabilized HIV DNA levels, so earlier measurements would help to observe early kinetics, but also later measurements would be critical to be confident about stability. 

The main goal of the present study was to understand the relationship of the HIV-specific CD8 T-cell responses early on ART with the reservoir changes across the subsequent 2.5-year period on suppressive therapy. We have revised the manuscript in order to clarify this.  We chose these time points because the 24 week time point is past the initial steep decline of HIV DNA, which takes place in the first weeks after ART initiation. It is known that HIV DNA continues to decay for years after (Besson, Lalama et al. 2014, Gandhi, McMahon et al. 2017). 

(2) Statistical analysis is frequently not sufficient for the claims being made, such that overinterpretation of the data is problematic in many places. 

(2a) First, though plausible that cd8s influence reservoir decay, much more rigorous statistical analysis would be needed to assert this directionality; this is an association, which could just as well be inverted (reservoir disappearance drives CD8 T cell disappearance). 

To correlate different reservoir measures between themselves and with CD8+ T-cell responses at 24 and 156 weeks, we now performed non-parametric (Spearman) correlation analyses, as they do not require any assumptions about the normal distribution of the independent and dependent variables. Benjamini-Hochberg corrections for multiple comparisons (false discovery rate, 0.25) were included in the analyses and did not change the results. 

Following this comment we would like to note that the association between the T-cell response at 24 weeks and the subsequent decrease in the reservoir cannot be bi-directional (that can only be the case when both variables are measured at the same time point). Therefore, to model the predictive value of T-cell responses measured at 24 weeks for the decrease in the reservoir between 24 and 156 weeks, we fitted generalized linear models (GLM), in which we included age and ART regimen, in addition to three different measures of HIV-specific CD8+ T-cell responses, as explanatory variables, and changes in total, intact, and total defective HIV DNA between 24 and 156 weeks ART as dependent variables.

(2b) Words like "strong" for correlations must be justified by correlation coefficients, and these heat maps indicate many comparisons were made, such that p-values must be corrected appropriately. 

We have now used Spearman correlation analysis, provided correlation coefficients to justify the wording, and adjusted the p-values for multiple comparisons (Fig. 1, Fig 3., Table 2). Benjamini-Hochberg corrections for multiple comparisons (false discovery rate, 0.25) were included in the analyses and did not change the results.  

(3) There is not enough introduction and references to put this work in the context of a large/mature field. The impacts of CD8s in HIV acute infection and HIV reservoirs are both deep fields with a lot of complexity. 

Following this comment we have revised and expanded the introduction to put our work more in the context of the field (CD8s in acute HIV and HIV reservoirs). 

Reviewer #2 (Public review): 

Summary: 

This study investigated the impact of early HIV specific CD8 T cell responses on the viral reservoir size after 24 weeks and 3 years of follow-up in individuals who started ART during acute infection. Viral reservoir quantification showed that total and defective HIV DNA, but not intact, declined significantly between 24 weeks and 3 years post-ART. The authors also showed that functional HIV-specific CD8⁺ T-cell responses persisted over three years and that early CD8⁺ T-cell proliferative capacity was linked to reservoir decline, supporting early immune intervention in the design of curative strategies. 

Strengths: 

The paper is well written, easy to read, and the findings are clearly presented. The study is novel as it demonstrates the effect of HIV specific CD8 T cell responses on different states of the HIV reservoir, that is HIV-DNA (intact and defective), the transcriptionally active and inducible reservoir. Although small, the study cohort was relevant and well-characterized as it included individuals who initiated ART during acute infection, 12 of whom were followed longitudinally for 3 years, providing unique insights into the beneficial effects of early treatment on both immune responses and the viral reservoir. The study uses advanced methodology. I enjoyed reading the paper. 

Weaknesses: 

All participants were male (acknowledged by the authors), potentially reducing the generalizability of the findings to broader populations. A control group receiving ART during chronic infection would have been an interesting comparison. 

We thank the reviewer for their appreciation of our study. Although we had indeed acknowledged the fact that all participants were male, we have clarified why this is a limitation of the study (Discussion, lines 296-298). The reviewer raises the point that it would be useful to compare our data to a control group. Unfortunately, these samples are not yet available, but our study protocol allows for a control group (chronic infection) to ensure we can include a control group in the future.

Reviewer #1 (Recommendations for the authors): 

Minor: 

On the introduction: 

(1) One large topic that is mostly missing completely is the emerging evidence of selection on HIV proviruses during ART from the groups of Xu Yu and Matthias Lichterfeld, and Ya Chi Ho, among others. 

Previously, it was only touched upon in the Discussion. Now we have also included this in the Introduction (lines 77-80).

(2) References 4 and 5 don't quite match with the statement here about reservoir seeding; we don't completely understand this process, and certainly, the tissue seeding aspect is not known. 

Line 61-62: references were changed and this paragraph was rewritten to clarify.

(3) Shelton et al. showed a strong relationship with HIV DNA size and timing of ART initiation across many studies. I believe Ananwaronich also has several key papers on this topic. 

References by Ananwaronich are included (lines 91-94).

(4) "the viral levels decline within weeks of AHI", this is imprecise, there is a peak and a decline, and an equilibrium. 

We agree and have rewritten the paragraph accordingly.

(5) The impact of CD8 cells on viral evolution during primary infection is complex and likely not relevant for this paper. 

We have left viral evolution out of the introduction in order to keep a focus on the current subject.

(6) The term "reservoir" is somewhat polarizing, so it might be worth mentioning somewhere exactly what you think the reservoir is, I think, as written, your definition is any HIV DNA in a person on ART? 

Indeed, we refer to the reservoir when we talk about the several aspects of the reservoir that we have quantified with our assays (total HIV DNA, unspliced RNA, intact and defective proviral DNA, and replication-competent virus). In most instances we try to specify which measurement we are referring to. We have added additional reservoir explanation to clarify our definition to the introduction (lines 55-58).

(7) I think US might be used before it is defined. 

We thank the reviewer for this notification, we have now also defined it in the Results section (line 131).

(8) In Figure 1 it's also not clear how statistics were done to deal with undetectable values, which can be tricky but important. 

We have now clarified this in the legend to Figure 2 (former Figure 1). Paired Wilcoxon tests were performed to test the significance of the differences between the time points. Pairs where both values were undetectable were always excluded from the analysis. Pairs where one value was undetectable and its detection limit was higher than the value of the detectable partner, were also excluded from the analysis. Pairs where one value was undetectable and its detection limit was lower than the value of the detectable partner, were retained in the analysis.

In the discussion: 

(1) "This confirms that the existence of a replication-competent viral reservoir is linked to the presence of intact HIV DNA." I think this statement is indicative of many of the overinterpretations without statistical justification. There are 4 of 12 individuals with QVOA+ detectable proviruses, which means there are 8 without. What are their intact HIV DNA levels? 

We thank the reviewer for the question that is raised here. We have now compared the intact DNA levels (measured by IPDA) between participants with positive vs. negative QVOA output, and observed a significant difference. We rephrased the wording as follows: “We compared the intact HIV DNA levels at the 24-week timepoint between the six participants, from whom we were able to isolate replicating virus, and the fourteen participants, from whom we could not. Participants with positive QVOA had significantly higher intact HIV DNA levels than those with negative QVOA (p=0.029, Mann-Whitney test; Suppl. Fig. 3). Five of six participants with positive QVOA had intact DNA levels above 100 copies/106 PBMC, while thirteen of fourteen participants with negative QVOA had intact HIV DNA below 100 copies/106 PBMC (p=0.0022, Fisher’s exact test). These findings indicate that recovery of replication-competent virus by QVOA is more likely in individuals with higher levels of intact HIV DNA in IPDA, reaffirming a link between the two measurements.”

(2) "To determine whether early HIV-specific CD8+ T-cell responses at 24 weeks were predictive for the change in reservoir size". This is a fundamental miss on correlation vs causation... it could be the inverse. 

We thank the reviewer for the remark. We have calculated the change in reservoir size (the difference between the reservoir size at 24 weeks and 156 weeks ART) and analyzed if the HIVspecific CD8+ T-cell response at 24 weeks ART are predictive for this change. We do not think it can be inverse, as we have a chronological relationship (CD8+ responses at week 24 predict the subsequent change in the reservoir).

(3) "This may suggest that active viral replication drives the CD8+ T-cell response." I think to be precise, you mean viral transcription drives CD8s, we don't know about the full replication cycle from these data. 

We agree with the reviewer and have changed “replication” to “transcription” (line 280).

(4) "Remarkably, we observed that the defective HIV DNA levels declined significantly between 24 weeks and 3 years on ART. This is in contrast to previous observations in chronic HIV infection (30)". I don't find this remarkable or in contrast: many studies have analyzed and/or modeled defective HIV DNA decay, most of which have shown some negative slope to defective HIV DNA, especially within the first year of ART. See White et al., Blankson et al., Golob et al., Besson et al., etc In addition, do you mean in long-term suppressed? 

The point we would like to make is that,  compared to other studies, we found a significant, prominent decrease in defective DNA (and not intact DNA) over the course of 3 years, which is in contrast to other studies (where usually the decrease in intact is significant and the decrease in defective less prominent). We have rephrased the wording (lines 227-230) as follows:

“We observed that the defective HIV DNA levels decreased significantly between 24 and 156 weeks of ART. This is different from studies in CHI, where no significant decrease during the first 7 years of ART (Peluso, Bacchetti et al. 2020, Gandhi, Cyktor et al. 2021), or only a significant decrease during the first 8 weeks on ART, but not in the 8 years thereafter, was observed (Nühn, Bosman et al. 2025).”

Reviewer #2 (Recommendations for the authors): 

(1) Page 4, paragraph 2 - will be informative to report the statistics here. 

(2) Page 4, paragraph 4 - "General phenotyping of CD4+ (Suppl. Fig. 3A) and CD8+ (Supplementary Figure 3B) T-cells showed no difference in frequencies of naïve, memory or effector CD8+ T-cells between 24 and 156 weeks." - What did the CD4+ phenotyping show? 

We thank the reviewer for the remark. Indeed, there were also no differences in frequencies of naïve, memory or effector CD4+ T-cells between 24 and 156 weeks. We have added this to the paragraph (now Suppl. Fig 4), lines 166-168.

(3) Page 5, paragraph 3 - "Similarly, a broad HIV-specific CD8+ T-cell proliferative response to at least three different viral proteins was observed in the majority of individuals at both time points" - should specify n=? for the majority of individuals. 

At time point 24 weeks, 6/11 individuals had a response to env, 10/11 to gag, 5/11 to nef, and 4/11 to pol. At 156 weeks, 8/11 to env, 10/11 to gag, 8/11 to nef and 9/11 to pol. We have added this to the text (lines 188-191).

(4) Seven of 22 participants had non-subtype B infection. Can the authors explain the use of the IPDA designed by Bruner et. al. for subtype B HIV, and how this may have affected the quantification in these participants? 

Intact HIV DNA was detectable in all 22 participants. We cannot completely exclude influence of primer/probe-template mismatches on the quantification results, however such mismatches could also have occurred in subtype B participants, and droplet digital PCR that IPDA is based on is generally much less sensitive to these mismatches than qPCR.

(5) Page 7, paragraph 2 - the authors report a difference in findings from a previous study ("a decline in CD8 T cell responses over 2 years" - reference 21), but only provide an explanation for this on page 9. The authors should consider moving the explanation to this paragraph for easier understanding. 

We agree with the reviewer that this causes confusion. Therefore, we have revised and changed the order in the Discussion.

(6) Page 7, paragraph 2 - Following from above, the previous study (21) reported this contradicting finding "a decline in CD8 T cell responses over 2 years" in a CHI (chronic HIV) treated cohort. The current study was in an acute HIV treated cohort. The authors should explain whether this may also have resulted in the different findings, in addition to the use of different readouts in each study.

We thank the reviewer for this attentiveness. Indeed, the study by Takata et al. investigates the reservoir and HIV-specific CD8+ T-cell responses in both the RV254/ SEARCH010 study who initiated ART during AHI and the RV304/ SEARCH013 who initiated ART during CHI. We had not realized that the findings of the decline in CD8 T cell responses were solely found in the RV304/ SEARCH013 (CHI cohort). It appears functional HIV specific immune responses were only measured in AHI at 96 weeks, so we have clarified this in the Discussion. 

Besson, G. J., C. M. Lalama, R. J. Bosch, R. T. Gandhi, M. A. Bedison, E. Aga, S. A. Riddler, D. K. McMahon, F. Hong and J. W. Mellors (2014). "HIV-1 DNA decay dynamics in blood during more than a decade of suppressive antiretroviral therapy." Clin Infect Dis 59(9): 1312-1321.

Gandhi, R. T., J. C. Cyktor, R. J. Bosch, H. Mar, G. M. Laird, A. Martin, A. C. Collier, S. A. Riddler, B. J. Macatangay, C. R. Rinaldo, J. J. Eron, J. D. Siliciano, D. K. McMahon and J. W. Mellors (2021). "Selective Decay of Intact HIV-1 Proviral DNA on Antiretroviral Therapy." J Infect Dis 223(2): 225-233.

Gandhi, R. T., D. K. McMahon, R. J. Bosch, C. M. Lalama, J. C. Cyktor, B. J. Macatangay, C. R. Rinaldo, S. A. Riddler, E. Hogg, C. Godfrey, A. C. Collier, J. J. Eron and J. W. Mellors (2017). "Levels of HIV-1 persistence on antiretroviral therapy are not associated with markers of inflammation or activation." PLoS Pathog 13(4): e1006285.

Nühn, M. M., K. Bosman, T. Huisman, W. H. A. Staring, L. Gharu, D. De Jong, T. M. De Kort, N. Buchholtz, K. Tesselaar, A. Pandit, J. Arends, S. A. Otto, E. Lucio De Esesarte, A. I. M. Hoepelman, R. J. De Boer, J. Symons, J. A. M. Borghans, A. M. J. Wensing and M. Nijhuis (2025). "Selective decline of intact HIV reservoirs during the first decade of ART followed by stabilization in memory T cell subsets." Aids 39(7): 798-811.

Peluso, M. J., P. Bacchetti, K. D. Ritter, S. Beg, J. Lai, J. N. Martin, P. W. Hunt, T. J. Henrich, J. D. Siliciano, R. F. Siliciano, G. M. Laird and S. G. Deeks (2020). "Differential decay of intact and defective proviral DNA in HIV-1-infected individuals on suppressive antiretroviral therapy." JCI Insight 5(4).

Author response:

Reviewer #1 (Public Review):

Summary

We thank the reviewer for the constructive and thoughtful evaluation of our work. We appreciate the recognition of the novelty and potential implications of our findings regarding UPR activation and proteasome activity in germ cells.

(1) The microscopy images look saturated, for example, Figure 1a, b, etc. Is this a normal way to present fluorescent microscopy?

The apparent saturation was not present in the original images, but likely arose from image compression during PDF generation. While the EMA granule was still apparent, in the revised submission, we will provide high-resolution TIFF files to ensure accurate representation of fluorescence intensity and will carefully optimize image display settings to avoid any saturation artifacts.

(2) The authors should ensure that all claims regarding enrichment/lower vs. lower values have indicated statistical tests.

We fully agree. In the revised version, we will correct any quantitative comparisons where statistical tests were not already indicated, with a clear statement of the statistical tests used, including p-values in figure legends and text.

(a) In Figure 2f, the authors should indicate which comparison is made for this test. Is it comparing 2 vs. 6 cyst numbers?

We acknowledge that the description was not sufficiently detailed. Indeed, the test was not between 2 vs 6 cyst numbers, but between all possible ways 8-cell cysts or the larger cysts studied could fragment randomly into two pieces, and produce by chance 6-cell cysts in 13 of 15 observed examples. We will expand the legend and main text to clarify that a binomial test was used to determine that the proportion of cysts producing 6-cell fragments differed very significantly from chance.

Revised text:

“A binomial test was used to assess whether the observed frequency of 6-cell cyst products differed from random cyst breakage. Production of 6-cell cysts was strongly preferred (13/15 cysts; ****p < 0.0001).”

(b) Figures 4d and 4e do not have a statistical test indicated.

We will include the specific statistical test used and report the corresponding p-values directly in the figure legends.

(3) Because the system is developmentally dynamic, the major conclusions of the work are somewhat unclear. Could the authors be more explicit about these and enumerate them more clearly in the abstract?

We will revise the abstract to better clarify the findings of this study. We will also replace the term Visham with mouse fusome to reflect its functional and structural analogy to the Drosophila and Xenopus fusomes, making the narrative more coherent and conclusive.

(4) The references for specific prior literature are mostly missing (lines 184-195, for example).

We appreciate this observation of a problem that occurred inadvertently when shortening an earlier version.  We will add 3–4 relevant references to appropriately support this section.

(5) The authors should define all acronyms when they are first used in the text (UPR, EGAD, etc).

We will ensure that all acronyms are spelled out at first mention (e.g., Unfolded Protein Response (UPR), Endosome and Golgi-Associated Degradation (EGAD)).

(6)  The jumping between topics (EMA, into microtubule fragmentation, polarization proteins, UPR/ERAD/EGAD, GCNA, ER, balbiani body, etc) makes the narrative of the paper very difficult to follow.

We are not jumping between topics, but following a narrative relevant to the central question of whether female mouse germ cells develop using a fusome.  EMA, microtubule fragmentation, polarization proteins, ER, and balbiani body are all topics with a known connection to fusomes. This is explained in the general introduction and in relevant subsections. We appreciate this feedback that further explanations of these connections would be helpful. In the revised manuscript, use of the unified term mouse fusome will also help connect the narrative across sections.  UPR/ERAD/EGAD are processes that have been studied in repair and maintenance of somatic cells and in yeast meiosis.  We show that the major regulator XbpI is found in the fusome, and that the fusome and these rejuvenation pathway genes are expressed and maintained throughout oogenesis, rather than only during limited late stages as suggested in previous literature.

(7) The heading title "Visham participates in organelle rejuvenation during meiosis" in line 241 is speculative and/or not supported. Drawing upon the extensive, highly rigorous Drosophila literature, it is safe to extrapolate, but the claim about regeneration is not adequately supported.

We believe this statement is accurate given the broad scope of the term "participates." It is supported by localization of the UPR regulator XbpI to the fusome. XbpI is the ortholog of HacI a key gene mediating UPR-mediated rejuvenation during yeast meiosis.  We also showed that rejuvenation pathway genes are expressed throughout most of meiosis (not previously known) and expanded cytological evidence of stage-specific organelle rejuvenation later in meiosis, such as mitochondrial-ER docking, in regions enriched in fusome antigens. However, we recognize the current limitations of this evidence in the mouse, and want to appropriately convey this, without going to what we believe would be an unjustified extreme of saying there is no evidence. 

Reviewer #2 (Public Review):

We thank the reviewer for the comprehensive summary and for highlighting both the technical achievement and biological relevance of our study. We greatly appreciate the thoughtful suggestions that have helped us refine our presentation and terminology.

(1) Some titles contain strong terms that do not fully match the conclusions of the corresponding sections.

(1a) Article title “Mouse germline cysts contain a fusome-like structure that mediates oocyte development”

We will change the statement to: “Mouse germline cysts contain a fusome that supports germline cyst polarity and rejuvenation.”

(1b) Result title “Visham overlaps centrosomes and moves on microtubules” We acknowledge that “moves” implies dynamics. We will include additional supplementary images showing small vesicular components of the mouse fusome on spindle-derived microtubule tracks.

(1c) Result title “Visham associates with Golgi genes involved in UPR beginning at the onset of cyst formation”

We will revise this title to: “The mouse fusome associates with the UPR regulatory protein Xbp1 beginning at the onset of cyst formation” to reflect the specific UPR protein that was immunolocalized. 

(1d) Result title “Visham participates in organelle rejuvenation during meiosis”

We will revise this to: “The mouse fusome persists during organelle rejuvenation in meiosis.”

(2) The authors aim to demonstrate that Visham is a fusome-like structure. I would suggest simply referring to it as a "fusome-like structure" rather than introducing a new term, which may confuse readers and does not necessarily help the authors' goal of showing the conservation of this structure in Drosophila and Xenopus germ cells. Interestingly, in a preprint from the same laboratory describing a similar structure in Xenopus germ cells, the authors refer to it as a "fusome-like structure (FLS)" (Davidian and Spradling, BioRxiv, 2025).

We appreciate the reviewer’s insightful comment. To maintain conceptual clarity and align with existing literature, we will refer to the structure as the mouse fusome throughout the manuscript, avoiding introduction of a new term.

Reviewer #3 (Public Review):

We thank the reviewer for emphasizing the importance of our study and for providing constructive feedback that will help us clarify and strengthen our conclusions.

(1) Line 86 - the heading for this section is "PGCs contain a Golgi-rich structure known as the EMA granule" 

We agree that the enrichment of Golgi within the EMA PGCs was not shown until the next section. We will revise this heading to:

“PGCs contain an asymmetric EMA granule.”

(2)  Line 105-106, how do we know if what's seen by EM corresponds to the EMA1 granule?

We will clarify that this identification is based on co-localization with Golgi markers (GM130 and GS28) and response to Brefeldin A treatment, which will be included as supplementary data. These findings support that the mouse fusome is Golgi-derived and can therefore be visualized by EM. The Golgi regions in E13.5 cyst cells move close together and associate with ring canals as visualized by EM (Figure 1E), the same as the mouse fusomes identified by EMA.

(3) Line 106-107-states "Visham co-stained with the Golgi protein Gm130 and the recycling endosomal protein Rab11a1". This is not convincing as there is only one example of each image, and both appear to be distorted.

Space is at a premium in these figures, but we have no limitation on data documenting this absolutely clear co-localization. We will replace the existing images with high-resolution, non-compressed versions for the final figures to clearly illustrate the co-staining patterns for GM130 and Rab11a1.

(4) Line 132-133---while visham formation is disrupted when microtubules are disrupted, I am not convinced that visham moves on microtubules as stated in the heading of this section.

We will include additional supplementary data showing small mouse fusome vesicles aligned along microtubules.

(5) Line 156 - the heading for this section states that Visham associates with polarity and microtubule genes, including pard3, but only evidence for pard3 is presented.

We agree and will revise the heading to: “Mouse fusome associates with the polarity protein Pard3.” We are adding data showing association of small fusome vesicles on microtubules.  

(6)  Lines 196-210 - it's strange to say that UPR genes depend on DAZ, as they are upregulated in the mutants. I think there are important observations here, but it's unclear what is being concluded.

UPR genes are not upregulated in DAZ in the sense we have never documented them increasing. We show that UPR genes during this time behave like pleuripotency genes and normally decline, but in DAZ mutants their decline is slowed.  We will rephrase the paragraph to clarify that Dazl mutation partially decouples developmental processes that are normally linked, which alters UPR gene expression relative to cyst development.

(7) Line 257-259-wave 1 and 2 follicles need to be explained in the introduction, and how these fits with the observations here clarified.

Follicle waves are too small a focus of the current study to explain in the introduction, but we will request readers to refer to the cited relevant literature (Yin and Spradling, 2025) for further details.

We sincerely thank all reviewers for their insightful and constructive feedback. We believe that the planned revisions—particularly the refined terminology, improved image quality, clarified statistics, and restructured abstract—will substantially strengthen the manuscript and enhance clarity for readers.

Author response:

Reviewer #1 (Public review):

Summary:

In this paper, the authors conduct both experiments and modeling of human cytomegalovirus (HCMV) infection in vitro to study how the infectivity of the virus (measured by cell infection) scales with the viral concentration in the inoculum. A naïve thought would be that this is linear in the sense that doubling the virus concentration (and thus the total virus) in the inoculum would lead to doubling the fraction of infected cells. However, the authors show convincingly that this is not the case for HCMV, using multiple strains, two different target cells, and repeated experiments. In fact, they find that for some regimens (inoculum concentration), infected cells increase faster than the concentration of the inoculum, which they term "apparent cooperativity". The authors then provided possible explanations for this phenomenon and constructed mathematical models and simulations to implement these explanations. They show that these ideas do help explain the cooperativity, but they can't be conclusive as to what the correct explanation is. In any case, this advances our knowledge of the system, and it is very important when quantitative experiments involving MOI are performed.

Strengths:

Careful experiments using state-of-the-art methodologies and advancing multiple competing models to explain the data.

Weaknesses:

There are minor weaknesses in explaining the implementation of the model. However, some specific assumptions, which to this reviewer were unclear, could have a substantial impact on the results. For example, whether cell infection is independent or not. This is expanded below.

Suggestions to clarify the study:

(1) Mathematically, it is clear what "increase linearly" or "increase faster than linearly" (e.g., line 94) means. However, it may be confusing for some readers to then look at plots such as in Figure 2, which appear linear (but on the log-log scale) and about which the authors also say (line 326) "data best matching the linear relationship on a log-log scale". 

This is a good point. In our revision, we will include a clarification to indicate that linear on the log-log scale relationship does not imply linear relationship on the linear-linear scale.

(2) One of the main issues that is unclear to me is whether the authors assume that cell infection is independent of other cells. This could be a very important issue affecting their results, both when analyzing the experimental data and running the simulations. One possible outcome of infection could be the generation of innate mediators that could protect (alter the resistance) of nearby cells. I can imagine two opposite results of this: i) one possibility is that resistance would lead to lower infection frequencies and this would result in apparent sub-linear infection (contrary to the observations); or ii) inoculums with more virus lead to faster infection, which doesn't allow enough time for the "resistance" (innate effect) to spread (potentially leading to results similar to the observations, supra-linear infection). 

In our models we assumed cells to be independent of each other (see also responses to other similar points). Because we measure infection in individual cells, assuming cells are independent is a reasonable first approximation. However, the reviewer makes an excellent point that there may be some between-cell signaling happening in the culture that “alerts” or “conditions” cells to change their “resistance”. It is also possible that at higher genome/cell numbers, exposure of cells to virions or virion debris may change the state of cells in the culture, and more cells become “susceptible” to infection. This is a good point that we will list in Limitations subsection of Discussion; it is a good hypothesis to test in our future experiments.

(3) Another unclear aspect of cell infection is whether each cell only has one chance to be infected or multiple chances, i.e., do the authors run the simulation once over all the cells or more times? 

Each cell has only one chance to be infected. Algorithm 1 clearly states that; we will add an extra sentence in “Agent-based simulations” to indicate this point.

(4) On the other hand, the authors address the complementary issue of the virus acting independently or not, with their clumping model (which includes nice experimental measurements). However, it was unclear to me what the assumption of the simulation is in this case. In the case of infection by a clump of virus or "viral compensation", when infection is successful (the cell becomes infected), how many viruses "disappear" and what happens to the rest? For example, one of the viruses of the clump is removed by infection, but the others are free to participate in another clump, or they also disappear. The only thing I found about this is the caption of Figure S10, and it seems to indicate that only the infected virus is removed. However, a typical assumption, I think, is that viruses aggregate to improve infection, but then the whole aggregate participates in infection of a single cell, and those viruses in the clump can't participate in other infections. Viral cooperativity with higher inocula in this case would be, perhaps, the result of larger numbers of clumps for higher inocula. This seems in agreement with Figure S8, but was a little unclear in the interpretation provided. 

This is a good point. We did not remove the clump if one of the virions in the clump manages to infect a cell, and indeed, this could be the reason why in some simulations we observe apparent cooperativity when modeling viral clumping. This is something we will explore in our revision.

(5) In algorithm 1, how does P_i, as defined, relate to equation 1? 

These are unrelated because eqn.(1) is a phenomenological model that links infection per cell to genomes per cell. P_i in algorithm 1 is “physics-inspired” potential barrier.

(6) In line 228, and several other places (e.g., caption of Table S2), the authors refer to the probability of a single genome infecting a cell p(1)=exp(-lambda), but shouldn't it be p(1)=1-exp(-lambda) according to equation 1?

Indeed, it was a typo, p(1)=1-exp(-lambda) per eqn 1. Thank you, it will be corrected in the revised paper.

(7) In line 304, the accrued damage hypothesis is defined, but it is stated as a triggering of an antiviral response; one would assume that exposure to a virion should increase the resistance to infection. Otherwise, the authors are saying that evolution has come up with intracellular viral resistance mechanisms that are detrimental to the cell. As I mentioned above, this could also be a mechanism for non-independent cell infection. For example, infected cells signal to neighboring cells to "become resistance" to infection. This would also provide a mechanism for saturation at high levels. 

We do not know how exposure of a cell to one virion would change its “antiviral state”, i.e., to become more or less resistant to the next infection. If a cell becomes more resistant, there is no possibility to observe apparent cooperativity in infection of cells, so this hypothesis cannot explain our observations with n>1. Whether this mechanism plays a role in saturation of cell infection rate at lower than 1 value when genome/cell is large is unclear but is a possibility. We will add this point to Discussion in revision.

(8) In Figure 3, and likely other places, t-tests are used for comparisons, but with only an n=5 (experiments). Many would prefer a non-parametric test. 

We repeated the analyses in Fig 3 with Mann-Whitney test, results were the same, so we would like to keep results from the t-test in the paper.

Reviewer #2 (Public review):

In their article, Peterson et al. wanted to show to what extent the classical "single hit" model of virion infection, where one virion is required to infect a cell, does not match empirical observations based on human cytomegalovirus in vitro infection model, and how this would have practical impacts in experimental protocols.

They first used a very simple experimental assay, where they infected cells with serially diluted virions and measured the proportion of infected cells with flow cytometry. From this, they could elegantly show how the proportion of infected cells differed from a "single hit" model, which they simulated using a simple mathematical model ("powerlaw model"), and better fit a model where virions need to cooperate to infect cells. They then explore which mechanism could explain this apparent cooperation:

(1) Stochasticity alone cannot explain the results, although I am unsure how generalizable the results are, because the mathematical model chosen cannot, by design, explain such observations only by stochasticity. 

Our null model simulations are not just about stochasticity; they also include variability in virion infectivity and cell resistance to infection. We agree that simulations cannot truly prove that such variability cannot result in apparent cooperativity; however, we also provide a mathematical proof that increase in frequency of infected cells should be linear with virion concentration at small genome/cell numbers.

(2) Virion clumping seemed not to be enough either to generally explain such a pattern. For that, they first use a mathematical model showing that the apparent cooperation would be small. However, I am unsure how extreme the scenario of simulated virion clumping is. They then used dynamic light scattering to measure the distribution of the sizes of clumps. From these estimates, they show that virion clumps cannot reproduce the observed virion cooperation in serial dilution assays. However, the authors remain unprecise on how the uncertainty of these clumps' size distribution would impact the results, as most clumps have a size smaller than a single virion, leaving therefore a limited number of clumps truly containing virions. 

As we stated in the paper, clumping may explain apparent cooperativity in simulations depending on how stock dilution impacts distribution of virions/clump. This could be explored further, however, better experimental measurements of virions/clump would be highly informative (but we do not have resources to do these experiments at present). Our point is that the degree of apparent cooperativity is dependent on the target cell used (n is smaller on epithelial cells than on fibroblasts) that is difficult to explain by clumping which is a virion property. Per comment by reviewer 1, we will do some more analyses of the clumping model to investigate importance of clump removal per successful infection on the detected degree of apparent cooperativity.

The two models remain unidentifiable from each other but could explain the apparent virion cooperativity: either due to an increase in susceptibility of the cell each time a virion tries to infect it, or due to viral compensation, where lesser fit viruses are able to infect cells in co-infection with a better fit virion. Unfortunately, the authors here do not attempt to fit their mathematical model to the experimental data but only show that theoretical models and experimental data generate similar patterns regarding virion apparent cooperation. 

In the revision we will provide examples of simulations that “match” experimental data with a relatively high degree of apparent cooperativity; we have done those before but excluded them from the current version since they are a bit messy. Fitting simulations to data may be an overkill.

Finally, the authors show that this virions cooperation could make the relationship between the estimated multiplicity of infection and viruses/cell deviate from the 1:1 relationship. Consequently, the dilution of a virion stock would lead to an even stronger decrease in infectivity, as more diluted virions can cooperate less for infection.

Overall, this work is very valuable as it raises the general question of how the estimate of infectivity can be biased if extrapolated from a single virus titer assay. The observation that HCMV virions often cooperate and that this cooperation varies between contexts seems robust. The putative biological explanations would require further exploration.

This topic is very well known in the case of segmented viruses and the semi-infectious particles, leading to the idea of studying "sociovirology", but to my knowledge, this is the first time that it was explored for a nonsegmented virus, and in the context of MOI estimation. 

Thank you.

Reviewer #3 (Public review): 

Summary:

The authors dilute fluorescent HCMV stocks in small steps (df ≈ 1.3-1.5) across 23 points, quantify infections by flow cytometry at 3 dpi, and fit a power-law model to estimate a cooperativity parameter n (n > 1 indicates apparent cooperativity). They compare fibroblasts vs epithelial cells and multiple strains/reporters, and explore alternative mechanisms (clumping, accrued damage, viral compensation) via analytical modeling and stochastic simulations. They discuss implications for titer/MOI estimation and suggest a method for detecting "apparent cooperativity," noting that for viruses showing this behavior, MOI estimation may be biased.

Strengths:

(1) High-resolution titration & rigor: The small-step dilution design (23 serial dilutions; tailored df) improves dose-response resolution beyond conventional 10× series.

(2) Clear quantitative signal: Multiple strain-cell pairs show n > 1, with appropriate model fitting and visualization of the linear regime on log-log axes.

(3) Mechanistic exploration: Side-by-side modeling of clumping vs accrued damage vs compensation frames testable hypotheses for cooperativity. 

Thank you.

Weaknesses:

(1) Secondary infection control: The authors argue that 3 dpi largely avoids progeny-mediated secondary infection; this claim should be strengthened (e.g., entry inhibitors/control infections) or add sensitivity checks showing results are robust to a small secondary-infection contribution. 

This is an important point. We do believe that the current knowledge about HCMV virion production time – it takes 3-4 days to make virions per multiple papers (see Fig 7 in Vonka and Benyesh-Melnick JB 1966; Fig 3B in Stanton et al JCI 2010; and Fig 1A in Li et al. PNAS 2015) – is sufficient to justify our experimental design but we do agree that an additional control to block novel infections with would be useful. We had previously performed experiments with a HCMV TB-gL-KO that cannot make infectious virions (but the stock virions can be made from complemented target cells). We will investigate if our titration experiments with this virus strain have sufficient resolution to detect apparent cooperativity. However, at present we do not have the resources to perform novel experiments.  

(2) Discriminating mechanisms: At present, simulations cannot distinguish between accrued damage and viral compensation. The authors should propose or add a decisive experiment (e.g., dual-color coinfection to quantify true coinfection rates versus "priming" without coinfection; timed sequential inocula) and outline expected signatures for each mechanism. 

Excellent suggestion. Because infection of a cell is a result of the joint viral infectivity and cell resistance, it may be hard to discriminate between these alternatives unless we specify them as particular molecular mechanisms. But we will try our best and list potential future experiments in the revised version of the paper.

(3) Decline at high genomes/cell: Several datasets show a downturn at high input. Hypotheses should be provided (cytotoxicity, receptor depletion, and measurement ceiling) and any supportive controls. 

Another good point. We do not have a good explanation, but we do not believe this is because of saturation of available target cells.  It seemed to only happen (or was most pronounced) with the ME stocks, which are typically lower in titer and so the higher MOI were nearly undiluted stock. It may be the effect of the conditioned medium.  Or perhaps there are non-infectious particles like dense bodies (enveloped particles that lack a capsid and genome) and non-infectious, enveloped particles (NIEPs) that compete for receptors or otherwise damage cells and these don’t get diluted out at the higher doses.  We plan to include these points in Discussion of the revised version of the paper.

(4) Include experimental data: In Figure 6, please include the experimentally measured titers (IU/mL), if available. 

This is a model-simulated scenario, and as such, there is no measured titers.

(5) MOI guidance: The practical guidance is important; please add a short "best-practice box" (how to determine titer at multiple genomes/cell and cell densities; when single-hit assumptions fail) for end-users. 

Good suggestion. We will include best-practice box using guidelines developed in Ryckman lab over the years in the revised version of the paper.

Overall note to all reviews: We have deposited our codes and the data on github; yet, none of the reviewers commented on it.

Author response:

We thank the editor and reviewers for their thoughtful feedback. We agree with eLife’s overall assessment that, while profiling terminating ribosomes is informative in revealing termination dynamics, the underlying mechanisms require more evidence. Our revision will focus on three conceptual points.

(1) We will tone down the statement that putative mRNA:rRNA interaction contributes to sequence-specific termination pausing.

(2) We will clarify the potential role of Rps26 in regulating translation termination.

(3) We will expand the discussion of tissue-specific termination pausing.

Reviewer #1 (Public Review):

(1) We admit that the modest effects of ABCE1 were partly due to the incomplete ABCE1 knockdown in HEK293 cells. Since the elevated ribosome density occurred at all stop codons, we argue that the action of ABCE1 is likely independent of the sequence context. We will rephrase relevant statements in the revised manuscript.

(2) In terms of Rps26 structures, we agree the structural rearrangement in the absence of Rps26 is highly speculative. However, we do not believe the Rps26 stoichiometry is solely dependent on stress. We will clarify this important point in the revised manuscript.

(3) We apologize for the confusion about 18S rRNA “scanning” and will revise the sentence in the main text.

(4) We agree that functional significance of testis-specific termination dynamics is unclear. Since other reviewers raised similar concern, we will expand the discussion of tissue-specific termination pausing in the revised manuscript.

Reviewer #2 (Public Review):

We appreciate the Reviewer’s time and efforts in reviewing our manuscript. We are grateful for the insightful comments and many recommendations made by the reviewer to improve our manuscript. We feel that the reviewer may have some misunderstanding in terms of the sequence motif associated with the termination pausing, partly because of the lack of clarity in our original description of the results from MPRA and reporter assays. We will ensure that the reviewer’s points are fully addressed in the revised manuscript.

Reviewer #3 (Public Review):

We thank the reviewer’s positive comment on our manuscript. We agree that the tissue-specific termination differences were poorly described in the main text. Notably, other reviewers raised similar concerns. We will expand the relevant discussion in the revised manuscript, outlining this as a limitation and a future direction.

Reviewer #4 (Public Review):

We believe the reviewer mixed xthe public view with recommendation comments. The reviewer appears to be preoccupied by previous studies and questioned some inconsistency in our results. With the development of new technology such as eRF1-seq, we are encouraged to present “new” and “different” findings. All other reviewers appreciate the development of eRF1-seq to profile terminating ribosomes. In fact, we do not believe our data is fundamentally different from the established principles. Rather, our data provides new perspectives to further our understanding of ribosome dynamics at stop codons. We thank the reviewer for understanding.

The reviewer is quite confused by our sequencing analysis based on peak height, or read density, which is commonly used to infer ribosome dynamics such as pausing. Regarding the sequencing analysis and reporter assays in cells expressing 18S mutant (Figure 5) and Rps26 (Figure 7), we feel that the reviewer has some misunderstanding. In the revised manuscript, we will do our best to clarify those relevant issues. Finally, the reviewer’s comment on base pairing is well-received and we will thoroughly revise the main text and discussion in the revised manuscript.

Author response:

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

Reviewer #1 (Public Review):

Summary:

In this manuscript, Bisht et al address the hypothesis that protein folding chaperones may be implicated in aggregopathies and in particular Tau aggregation, as a means to identify novel therapeutic routes for these largely neurodegenerative conditions.

The authors conducted a genetic screen in the Drosophila eye, which facilitates the identification of mutations that either enhance or suppress a visible disturbance in the nearly crystalline organization of the compound eye. They screened by RNA interference all 64 known Drosophila chaperones and revealed that mutations in 20 of them exaggerate the Tau-dependent phenotype, while 15 ameliorated it. The enhancer of the degeneration group included 2 subunits of the typically heterohexameric prefoldin complex and other co-translational chaperones.

The authors characterized in depth one of the prefoldin subunits, Pfdn5, and convincingly demonstrated that this protein functions in the regulation of microtubule organization, likely due to its regulation of proper folding of tubulin monomers. They demonstrate convincingly using both immunohistochemistry in larval motor neurons and microtubule binding assays that Pfdn5 is a bona fide microtubule-associated protein contributing to the stability of the axonal microtubule cytoskeleton, which is significantly disrupted in the mutants.

Similar phenotypes were observed in larvae expressing Frontotemporal dementia with Parkinsonism on chromosome 17-associated mutations of the human Tau gene V377M and R406W. On the strength of the phenotypic evidence and the enhancement of the TauV377Minduced eye degeneration, they demonstrate that loss of Pfdn5 exaggerates the synaptic deficits upon expression of the Tau mutants. Conversely, the overexpression of Pfdn5 or Pfdn6 ameliorates the synaptic phenotypes in the larvae, the vacuolization phenotypes in the adult, and even memory defects upon TauV377M expression.

Strengths

The phenotypic analyses of the mutant and its interactions with TauV377M at the cell biological, histological, and behavioral levels are precise, extensive, and convincing and achieve the aims of characterization of a novel function of Pfdn5. 

Regarding this memory defect upon V377M tau expression. Kosmidis et al (2010), PMID: 20071510, demonstrated that pan-neuronal expression of Tau^V377M disrupts the organization of the mushroom bodies, the seat of long-term memory in odor/shock and odor/reward conditioning. If the novel memory assay the authors use depends on the adult brain structures, then the memory deficit can be explained in this manner. 

(1) If the mushroom bodies are defective upon Tau^V377M. expression, does overexpression of Pfdn5 or 6 reverse this deficit? This would argue strongly in favor of the microtubule stabilization explanation.

We thank the reviewer for this insightful comment. Consistent with Kosmidis et al. (2010), we confirm that expression of hTau^V377M disrupts the architecture of mushroom bodies.   In addition, we find, as suggested by the reviewer, that coexpression of either Pfdn5 or Pfdn6 with hTau^V377M significantly restores the organization of the mushroom bodies. These new findings strongly support the hypothesis that Pfdn5 or Pfdn6 mitigate hTau^V377M -induced memory deficits by preserving the structure of the mushroom body, likely through stabilizing the microtubule network. This data has now been included in the revised manuscript (Figure 7H-O).

(2) The discovery that Pfdn5 (and 6 most likely) affects tauV377M toxicity is indeed a novel and important discovery for the Tauopathies field. It is important to determine whether this interaction affects only the FTDP-17-linked mutations or also WT Tau isoforms, which are linked to the rest of the Tauopathies. Also, insights on the mode(s) that Pfdn5/6 affect Tau toxicity, such as some of the suggestions above, are aiming at will likely be helpful towards therapeutic interventions.

We agree that determining whether prefoldin modulates the toxicity of both mutant and wildtype Tau is critical for understanding its broader relevance to Tauopathies. We have now performed additional experiments required to address this issue. These new data show that loss of Pfdn5 also exacerbates toxicity associated with wildype Tau (hTau^WT), in a manner similar to that observed with hTau^V337M or hTau^R406W. Specifically, overexpression of hTau^WT in a Pfdn5 mutant background leads to Tau aggregate formation (Figure S7G-I), and coexpression of Pfdn5 with hTau^WT reduces the associated synaptic defects (Figure S11F-L). These findings underscore a general role for Pfdn5 in modulating diverse Tauopathy-associated phenotypes and suggest that it could be a broadly relevant therapeutic target. 

Weakness

(3) What is unclear, however, is how Pfdn5 loss or even overexpression affects the pathological Tau phenotypes. Does Pfdn5 (or 6) interact directly with TauV377M? Colocalization within tissues is a start, but immunoprecipitations would provide additional independent evidence that this is so.

We appreciate this important suggestion. To investigate a potential direct interaction between Pfdn5 and Tau^V377M, we performed co-immunoprecipitation experiments using lysates from adult fly brain expressing hTau^V337M. Under the conditions tested, we did not detect a direct physical interaction. While this does not support a direct interaction, it does not strongly refute it either. We note that Pfdn5 and Tau are colocalized within axons (Figure S13J-K). At this stage, we are unable to resolve the issue of direct vs indirect association. If indirect, then Tau and Pfdn5 act within the same subcellular compartments (axon); if direct, then either only a small fraction of the total cellular proteins is in the Tau-Pfdn5 complex and therefore difficult to detect in bulk protein westerns, or the interactions are dynamic or occur in conditions that we have not been able to mimic in vitro. 

(4) Does Pfdn5 loss exacerbate Tau^V377M phenotypes because it destabilizes microtubules, which are already at least partially destabilized by Tau expression? Rescue of the phenotypes by overexpression of Pfdn5 agrees with this notion. 

However, Cowan et al (2010) pmid: 20617325 demonstrated that wildtype Tau accumulation in larval motor neurons indeed destabilizes microtubules in a Tau phosphorylation-dependent manner. So, is Tau^V377M hyperphosphorylated in the larvae?? What happens to Tau^V377M phosphorylation when Pfdn5 is missing and presumably more Tau is soluble and subject to hyperphosphorylation as predicted by the above?

We completely agree that it is important to link Tau-induced phenotypes with the microtubule destabilization and phosphorylation state of Tau.   We performed immunostaining using futsch antibody to check the microtubule organization at the NMJ and observed a severe reduction in futsch intensity when Tau^V337M was expressed in the Pfdn5 mutant (ElavGal4>Tau^V337M; DPfdn5^15/40), suggesting that Pfdn5 absence exacerbates the hTau^V337M defects due to more microtubule destabilization (Figure S6F-J). 

We have performed additional experiments to examine the phosphorylation state of hTau in Drosophila larval axons. Immunocytochemistry indicated that only a subset of hTau aggregates in Pfdn5 mutants (Elav-Gal4>Tau^V337M; DPfdn5^15/40) are recognized by phospho-hTau antibodies.   For instance, the AT8 antibody (targeting pSer202/pThr205) (Goedert et al., 1995) labelled only a subset of aggregates identified by the total hTau antibody (D5D8N) (Figure S9AE). Moreover, feeding these larvae (Elav-Gal4>Tau<sup>V337M</sup; DPfdn5^15/40) with LiCl, which blocks GSK3b, still showed robust Tau aggregation (Figure S9F-J). 

These results imply that: a) soluble phospho-hTau levels in Pfdn5 mutants are low and not reliably detected with a single phospholylation-specific antibody; b) Loss of Pfdn5 results in Tau aggregation in a hyperphosphorylation-independent manner similar to what has been reported earlier (LI et al. 2022); and c) the destabilization of microtubules in Elav-Gal4>Tau^V337M; DPfdn5^15/40 results in Tau dissociation and aggregate formation. These data and conclusions have been incorporated into the revised manuscript.

(5) Expression of WT human Tau (which is associated with most common Tauopathies other than FTDP-17) as Cowan et al suggest has significant effects on microtubule stability, but such Tauexpressing larvae are largely viable. Will one mutant copy of the Pfdn5 knockout enhance the phenotype of these larvae?? Will it result in lethality? Such data will serve to generalize the effects of Pfdn5 beyond the two FDTP-17 mutations utilized.

We have now examined whether heterozygous loss of Pfdn5 (∆Pfdn5/+) enhances the effect of Tau expression. While each genotype (hTau^V337M, hTau^WT or ∆Pfdn5/+) alone is viable, Elav-Gal4 driven expression of hTau^V337M or hTau^WT in Pfdn5 heterozygous background does not cause lethality. 

(6) Does the loss of Pfdn5 affect TauV377M (and WTTau) levels?? Could the loss of Pfdn5 simply result in increased Tau levels? And conversely, does overexpression of Pfdn5 or 6 reduce Tau levels?? This would explain the enhancement and suppression of Tau^V377M (and possibly WT Tau) phenotypes. It is an easily addressed, trivial explanation at the observational level, which, if true, begs for a distinct mechanistic approach.

To test whether Pfdn5 modulates Tau phenotypes by altering Tau protein levels, we performed western blot analysis under Pfdn5 or Pfdn6 overexpression conditions and observed no change in hTau^V337M levels (Figure 6O). However, in the absence of Pfdn5, both hTau^V337M and hTau^WT form large, insoluble aggregates that are not detected in soluble lysates by standard western blotting but are visualized by immunocytochemistry (Figure S7G-I). Thus, the apparent reduction in Tau levels on western blots reflects a solubility shift, not an actual decrease in Tau expression. These findings argue against a simple model in which Pfdn5 regulates Tau abundance and instead support a mechanism in which Pfdn5 loss leads to change in Tau conformation, leading to its sequesteration away for already destabilized microtubules.  

(7) Finally, the authors argue that Tau^V377M forms aggregates in the larval brain based on large puncta observed especially upon loss of Pfdn5. This may be so, but protocols are available to validate this molecularly the presence of insoluble Tau aggregates (for example, pmid: 36868851) or soluble Tau oligomers, as these apparently differentially affect Tau toxicity. Does Pfdn5 loss exaggerate the toxic oligomers, and overexpression promote the more benign large aggregates??

We have performed additional experiments to analyze the nature of these aggregates using 1,6-HD. The 1,6-hexanediol can dissolve the Tau aggregate seeds formed by Tau droplets, but cannot dissolve the stable Tau aggregates (WEGMANN et al. 2018). We observed that 5% 1,6hexanediol failed to dissolve these Tau aggregates (Figure S8), demonstrating the formation of stable filamentous flame-shaped NFT-like aggregates in the absence of Pfdn5 (Figure 5D and Figure S9).

Reviewer #2 (Public review):

Bisht et al detail a novel interaction between the chaperone, Prefoldin 5, microtubules, and taumediated neurodegeneration, with potential relevance for Alzheimer's disease and other tauopathies. Using Drosophila, the study shows that Pfdn5 is a microtubule-associated protein, which regulates tubulin monomer levels and can stabilize microtubule filaments in the axons of peripheral nerves. The work further suggests that Pfdn5/6 may antagonize Tau aggregation and neurotoxicity. While the overall findings may be of interest to those investigating the axonal and synaptic cytoskeleton, the detailed mechanisms for the observed phenotypes remain unresolved and the translational relevance for tauopathy pathogenesis is yet to be established. Further, a number of key controls and important experiments are missing that are needed to fully interpret the findings.

The strength of this study is the data showing that Pfdn5 localizes to axonal microtubules and the loss-of-function phenotypic analysis revealing disrupted synaptic bouton morphology. The major weakness relates to the experiments and claims of interactions with Tau-mediated neurodegeneration. 

In particular, it is unclear whether knockdown of Pfdn5 may cause eye phenotypes independent of Tau. 

Our new experiments confirm that knockdown of Pfdn5 alone does not cause eye phenotypes.

Further, the GMR>tau phenotype appears to have been incorrectly utilized to examine agedependent, neurodegeneration.

In response, we have modulated and explained our conclusions in this regard as described later in our “rebuttal.”

This manuscript argues that its findings may be relevant to thinking about mechanisms and therapies applicable to tauopathies; however, this is premature given that many questions remain about the interactions from Drosophila, the detailed mechanisms remain unresolved, and absent evidence that Tau and Pfdn may similarly interact in the mammalian neuronal context. Therefore, this work would be strongly enhanced by experiments in human or murine neuronal culture or supportive evidence from analyses of human data.

The reviewer is correct that the impact would be greater if Pfdn5-Tau interactions were also examined in human tissue.   While we have not attempted these experiments ourselves, we hope that our observations will stimulate others to test the conservation of phenomena we describe. There are, however, several lines of circumstantial evidence from human Alzheimer’s disease datasets that implicate PFDN5 in disease pathology. For example, recent compilations and analyses of proteomic data show reductions of CCT components, TBCE, as well as Prefoldin subunits, including PFDN5, in AD tissue (HSIEH et al. 2019; TAO et al. 2020; JI et al. 2022; ASKENAZI et al. 2023; LEITNER et al. 2024; SUN et al. 2024). Furthermore, whole blood mRNA expression data from Alzheimer's patients revealed downregulation of PFDN5 transcript (JI et al. 2022). Together, these findings from human data are consistent with the roles of PFDN5 in suppressing diverse neurodegenerative processes. We have incorporated these points into the discussion section of the revised manuscript.

Reviewer #1 (Recommendations for the authors):

See public review for experimental recommendations focusing on the Tau Pfdn interactions.  I would refrain from using the word aggregates, I would call them puncta, unless there is molecular or visual (ie AFM) evidence that they are indeed insoluble aggregates.  Finally, although including the full genotypes written out below the axis in the bar graphs is appreciated, it nevertheless makes them difficult to read due to crowding in most cases and somewhat distracting from the figure. 

In my opinion, a more reader-friendly manner of reporting the phenotypes will be highly helpful. For example, listing each component of the genotype on the left of each bar graph and adding a cross or a filled circle under the bar to inform of the full genotype of the animals used.

As described in the response to the previous comment, we now have strong direct evidences to support our view that the observed puncta are stable Tau aggregates. Thus, we feel justified to use the term Tau-aggregates in preference to Tau puncta. 

We have tried to write the genotypes to make them more reader-friendly.

Reviewer #2 (Recommendations for the authors):

(1) Lines 119-121: 35 modifiers from 64 seem like an unusually high hit rate. Are these individual genes or lines? Were all modifiers supported by at least 2 independent RNAi strains targeting non-overlapping sequences? A supplemental table should be included detailing all genes and specific strains tested, with corresponding results.

We agree with the reviewer that 35 modifiers from 64 genes may be too high. However, since the genes knocked down in the study are chaperones, crucial for maintaining proteostasis, we may have got unusually high hits. The information related to individual genes and lines is provided in Supplemental Table 1. We have now included an additional Supplemental Table 3, which lists the genes and the RNAi lines used in Figure 1, detailing the sequence target information. The table also specifies the number of independent RNAi strains used and the corresponding results. 

(2) Figure 1: The authors quantify the areas of ommatidial fusion and necrosis as degeneration, but it is difficult to appreciate the aberrations in the photos provided. Was any consideration given to also quantifying eye size?

We have processed the images to enhance their contrast and make the aberrations clearer. The percentage of degenerated eye area (Figure 1M) was normalized with total eye area. The method for quantifying degenerated area has been explained in the materials and methods section.

(3) Figure 1: a) Only enhancers of rough eyes are shown but no controls are included to evaluate whether knockdown of these genes causes eye toxicity in the absence of Tau. These are important missing controls. All putative Tau enhancers, including Pdn5/6, need to be tested with GMR-GAL4 independently of Tau to determine whether they cause a rough eye. In a previous publication from some of the same investigators (Raut et al 2017), knockdown of Pfdn using eyGAL4 was shown to induce severe eye morphology defects - this raises questions about the results shown here. 

We agree that assessing the effects of HSP knockdown independent of Tau is essential to confirm modifier specificity. We have now performed these knockdowns, and the data are reported in Supplemental Table 1. For RNAi lines represented in Figure 1, which enhanced Tau-induced degeneration/eye developmental defect, except for one of the RNAi lines against Pfdn6 (GD34204), no detectable eye defects were observed when knocked down with GMR-Gal4 at 25°C, suggesting that enhancement is specific to the Tau background. 

Use of a more eye-specific GMR-Gal4 driver at 25°C versus broader expressing ey-Gal4 at 29°C in prior work (Raut et al. 2017) likely reflects the differences in the eye morphological defects.

(b) Besides RNAi, do the classical Pdn5 deletion alleles included in this work also enhance the tau rough eye when heterozygous? Please also consider moving the Pfdn5/6 overexpression studies to evaluate possible suppression of the Tau rough eye to Figure 1, as it would enhance the interpretation of these data (but see also below).

GMR-Gal4 driven expression of hTau^V337M or hTau^WT in Pfdn5 heterozygous background does not enhance rough eye phenotype. 

(4) For genes of special interest, such as Pdn5, and other genes mentioned in the results, the main figure, or discussion, it is also important to perform quantitative PCR to confirm that the RNAi lines used actually knock down mRNA expression and by how much. These studies will establish specificity.

We agree that confirming RNAi efficiency via quantitative PCR (qPCR) is essential for validating the knockdown efficiency. We have now included qPCR data, especially for key modifiers, confirming effective knockdown (Figure S2).

(5) Lines 235-238: how do you conclude whether the tau phenotype is "enhanced" when Pfdn5 causes a similar phenotype on its own? Could the combination simply be additive? Did overexpression of Pdn5 suppress the UAS-hTau NMJ bouton phenotype (see below)? 

Although Pfdn5 mutants and hTau expression individually increase satellite boutons, their combination leads to a significantly more severe and additional phenotype, such as significantly decreased bouton size and increased bouton number, indicating an enhancing rather than purely additive interaction (Figure 4 and Figure S6C). Moreover, we now show that overexpression of Pfdn5 significantly suppressed the hTau^V337M-induced NMJ phenotypes. This new data has been incorporated as Figure S11F-L in the revised manuscript. 

Alternatively, did the authors consider reducing fly tau in the Pdn5 mutant background?

In new additional experiments, we observe that double mutants for Drosophila Tau (dTau) and Pfdn5 also exhibit severe NMJ defects, suggesting genetic interactions between dTau and Pfdn5. This data is shown below for the reviewer.

Author response image 1.

A double mutant combination of dTau and Pfdn5 aggravates the synaptic defects at the Drosophila NMJ. (A-D') Confocal images of NMJ synapses at muscle 4 of A2 hemisegment showing synaptic morphology in (A-A') control, (B-B') ΔPfdn5<SUP>15/40</SUP>, (C-C') dTauKO/dTauKO (Drosophila Tau mutant), (D-D') dTauKO/dTauKO; ∆Pfdn5<SUP>15/40</SUP> double immunolabeled for HRP (green), and CSP (magenta). The scale bar in D for (A-D') represents 10 µm. 

(6) It may be important to further extend the investigation to the actin cytoskeleton. It is noted that Pfdn5 also stabilizes actin. Importantly, tau-mediated neurodegeneration in Drosophila also disrupts the actin cytoskeleton, and many other regulators of actin modify tau phenotypes.

We appreciate the suggestion to examine the actin cytoskeleton. While prior studies indicate that Pfdn5 might regulate the actin cytoskeleton and that Tau^V377M hyperstabilizes the actin cytoskeleton, we did not observe altered actin levels in Pfdn5 mutants (Figure 2G). However, actin dynamics may represent an additional mechanism through which Pfdn5 might temporally influence Tauopathy. Future work will address potential actin-related mechanisms in Tauopathy.

(7) Figure 2: in the provided images, it is difficult to appreciate the futsch loops. Please include an image with increased magnification. It appears that fly strains harboring a genomic rescue BAC construct are available for Pfdn-this would be a complementary reagent to test besides Pfdn overexpression.

We have updated Figure 2 to include high magnification NMJ images as insets, clearly showing the Futsch loops. While we have not yet tested a genomic rescue BAC construct for Pfdn5, we plan to use the fly line harboring this construct in future work.

(8) Figure 3: Some of the data is not adequately explained. The use of Ran as a loading control seems rather unusual. What is the justification? Pfdn appears to only partially co-localize with a-tubulin in the axon; can the authors discuss or explain this? Further, in Pfdn5 mutants, there appears to be a loss of a-tubulin staining (3b'); this should also be discussed.

We appreciate the reviewer's concern regarding the choice of loading control for our Western blot analysis. Importantly, since Tubulin levels and related pathways were the focus of our analysis, traditional loading controls such as α- or β-tubulin or actin were deemed unsuitable due to potential co-regulation. Ran, a nuclear GTPase involved in nucleocytoplasmic transport, is not known to be transcriptionally or post-translationally regulated by Tubulin-associated signaling pathways. To ensure its reliability as a loading control, we confirmed by densitometric analysis that Ran expression showed minimal variability across all samples. Hence, we used Ran for accurate normalization in the Western blot data represented in this manuscript. We have also used GAPDH as a loading control and found no difference with respect to Ran as a loading control across samples.

We appreciate the reviewer's comment regarding the interpretation of our Pearson's correlation coefficient (PCC) results. While the mean colocalization value of 0.6 represents a moderate positive correlation (MUKAKA 2012), which may not reach the conventional threshold for "high positive" colocalization (usually considered 0.7-0.9), it nonetheless indicates substantial spatial overlap between the proteins of interest. Importantly, colocalization analysis provides supportive but indirect evidence for molecular proximity.  To further validate the interaction, we performed a microtubule binding assay, which directly demonstrates the binding of Pfdn5 to stabilized microtubules.

In accordance with the western blot analysis shown in Figure 2G-I, the levels of Tubulin are reduced in the Pfdn5 mutants (Figure 3B''). We have incorporated and discussed this in the revised manuscript.

(9) Figure 4: Overexpression of Pfdn appears to rescue the supernumerary satellite bouton numbers induced by human Tau; however, interpretation of this experiment is somewhat complicated as it is performed in Pfdn mutant genetic background. Can overexpression of Pfdn on its own rescue the Tau bouton defect in an otherwise wildtype background?

We have now coexpressed Pfdn5 and hTau<SUP>V337M</SUP> in an otherwise wild-type background. As shown in Figure S11F-L, Pfdn5 overexpression suppresses Tau-induced bouton defects. We have incorporated the data in the Results section to support the role of Pfdn5 as a modifier of Tau toxicity.

(10) Lines 256-263 / Figure 5: (a) What exactly are these tau-positive structures (punctae) being stained in larval brains in Fig 5C-E? Most prior work on tau aggregation using Drosophila models has been done in the adult brain, and human wildtype or mutant Tau is not known to form significant numbers of aggregates in neurons (although aggregates have been described following glia tau expression). 

Therefore, the results need to be further clarified. Besides the provided schematic, a zoomed-out image showing the whole larval brain is needed here for orientation. Have these aggregates been previously characterized in the literature? 

We agree with the reviewer that the expression of the wildtype or mutant form of human Tau in Drosophila is not known to form aggregates in the larval brain, in contrast to the adult brain (JACKSON et al. 2002; OKENVE-RAMOS et al. 2024). Consistent with previous reports, we also observed that Tau expression on its own does not form aggregates in the Drosophila larval brain.

However, in the absence of Pfdn5, microtubule disruption is severe, leading to reduced Taumicrotubule binding and formation of globular/round or flame-shaped tangles like aggregates in the larval brain. Previous studies have reported that 1,6-hexanediol can dissolve the Tau aggregate seeds formed by Tau droplets, but cannot dissolve the stable Tau aggregates (WEGMANN et al. 2018). We observed that 5% 1,6-Hexanediol failed to dissolve these Tau puncta, demonstrating the formation of stable aggregates in the absence of Pfdn5. Additionally, we now performed a Tau solubility assay and show that in the absence of Pfdn5, a significant amount of Tau goes in the pellet fraction, which could not be detected by phospho-specific AT8 Tau antibody (targeting pSer202/pThr205) but was detected by total hTau antibody (D5D8N) on the western blots (Figure S8). These data further reinforce our conclusion that  Pfdn5 prevents the transition of hTau from soluble and/or microtubule-associated state to an aggregated, insoluble, and pathogenic state. These new data have been incorporated into the revised manuscript.

(b) Can additional markers (nuclei, cell membrane, etc.) be used to highlight whether the taupositive structures are present in the cell body or at synapses?

We performed the co-staining of Tau and Elav to assess the aggregated Tau localization. We found that in the presence of Pfdn5, Tau is predominantly cytoplasmic and localised to the cell body and axons. In the absence of Pfdn5, Tau forms aggregates but is still localized to the cell body or axons. However, some of the aggregates are very large, and the subcellular localization could not be determined (Figure S8M-N'). These might represent brain regions of possible nuclear breakdown and cell death (JACKSON et al. 2002).

(c) It would also be helpful to perform western blots from larval (and adult) brains examining tau protein levels, phospho-tau species, possible higher-molecular weight oligomeric forms, and insoluble vs. soluble species. These studies would be especially important to help interpret the potential mechanisms of observed interactions.

Western blot analysis revealed that overexpression of Pfdn5 does not alter total Tau levels (Figure 6O). In Pfdn5 mutants, however, hTau^V337M levels were reduced in the supernatant fraction and increased in the pellet fraction, indicating a shift from soluble monomeric Tau to aggregated Tau.

(d) Does overexpression of Pdn5 (UAS-Pdn5) suppress the formation of tau aggregates? I would therefore recommend that additional experiments be performed looking at adult flies (perhaps in Pfdn5 heterozygotes or using RNAi due to the larval lethality of Pdn5 null animals).

Overexpression of Pfdn5 significantly reduced Tau-aggregates (Elav-Gal4/UASTau^V337M; UAS-Pfdn5; DPfdn5^15/40) observed in Pfdn5 mutants (Figure 5E). Coexpression of Pfdn5 and hTau^V337M suppresses the Tau aggregates/puncta in 30-day adult brain. Since heterozygous DPfdn¹⁵/+ did not show a reduction in Pfdn5 levels, we did not test the suppression of Tau aggregates in  DPfdn¹⁵/+; Elav>UAS-Pfdn5, UAS-Tau^V337M.

(11) Figure 6, panels A-N: The GMR>Tau rough eye is not a "neurodegenerative" but rather a predominantly developmental phenotype. It results from aberrant retinal developmental patterning and the subsequent secretion/formation of the overlying eye cuticle (lenslets). I am confused by the data shown suggesting a "shrinking eye size" and increasing roughened surface over time (a GMR>tau eye similar to that shown in panel B cannot change to appear like the one in panel H with aging). The rough eye can be quite variable among a population of animals, but it is usually fixed at the time the adult fly ecloses from the pupal case, and quite stable over time in an individual animal. Therefore, any suppression of the Tau rough eye seen at 30 days should be appreciable as soon as the animals eclose. These results need to be clarified. If indeed there is robust suppression of Tau rough eye, it may be more intuitive and clearer to include these data with Figure 1, when first showing the loss-of-function enhancement of the Tau rough eye. Also, why is Pfdn6 included in these experiments but not in the studies shown in Figures 2-5?

We thank the reviewer for their careful and knowledgeable assessment of the GMR>Tau rough eye model. We appreciate the clarification that the rough eye phenotype could be “developmental” rather than neurodegenerative.”  Our initial observations regarding "shrinking eye size" and "increased surface roughness" clearly show age-related progression of structural change.   Such progression has been observed and reported by others (IIJIMA-ANDO et al. 2012; PASSARELLA AND GOEDERT 2018).   We observed an age-dependent increase in the number of fused ommatidia in GMR-Gal4 >Tau, which were rescued by Pfdn5 or Pfdn6 expression. We noted that adult-specific induction of hTau^V337M adult flies using the Gal80^ts and GMR-GeneSwitch (GMR-GS) systems was not sufficient to induce a significant eye phenotype; thus, early expression of Tau in the developing eye imaginal disc appears to be required for the adult progressive phenotype that we observe. We feel that it is inadequate to refer to this adult progressive phenotype as “developmental,” and while admittedly arguable whether this can be termed “degenerative.”   

To address neurodegeneration more directly, we focused on 30-day-old adult fly brains and demonstrated that Pfdn5 overexpression suppresses age-dependent Tau-induced neurodegeneration in the central nervous system (Figure 6H-N and Figure S12). This supports our central conclusion regarding the neuroprotective role of Pfdn5 in age-associated Tau pathology. Since we found an enhancement in the Tau-induced synaptic and eye phenotypes by Pfdn6 knockdown, we also generated CRISPR/Cas9-mediated loss-of-function mutants for Pfdn6. However, loss of Pfdn6 resulted in embryonic/early first instar lethality, which precluded its detailed analysis at the larval stages.

(12) Figure 6, panels O-T: the elav>tau image appears to show a different frontal section plane compared to the other panels. It is advisable to show images at a similar level in all panels since vacuolar pathology can vary by region. It is also useful to be able to see the entire brain at a lower power, but the higher power inset view is obscuring these images. I would recommend creating separate panels rather than showing them as insets.

In the revised figure, we now display the low- and high-magnification images as separate, clearly labeled panels instead of using insets. This improves visibility of the brain morphology while providing detailed views of the vacuolar pathology (Figure 6H-L).

(13) Figure 6/7: For the experiments in which Pfdn5/6 is overexpressed and possibly suppresses tau phenotypes (brain vacuoles and memory), it is important to use controls that normalize the number of UAS binding sites, since increased UAS sites may dilute GAL4 and reduced Tau expression levels/toxicity. Therefore, it would be advisable to compare with Elav>Tau flies that also include a chromosome with an empty UAS site or other transgenes, such as UAS-GFP or UAS-lacZ.

We thank the reviewer for the suggestion. Now we have incorporated proper controls in the brain vacuolization, the mushroom body, and ommatidial fusion rescue experiments. Also, we have independently verified whether Gal4 dilution has any effect on the Tau phenotypes (Figure 6H-L, Figure 7, and Figure S11A-B).

(14) Lines 311-312: the authors say vacuolization occurs in human neurodegenerative disease, which is not really true to my knowledge and definitely not stated in the citation they use. Please re-phrase.

Now we have made the appropriate changes in the revised manuscript.

(15) Figure 7: The authors claim that Pfdn5/6 expression does not impact memory behavior, but there in fact appears to be a decrease in preference index (panel D vs panel B). Does this result complicate the interpretation of the potential interaction with Tau (panel F). Are data from wildtype control flies available?

In our memory assay, a decrease in performance index (PI) of the trained flies compared to the naïve flies indicates memory formation (normal memory in control flies, Figure 7B). In contrast, a lack of significant difference in PI indicates a memory defect (Figure 7C: hTau^V337M overexpressed flies). "Decrease in preference index (panel D vs panel B)" is not a sign of memory defect; it may be interpreted as a better memory instead. Hence, neuronal overexpression of Pfdn5 (Figure 7D) or Pfdn6 (Figure 7E) in wildtype neurons does not cause memory deficits. In addition, coexpression of Pfdn5/6 and hTau^V337M successfully rescues the Tau-induced memory defect (significant drop in PI compared to the PI of naïve flies in Figure 7F-G). Moreover, almost complete rescue of the Tau-induced mushroom body defect on Pfdn5 or Pfdn6 expression further establishes potential interaction between Pfdn5/6 and Tau. This data has been incorporated into the revised manuscript.

The memory assay itself with extensive data on wildtype flies and various other genotype will shortly be submitted for publication in another manuscript (Majumder et al, manuscript under preparation); However, we can confirm for the reviewer that wildtype flies, trained and assayed by the protocol described, show a significant decrease in performance index compared to the naïve flies, indicative of strong learning and memory performance, very similar to the control genotype data shown in Figure 7B. 

Additional minor considerations

(16) Lines 50-52: there are many therapeutic interventions for treating tauopathies, but not curative or particularly effective ones.

Now we have made the appropriate changes in the revised manuscript.

(17) Lines 87-106 seem like a duplication of the abstract. Consider deleting or condensing.

We have made the appropriate changes in the revised manuscript.

(18) Where is pfdn5 expressed? Development v. adult? Neuron v. glia? Conservation?

Prefoldin5 is expressed throughout development but strongly localized to the larval trachea and neuronal axons. Drosophila Pfdn5 shows 35% overall identity with human PFDN5. 

(19) Liine 187: is pfdn5 truly "novel"?

The role of Pfdn5 as microtubule-binding and stabilizing is a new finding and has not been predicted or described before. Hence, it is a novel neuronal microtubule-associated protein.  

(20) Figure 5, panel F, genotype labels on the x-axis are confusing; consider simplifying to Control, DPfdn, and Rescue.

We have made appropriate changes in the figure for better readability.

(21) Figures 5/8: it might be preferable to use consistent colors for Tau/HRP--Tau is labeled green in Figure 5 and then purple in Figure 8.

We have made these changes where possible. 

(22) Lines 311-312: Vacuolar neuropathology is NOT typically observed in human Tauopathy.

We thank the reviewer for pointing this out. We have made the appropriate changes in the revised manuscript.

(23) Lines 328-349: The explanation could be made more clear. Naïve flies should not necessarily be called controls. Also, a more detailed explanation of how the preference index is computed would be helpful. Why are some datapoints negative values?

(a) We have rewritten this paragraph to make the description and explanation clearer. The detailed method and formula to calculate the Preference index have been incorporated in the Materials and Methods section.

(b) We have replaced the term Control with Naïve. 

(c) Datapoints with negative values appeared in some of the 'Trained' group flies. It indicates that post-CuSO₄ training, some groups showed repulsion towards the otherwise attractive odor 2,3B. As 2,3B is an attractive odorant, naïve or control flies show attraction towards it compared to air, which is evident from a higher number of flies in the Odor arm (O) compared to that of the Air arm (A) of the Y-maze; thus, the PI [(O-A/O+A)*100] is positive in case of naïve fly groups. Training of the flies led to an association of the attractive odorant with bitter food, leading to a decrease of attraction, and even repulsion towards the odorant in a few instances, resulting in less fly count in the odor arm compared to the air arm. Hence, the PI becomes negative as (O-A) is negative in such instances. Thus, it is not an anomaly but indicates strong learning. 

(24) Line 403: misspelling "Pdfn"

We have corrected this.

(25) Lines 423-425: recommend re-phrasing, since tauopathies are human diseases. Mice and other animal models may be susceptible to tau-mediated neuronal dysfunction but not Tauopathy, per see.

We have made the appropriate changes in the revised manuscript.

(26) Lines 468-469: "tau neuropathology" rather than "tau associated neuropathies".

We have made the appropriate changes in the revised manuscript. 

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