Author response:

The following is the authors’ response to the original reviews

Public reviews:

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors Eapen et al. investigated the peptide inhibitors of Cdc20. They applied a rational design approach, substituting residues found in the D-box consensus sequences to better align the peptides with the Cdc20-degron interface. In the process, the authors designed and tested a series of more potent binders, including ones that contain unnatural amino acids, and verified binding modes by elucidating the Cdc-20-peptide structures. The authors further showed that these peptides can engage with Cdc20 in the cellular context, and can inhibit APC/CCdc20 ubiquitination activity. Finally, the authors demonstrated that these peptides could be used as portable degron motifs that drive the degradation of a fused fluorescent protein.

Strengths:

This manuscript is clear and straightforward to follow. The investigation of different peptide variations was comprehensive and well-executed. This work provided the groundwork for the development of peptide drug modalities to inhibit degradation or apply peptides as portable motifs to achieve targeted degradation. Both of which are impactful.

Weaknesses:

A few minor comments:

(1) In my opinion, more attention to the solubility issue needs to be discussed and/or tested. On page 10, what is the solubility of D2 before a modification was made? The authors mentioned that position 2 is likely solvent exposed, it is not immediately clear to me why the mutation made was from one hydrophobic residue to another. What was the level of improvement in solubility? Are there any affinity data associated with the peptide that differ with D2 only at position 2?

The reviewer is correct that we have not done any detailed solubility characterisation; we refer only to observations rather than quantitative analysis. We wrote that we reverted from Leu to Ala due to solubility - we have clarified this statement (page 11) to say that that we reverted to Ala, as it was the residue present in D1, for which we observed a measurable affinity by SPR and saw a concentration-dependent response in the thermal shift analysis. We do not have any peptides or affinity data that explore single-site mutations with the parental peptide of D2. D2 is included in the paper because of its link to the consensus D-box sequence and thus was the logical path to the investigations into positions 3 and 7 that come later in the manuscript.

(2) I'm not entirely convinced that the D19 density not observed in the crystal structure was due to crystal packing. This peptide is peculiar as it also did not induce any thermal stabilization of Cdc20 in the cellular thermal shift assay. Perhaps the binding of this peptide could be investigated in more detail (i.e., NMR?) Or at least more explanation could be provided.

This section has been clarified (page 16). The lack of observed density was likely due to the relatively low affinity of D19 and also to the lack of binding of the three C-terminal residues in the crystal, and consequently it has a further reduced affinity. The current wording in the manuscript puts greater emphasis on this second aspect being a D19-specific issue, even though it applies to all four soaked peptides. The extent of peptide-induced thermal stabilisations observed by TSA and CETSA is different, with the latter experiment consistently showing smaller shifts. This observation may be due to the more complex medium (cell lysate vs. purified protein) and/or different concentrations of the proteins in solution. In the CETSA, we over-expressed a HiBiT-tagged Cdc20, which is present in addition to any endogenously expressed Cdc20. Although we did not investigate it, the near identical D-box binding sites on Cdc20 and Cdh1 would suggest that there will be cross-specificity, which could further influence the CETSA experiments.

The section now reads:

“We therefore assume that this is the reason for the lack of observed density in this region of the peptides D20 and D21 (Fig. S3E and S3F, respectively). We believe that it causes a reduction in binding affinities of all peptides in crystallo, given the evidence from SPR highlighting a role of position 7 in the interaction (Table 1). Interestingly, the observed electron density of the peptide correlates with Cdc20 binding affinity: D21 and D20, having the highest affinities, display the clearest electron density allowing six amino acids to be modeled, whereas D7 shows relatively poor density permitting modelling of only four residues. For D19, the lack of density observed likely reflects its intrinsically weaker affinity compared to the other peptides, in addition to losing the interactions from position 7 due to crystal packing.”

Reviewer #2 (Public review):

Summary:

The authors took a well-characterised (partly by them), important E3 ligase, in the anaphase-promoting complex, and decided to design peptide inhibitors for it based on one of the known interacting motifs (called D-box) from its substrates. They incorporate unnatural amino acids to better occupy the interaction site, improve the binding affinity, and lay foundations for future therapeutics - maybe combining their findings with additional target sites.

Strengths:

The paper is mostly strengths - a logical progression of experiments, very well explained and carried out to a high standard. The authors use a carefully chosen variety of techniques (including X-ray crystallography, multiple binding analyses, and ubiquitination assays) to verify their findings - and they impressively achieve their goals by honing in on tight-binders.

Weaknesses:

Some things are not explained fully and it would be useful to have some clarification. Why did the authors decide to model their inhibitors on the D-box motif and not the other two SLiMs that they describe?

For completeness, in addition to the D-box we did originally construct peptides based on the ABBA and KEN-box motifs, but they did not show any shift in melting temperature of cdc20 in the thermal shift assay whereas the D-box peptides did; consequently, we focused our efforts on the D-box peptides. Moreover, there is much evidence from the literature that points to the unique importance of the D-box motif in mediating productive interactions of substrates with the APC/C (i.e. those leading to polyubiquitination & degradation). One of the clearest examples is a study by Mark Hall’s lab (described in Qin et al. 2016), which tested the degradation of 15 substrates of yeast APC/C in strains carrying alleles of Cdh1 in which the docking sites for D-box, KEN or ABBA were mutated. They observed that whereas degradation of all 15 substrates depended on D-box binding, only a subset required the KEN binding site on Cdh1 and only one required the ABBA binding site. A more recent study from David Morgan’s lab (Hartooni et al. 2022) looking at binding affinities of different degron peptides concluded that KEN motif has very low affinity for Cdc20 and is unlikely to mediate degradation of APC/C-Cdc20 substrates. Engagement of substrate with the D-box receptor is therefore the most critical event mediating APC/C activity and the interaction that needs to be blocked for most effective inhibition of substrate degradation.

We have added the following text to the Results section “Design of D-box peptides” (page 10):

“We focused on D-box peptides, as there is much evidence from the literature that points to the unique importance of the D-box motif in mediating productive interactions of substrates with the APC/C (i.e. those leading to polyubiquitination & degradation). One of the clearest examples is a study that tested the degradation of 15 substrates of yeast APC/C in strains carrying alleles of Cdh1 in which the docking sites for D-box, KEN or ABBA were mutated ((Qin et al. 2017)). They observed that, whereas degradation of all 15 substrates depended on D-box binding, only a subset required the KEN binding site on Cdh1 and only one required the ABBA binding site. A more recent study (Hartooni et al. 2022) of binding affinities of different degron peptides concluded that KEN motif has very low affinity for Cdc20 and is unlikely to mediate degradation of APC/C-Cdc20 substrates. Engagement of substrate with the D-box receptor is therefore the most critical event mediating APC/C activity and the interaction that needs to be blocked for most effective inhibition of substrate degradation.”

What exactly do they mean when they say their 'observation is consistent with the idea that high-affinity binding at degron binding sites on APC/C, such as in the case of the yeast 'pseudo-substrate' inhibitor Acm1, acts to impede polyubiquitination of the bound protein'? It's an interesting thing to think about, and probably the paper they cite explains it more but I would like to know without having to find that other paper.

Interesting results from a number of labs (Choi et al. 2008,  Enquist-Newman et al. 2008,  Burton et al. 2011, Qin et al. 2019) have shown that mutation of degron SLiMs in Acm1 that weaken interaction with the APC/C have the unexpected consequence of converting Acm1 from APC/C inhibitor to APC/C substrate. A necessary conclusion of these studies is that the outcome of degron binding (i.e. whether the binder functions as substrate or inhibitor) depends on factors other than D-box affinity and that D-box affinity can counteract them. One idea is that if a binder interacts too tightly, this removes some flexibility required for the polyubiquitination process. The most recent study on this question (Qin et al.2019) specifically pins the explanation for the inhibitory function of the high affinity D-box in Acm1 on its ‘D-box Extension’ (i.e. residues 8-12) preventing interaction with APC10.  In our current study, the binding affinity of peptides is measured against Cdc20. In cellular assays however, the D-box must also engage APC10 for degradation to occur. It may be that the peptide binding most strongly to the D-box pocket on Cdc20 is less able to bind to APC10 and therefore less effective in triggering APC10-dependent steps in the polyubiquitination pathway. The important Hartooni et al. paper from David Morgan’s lab confirms that even though the binding of D-box residues to APC10 is very weak on its own, it can contribute 100X increase in affinity of a peptide by adding cooperativity to the interaction of D-box with co-activator. Re Figure 6 and the fact that we did look at peptide binding in cells, these experiments were done in unsynchronised cells, so most Cdc20 would not be bound to APC/C.

We have modified the text (page 18) from:

“However, we found the opposite effect: D2 and D3 showed increased rates of mNeon degradation compared to D1 and D19 (Fig. 8C,D). This observation is consistent with the idea that high-affinity binding at degron binding sites on APC/C, such as in the case of the yeast ‘pseudo-substrate’ inhibitor Acm1, acts to impede polyubiquitination of the bound protein (Qin et al. 2019). Indeed, there is no evidence that Hsl1, which is the highest affinity natural D-box (D1) used in our study, is degraded any more rapidly than other substrates of APC/C in yeast mitosis. As shown in Qin et al., mutation of the high affinity D-box in Acm1 converts it from inhibitor to substrate (Qin et al. 2019). Overall, our results support the conclusions that all the D-box peptides engage productively with the APC/C and that the highest affinity interactors act as inhibitors rather than functional degrons of APC/C.”

to:

“However, we found the opposite effect: D2 and D3 showed increased rates of mNeon degradation compared to D1 and D19 (Fig. 8C,D). This observation is consistent with conclusions from other studies that affinity of degron binding does not necessarily correlate with efficiency of degradation.  Indeed, there is no evidence that Hsl1, which is the highest affinity natural D-box (D1) used in our study, is degraded any more rapidly than other substrates of APC/C in yeast mitosis. A number of studies of a yeast ‘pseudo-substrate’ inhibitor Acm1, have shown that mutation of the high affinity D-box in Acm1 converts it from inhibitor to substrate (Choi et al. 2008,  Enquist-Newman et al. 2008,  Burton et al. 2011) through a mechanism that governs recruitment of APC10 (Qin et al. 2019). Our study does not consider the contribution of APC10 to binding of our peptides to APC/C^Cdc20 complex, but since there is strong cooperativity provided by this additional interaction (Hartooni et al. 2022) we propose this as the critical factor in determining the ability of the different peptides to mediate degradation of associated mNeon.”

Reviewer #3 (Public review):

Summary:

Eapen and coworkers use a rational design approach to generate new peptide-inspired ligands at the D-box interface of cdc20. These new peptides serve as new starting points for blocking APC/C in the context of cancer, as well as manipulating APC/C for targeted protein degradation therapeutic approaches.

Strengths:

The characterization of new peptide-like ligands is generally solid and multifaceted, including binding assays, thermal stability enhancement in vitro and in cells, X-ray crystallography, and degradation assays.

Weaknesses:

One important finding of the study is that the strongest binders did not correlate with the fastest degradation in a cellular assay, but explanations for this behavior were not supported experimentally. Some minor issues regarding experimental replicates and details were also noted.

Interesting results from a number of labs (Choi et al. 2008,  Enquist-Newman et al. 2008,  Burton et al. 2011, Qin et al. 2019) have shown that mutation of degron SLiMs in Acm1 that weaken interaction with the APC/C have the unexpected consequence of converting Acm1 from APC/C inhibitor to APC/C substrate. A necessary conclusion of these studies is that the outcome of degron binding (i.e. whether the binder functions as substrate or inhibitor) depends on factors other than D-box affinity and that D-box affinity can counteract them. One idea is that if a binder interacts too tightly, this removes some flexibility required for the polyubiquitination process. The most recent study on this question (Qin et al.2019) specifically pins the explanation for the inhibitory function of the high affinity D-box in Acm1 on its ‘D-box Extension’ (i.e. residues 8-12) preventing interaction with APC10.  In our current study, the binding affinity of peptides is measured against Cdc20. In cellular assays however, the D-box must also engage APC10 for degradation to occur. It may be that the peptide binding most strongly to the D-box pocket on Cdc20 is less able to bind to APC10 and therefore less effective in triggering APC10-dependent steps in the polyubiquitination pathway. The important Hartooni et al. paper from David Morgan’s lab confirms that even though the binding of D-box residues to APC10 is very weak on its own, it can contribute 100X increase in affinity of a peptide by adding cooperativity to the interaction of D-box with co-activator. Re Figure 6 and the fact that we did look at peptide binding in cells, these experiments were done in unsynchronised cells, so most Cdc20 would not be bound to APC/C.

We have modified the text (page 18) from:

“However, we found the opposite effect: D2 and D3 showed increased rates of mNeon degradation compared to D1 and D19 (Fig. 8C,D). This observation is consistent with the idea that high-affinity binding at degron binding sites on APC/C, such as in the case of the yeast ‘pseudo-substrate’ inhibitor Acm1, acts to impede polyubiquitination of the bound protein (Qin et al. 2019). Indeed, there is no evidence that Hsl1, which is the highest affinity natural D-box (D1) used in our study, is degraded any more rapidly than other substrates of APC/C in yeast mitosis. As shown in Qin et al., mutation of the high affinity D-box in Acm1 converts it from inhibitor to substrate (Qin et al. 2019). Overall, our results support the conclusions that all the D-box peptides engage productively with the APC/C and that the highest affinity interactors act as inhibitors rather than functional degrons of APC/C.”

to:

“However, we found the opposite effect: D2 and D3 showed increased rates of mNeon degradation compared to D1 and D19 (Fig. 8C,D). This observation is consistent with conclusions from other studies that affinity of degron binding does not necessarily correlate with efficiency of degradation.  Indeed, there is no evidence that Hsl1, which is the highest affinity natural D-box (D1) used in our study, is degraded any more rapidly than other substrates of APC/C in yeast mitosis. A number of studies of a yeast ‘pseudo-substrate’ inhibitor Acm1, have shown that mutation of the high affinity D-box in Acm1 converts it from inhibitor to substrate (Choi et al. 2008,  Enquist-Newman et al. 2008,  Burton et al. 2011) through a mechanism that governs recruitment of APC10 (Qin et al. 2019). Our study does not consider the contribution of APC10 to binding of our peptides to APC/C^Cdc20 complex, but since there is strong cooperativity provided by this additional interaction (Hartooni et al. 2022) we propose this as the critical factor in determining the ability of the different peptides to mediate degradation of associated mNeon.”

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) On page 12 (towards the end), the author stated D10 contained an A3P mutation, they meant P3A right? 'To test this hypothesis, we proceeded to synthesise D10, a derivative of D4 containing an A3P single point mutation.'

We thank the reviewer for spotting this typo, which we have corrected.

(2) Have the authors considered other orthogonal approaches to cross-examine/validate binding affinities? That said, I do not think extra experiments are necessary.

We did not explore further orthogonal approaches due to the challenges of producing sufficient amounts of the Cdc20 protein. Due to the low affinities of many peptides for Cdc20, many techniques would have required more protein than we were able to produce. We believe that the qualitative TSA combined with the SPR is sufficient to convince the readers; indeed there is a correlation between SPR-determined binding affinities and the thermal shifts: For the natural amino acid-containing peptides (Table 1) D19 has the highest affinity and causes the largest thermal shift in the Cdc20 melting temperature, D10 has the lowest affinity and causes the smallest thermal shift, and D1, D3, D4, and D5 and all rank in the middle by both techniques. For those peptides containing unnatural amino acids (Table 2), again higher affinities are reflected in larger thermal shifts.

Reviewer #2 (Recommendations for the authors):

The data seem fine to me. I would appreciate a little more detail on the points mentioned in the public review. Also a thorough reread, maybe by a disinterested party as there are various typos that could be corrected - all in all an excellent clear paper that encompasses a lot of work.

A colleague has carefully checked the manuscript, and typos have been corrected.

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

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Reply to the reviewers

1. Description of the planned revisions

Insert here a point-by-point reply that explains what revisions, additional experimentations and analyses are planned to address the points raised by the referees.

The following revisions are in progress:

- From Reviewer-1: The authors observe defects in CNCCs through genomic experiments. It would be really nice to perform simple wound healing/scratch assays and/or transwell assays to test if the CNCC migration phenotype is reduced in the CHD3 KO as well which would support the transcriptomic data.

As recommended by the Reviewer, we are performing a transwell assays to investigate whether CHD3 loss leads to defects in cell migration. These experiments should be completed in the next two weeks.

__- From Reviewer-2: __Since CHD3 shows a progressive upregulation in expression during CNCC differentiation (Fig. 2E), one hypothesis can be that it is not necessary involved in the activation of the CNCC programs but instead it is involved in maintaining these programs active - by keeping regulatory elements accessible. Thus, authors should check expression of CNCC markers, and EMT genes at the same time point than Fig. 2E in both WT and KO cells.

As recommended by the reviewer we are differentiating the cells to perform RT-qPCR timecourse for CNCC and EMT markers. These experiments will be completed in the next two weeks.

__- From Reviewer-2: __It has been shown that CNCC regulatory elements controlling differentiation genes are primed/accessible prior migration (PMID: 31792380; PMID: 33542111). Since the authors claim "CHD3 may have the role of priming the developing CNCCs to respond to BMP by opening the chromatin at the BMP responsive enhancers", it will be good to perform ATAC-seq are several time point during the differentiation process to assess the dynamic of chromatin reorganization to see when the switch to mesoderm fate occurs and how accessibility of BMP responsive element changes in WT and KO cells during CNCC differentiation to be able to demonstrate the KO fail to make BMP responsive element accessible or whether it is a defect in the maintenance of this accessibility.

As recommended by the Reviewer, we are differentiating the cells to perform ATAC-seq timecourse. These experiments will be completed in the next two/three weeks.

2. Description of the revisions that have already been incorporated in the transferred manuscript

The following revisions have already been carried out:

Reviewer1

1. Figure 1 presents nice confirmation of the CHD3 KO cell lines being used. However, given that these cell lines were previously published, I suggest moving these data to the supplement. As suggested by the Reviewer, we moved most of Figure 1 to the supplement, merging the remaining Figure 1 with Figure 2.

In the results section for Figure 1, the authors discuss the CHD3 heterozygotes, but I only see the KO cell line data presented. It would be especially nice to see the protein levels of Chd3 in the het.

As suggested, we have now performed western blot and qPCR for CHD3 in the heterozygous line and added it to Supplementary Figure S1.

The authors discuss which genes are up and downregulated in the Chd3 KO D18 RNA-seq, and show a clear heatmap in Figure 2A for WT cells. The same heatmap for candidate genes discussed in the results would be appreciated for Chd3 KO.

As recommended by the Reviewer, we have added CHD3-KO RNA-seq to the heatmap in Fig. 2A.

In general 2-3 replicates are presented. While the authors are showing heatmaps for selected locations for individual clones, which is appreciated (ex: Figure 4B and Fig 6), the QC for data quality is missing. For example, show spearmean correlation across the genome for datasets as a supplement.

We performed spearman correlation of ATAC-seq and RNA-seq data, which confirmed the replicates are very highly correlated, and created new dedicated supplemental figures (Supplemental Figures S3, S4, S5, S6, S7).

In the section discussing the results presented in Figure 4, the authors discuss the ATAC-seq peak number changes and overlap with gene expression changes. However, the overlap with gene expression changes is not shown. Making a simple Venn diagram would help readers.

As suggested, we added a Venn diagram with ATAC-seq/RNA-seq overlap in Figure 3D.

In addition, showing a heatmap for unchanged ATAC-seq peaks can help to demonstrate the increase/decrease.

As recommended, we have added an heatmap for unchanged ATAC-seq regions as Supplementary Figure S7.

In Figure 6, the authors present ChIPseq data for CHD3 in D14 and D18 samples, focusing on locations losing or gaining accessibility. What is enrichment at unchanged sites? Is CHD3 specifically enriched at changed locations? Then what about over genes with altered gene expression vs not changed? Is CHD3 only bound to distal elements? Performing an analysis of the peak distribution, perhaps with ChromHMM or other methods to look at promoter vs enhancer vs other locations. These types of analyses could really enrich the interpretation of direct CHD3 function.

Unfortunately, there is no ChromHMM data for neural crest cells, nor for closely related cell types. Therefore, to address the Reviewer's suggestion, we have taken two approaches: 1) We have further broken down the distribution of the peaks, dividing them between intergenic, intronic, exonic and TSS. Moreover, we have leveraged publicly available H3K27ac ChIP-seq data generated (by our group) in iPSC-derived CNCCs to identify CHD3 peaks that are decorated by this histone modification which typically marks active enhancers. This analysis revealed that 91% of the peaks are either intergenic (50%) or intronic (41%) and that ~a third of the peaks are decorated with H3K27ac in human iPSC-derived CNCCs, suggesting that they are bona-fide active enhancers in this cell type.

Related to the above, I am not sure if there is a phenotypic test for enhanced mesoderm. I suspect only IF/expression and morphology are possible, which the authors did. However, sorting the cells (with some defined markers) to ask how many are mesoderm-like vs CNCC in WT vs CHD3 KO would give some information outside of the bulk expression data.

The manuscript already included IF experiments for mesodermal markers, which clearly show that nearly all the cells acquired the mesodermal fate. See for example Brachyury IF in Figure 2E.

Minor points Reviewer-1: 12. 1A seems to fit better with Figure 2. Done 13. The authors say that the KO cell lines are not defective in pluripotency, but Figures 1G suggests a slight decrease in SSEA-1. Is this reproducibly observed? It is not statistically significant and not reproducibly observed. 14. Would be nice to show number of up and downregulated genes in volcano plots for fast viewing of readers (ex: Fig 2B). We have modified the volcano plot as suggested. 15. Is it fair to use violin plots when data points are only 2-3 replicates (as in Figures 2C, 3D). To address this, we have layered the actual datapoints on top of the violin plots.

The labels in Fig 4A and 5E are very hard to read.We have changed color to improve readability. 17. For browser tracks, the authors show very zoomed in examples (Fig 4C, and especially Fig 6C). showing a bit more of the area around these peaks would give readers a more clear appreciation of the data. Related to browser tracks, including more information just as including the gene expression changes (such as in Fig 6C) to enhance the interpretation of the impact of Chd3 binding, accessibility change and then, I presume, reduced Sox9 expression. Similar suggestion for Figure 4C, where I anticipate coordinate transcription changes of the associated genes. We have zoomed out the tracks, as suggested, and added expression data next to them. 19. Do the authors observe any clone variability between the two CHD3 KO clones? There is variability I see in some of the heatmaps, but don't know if that it is because of clones or technical variation. We do not observe any significant variability between the clones.

Reviewer-2 1. What is the expression level of CHD3 in the heterozygote line? Does the remaining allele compensate for the loss which will explain the absence of phenotype?

Ass suggested also by Reviewer-1, we have performed western blot for CHD3 in the heterozygous line and added it to Supplementary Figure S1. The bot shows that the remaining allele does not compensate. However it is likely that even a reduced amount of wild-type CHD3 is sufficient for proper CNCC specification.

The authors should use the term "regulatory elements" instead of "enhancers" as they can act either as activator or repressors.

As suggested, we have changed nomenclature from enhancers to cis-regulatory elements.

On the same line, while the authors indicate "Motif analysis of the enhancers aberrantly active in CHD3-KO cells ", they haven't shown these are active. They should say they perform the analysis on regulatory elements aberrantly accessible in CHD3 KO. Done.

See point 3 above.

The rationale that led the authors to focus on genes typically expressed in the primitive streak and in the early pre-migratory mesoderm, and BMP responsive transcription factors could be better explained. Are they part of the most deregulated genes in the RNA-seq analysis?

Not only mesodermal genes are among the most upregulated genes in the RNA-seq, but the motifs for the transcription factors encoded by these genes (e.g. TBR2, Brachyury, GATA, TBX3, TBX6) are among the most frequently represented in the aberrantly accessible cis-regulatory elements. The same applies to BMP responsive factor, but the other way around (they are downregulated and enriched in the aberrantly closed ATAC-seq regions).

In the absence of CHD3, BMP response is not effective. While the authors nicely showed this is linked with changes in chromatin accessibility, it is necessary to check the expression levels of BMP receptors in CHD3 KO cells.

We have checked the expression of these genes, and they were not differentially expressed. This is consistent with the downstream response being affected rather than ligand binding to the receptors.

Aberrant early mesoderm signature of the CHD3-KO cells needs to be better shown. It is not obvious from the GO analysis in Fig. 2 and the authors then showed expression of some markers but it is unclear how they picked them up.

See point 5: not only mesodermal genes are among the most upregulated genes in the RNA-seq, but the motifs for the transcription factors encoded by these genes (e.g. TBR2, Brachyury, GATA, TBX3, TBX6) are among the most frequently represented in the aberrantly accessible cis-regulatory elements. See for example expression levels of typical mesodermal genes below:

EOMES - upregulated log2FC: 5.5

TBXT - upregulated log2FC: 4.6

MESP1 - upregulated log2FC: 4.7

MIXL1 - upregulated log2FC: 5.4

TBX6 - upregulated log2FC: 3.2

MSGN1 - upregulated log2FC: 4.6

HAND1 - upregulated log2FC: 5.5

The authors claim CHD3 directly binds at BMP responsive enhancers, but in the figure, they show the data for all the region gaining or losing activity. It will be nice to add the information for the BMP responsive elements only.

As recommended, we have added an heatmap for BMP responsive regions only, clearly showing that CHD3 binds them (Supplementary Figure S7).

The authors need to support better that CHD3-KO express more Wnt signaling/activity.

We have checked expression of many genes that are typically Wnt responsive during mesoderm specification (see also point 7). These include:

EOMES - upregulated log2FC: 5.5

TBXT - upregulated log2FC: 4.6

MESP1 - upregulated log2FC: 4.7

MIXL1 - upregulated log2FC: 5.4

TBX6 - upregulated log2FC: 3.2

MSGN1 - upregulated log2FC: 4.6

HAND1 - upregulated log2FC: 5.5

These data clearly support that the Wnt-mediated mesodermal program is markedly upregulated.

Minor points Reviewer-2: 13. In the discussion, the authors could indicate whether CHD3 mutants somehow phenocopies some of the craniofacial defects observed in DLX5 mutant patients. Done. 14. It is not indicated were to find the data regarding expression epithelial and mesenchymal genes in the CHD3-KO cells. They are in the heatmap in Fig. 1C. 15. Authors could add in the discussion what is known about how CHD3 function changes from opening or closing chromatin is very intriguing a could be discussed. To our knowledge, nothing is known on this. CHD3 is significantly understudied.

OPTIONAL: While this is not necessary for the current study, it is very intriguing that other CHD family member do not compensate. How this tissue or DNA sequence activity is achieved could be discussed. What are CHD4 or CHD5 expressed during CNCC differentiation? Could they be used to rescue the CHD3 KO phenotype? While this may be difficult to test, it could perhaps be discussed.

We have added a paragraph on this in the discussion.

3. Description of analyses that authors prefer not to carry out* *

From Reviewer 1: Given the changes in the CHD3-KO accessibility are mostly gene distal, are there existing Hi-C/microC/promoter CaptureC or other that can be used to ask if these are interacting with the predicted genes?

We are not aware of this type of essays being performed genome-wide in human CNCCs. The only studies performed in human CNCCs are SOX9-centred. Looking at 3D chromatin conformation would also be out of the scope of the paper.

From Reviewer-2:

OPTIONAL: Does increasing BMP concentration early during CHD3 KO differentiation has a better effect at rescuing CNCC differentiation?

Indicated by Reviewer as OPTIONAL. We do not think that adding BMP earlier on would make a significant difference in rescuing CNCC differentiation.

From Reviewer-1: Are the results observed NuRD-based or CHD3 NuRD independent functions? Looking at other NuRD subunit binding or effects in differentiation would help to dig into this a bit more. I realize this is a bit of a big ask, so I am not asking for everything. Are there existing binding data in CNCCs for a NuRD subunit that could be examined for overlap in where these changes occur, for example? I want to be clear I am not asking the authors to do all the experiments for an alternative NuRD subunit.

There are no existing data on NuRD binding in CNCCs. However, while the Reviewer is definitely not recommending generating new data in this regard, we still decided to make an attempt at performing ChIP-seq for the core NuRD subunit MBD3 in our CNCC. We will only make one attempt (multiple replicates), and if it does not work we will not pursue this any further as the Reviewer clearly stated that this is not necessary nor required and we do not want to delay the resubmission.

Reviewer #3 (Public review):

Summary:

The authors compare how well their automatic dimension prediction approach (DimPred) can support similarity judgements and compare it to more standard RSA approaches. The authors show that the DimPred approach does better when assessing out-of-sample heterogeneous image sets, but worse for out-of-sample homogeneous image sets. DimPred also does better at predicting brain-behaviour correspondences compared to an alternative approach. The work appears to be well done, but I'm left unsure what conclusions the authors are drawing.

In the abstract, the authors write: "Together, our results demonstrate that current neural networks carry information sufficient for capturing broadly-sampled similarity scores, offering a pathway towards the automated collection of similarity scores for natural images". If that is the main claim, then they have done a reasonable job supporting this conclusion. However the importance of automating this process for broadly-sampled object categories is not made so clear.

But the authors also highlight the importance that similarity judgements have been for theories of cognition and brain, such as in the first paragraph of the paper they write: "Similarity judgments allow us to improve our understanding of a variety of cognitive processes, including object recognition, categorization, decision making, and semantic memory6-13. In addition, they offer a convenient means for relating mental representations to representations in the human brain14,15 and other domains16,17". The fact that the authors also assess how well a CLIP model using DimPred can predict brain activation suggests that their work is not just about automating similarity judgements, but highlighting how their approach reveals that ANNs are more similar to brains than previously assessed.

My main concern is with regards to the claim that DimPred is revealing better similarities between ANNs and brains (a claim that the authors may not be making, but this should be clarified). The fact that predictions are poor for homogenous images is problematic for this claim, and I expect their DimPred scores would be very poor under many conditions, such as when applied to line drawings of objects, or a variety of addition out-of-sample stimuli that are easily identified by humans. The fact that so many different models get such similar prediction scores (Fig 3) also raises questions as to the inferences you can make about ANN-brain similarity based on the results. Do the authors want to claim that CLIP models are more like brains?

With regards to the brain prediction results, why is the DimPred approach doing so much better in V1? I would not think the 49 interpretable categories are encoded in V1, and the ability to predict would likely reflect a confound rather than V1 encoding these categories (e.g., if a category was "things that are burning" then DNN might predict V1 activation based on the encoding of colour).

In addition, more information is needed on the baseline model, as it is hard to appreciate whether we should be impressed by the better performance of DimPred based on what is provided: "As a baseline, we fit a voxel encoding model of all 49 dimensions. Since dimension scores were available only for one image per category36, for the baseline model, we used the same value for each image of the same category and estimated predictive performance using cross-validation". Is it surprising that predictions are not good with one image per category? Is this a reasonable comparison?

Relatedly, what was the ability of the baseline model to predict? (I don't think that information was provided). Did the authors attempt to predict outside the visual brain areas? What would it mean if predictions were still better there?

Minor points:

The authors write: "Please note that, for simplicity, we refer to the similarity matrix derived from this embedding as "ground-truth", even though this is only a predicted similarity". Given this, it does not seem a good idea to use "ground truth" as this clarification will be lost in future work citing this article.

It would be good to have the 49 interpretable dimensions listed in the supplemental materials rather than having to go to the original paper.

Strengths:

The experiments seem well done.

Weaknesses:

It is not clear what claims are being made.

Author response:

We thank the reviewers for their comments and for their constructive suggestions. We intend to submit a revised manuscript where we address the comments made in the Public Reviews as well as in the Recommendations for the Authors.

One of our most interesting findings, as noted by the reviewers, was the discovery of a small subpopulation of cells likely arrested in G2 that accounts for a disproportionate amount of radiation-induced gene expression. In addition, to the responses indicated below, we are planning to include additional “wet lab” experiments in the revised manuscript that address the properties of this seemingly important subpopulation of cells.

Reviewer 1:

Strengths:

(1) The authors have used robust methods for rearing Drosophila larvae, irradiating wing discs, and analyzing the data with Seurat v5 and HHI.

(2) These data will be informative for the field.

(3) Most of the data is well-presented.

(4) The literature is appropriately cited.

Thank you for these comments

Weaknesses:

(1) The data in Figure 1 are single-image representations. I assume that counting the number of nuclei that are positive for these markers is difficult, but it would be good to get a sense of how representative these images are and how many discs were analyzed for each condition in B-M.

(2) Some of the figures are unclear.

In the revised manuscript, we will provide a more detailed quantitative analysis. For each condition, we analyzed 4 - 9 discs.

We assume that the reviewer in referring to panels in Figure 1. We will review these images and if necessary, repeat the experiments or choose alternative images that appear clearer.

Reviewer 2:

Overall, the data presented in the manuscript are of high quality but are largely descriptive. This study is therefore perceived as a resource that can serve as an inspiration for the field to carry out follow-up experiments.

We intend to include more  “wet lab” experiments in our revised manuscript to address the identity and properties of the high-trbl cells that we have identified using the clustering approach based on cell-cycle gene expression.

Reviewer 3:

Strengths:

Overall, the manuscript makes a compelling case for heterogeneity in gene expression changes that occur in response to uniform induction of damage by X-rays in a single-layer epithelium. This is an important finding that would be of interest to researchers in the field of DNA damage responses, regeneration, and development.

Thank you.

Weaknesses:

This work would be more useful to the field if the authors could provide a more comprehensive discussion of both the impact and the limitations of their findings, as explained below.

Propidium iodide staining was used as a quality control step to exclude cells with a compromised cell membrane. But this would exclude dead/dying cells that result from irradiation. What fraction of the total do these cells represent? Based on the literature, including works cited by the authors, up to 85% of cells die at 4000R, but this likely happens over a longer period than 4 hours after irradiation. Even if only half of the 85% are PI-positive by 4 hr, this still removes about 40% of the cell population from analysis. The remaining cells that manage to stay alive (excluding PI) at 4 hours and included in the analysis may or may not be representative of the whole disc. More relevant time points that anticipate apoptosis at 4 hr may be 2 hr after irradiation, at which time pro-apoptotic gene expression peaks (Wichmann 2006). Can the authors rule out the possibility that there is heterogeneity in apoptosis gene expression, but cells with higher expression are dead by 4 hours, and what is left behind (and analyzed in this study) may be the ones with more uniform, lower expression? I am not asking the authors to redo the study with a shorter time point, but to incorporate the known schedule of events into their data interpretation.

We thank the reviewer for these important comments. The generation of single-cell RNAseq data from irradiated cells is tricky. Many cells have already died. Even those that do not incorporate propidium iodide are likely in early stages of apoptosis or are physiologically unhealthy and likely made it through our FACS filters. Indeed, in irradiated samples up to  57% of sequenced cells were not included in our analysis since their RNA content seemed to be of low quality. It is therefore likely that our data are biased towards cells that are less damaged. As advised by the reviewer, we will include a clearer discussion of these issues as well as the time course of events and how our analysis captures RNA levels only at a single time point.

If cluster 3 is G1/S, cluster 5 is late S/G2, and cluster 4 is G2/M, what are clusters 0, 1, and 2 that collectively account for more than half of the cells in the wing disc? Are the proportions of clusters 3, 4, and 5 in agreement with prior studies that used FACS to quantify wing disc cells according to cell cycle stage?

Clusters 0, 1, and 2 likely contain cells in other stages of the cell cycle, including early G1. Other studies indicate that more than 70% of cells are expected to have a 4C DNA content 4 h after irradiation at 4000 Rad. The high-trbl cluster only accounts for 18% of cells. Thus clusters 0, 1 and 2 could potentially contain other populations that also have a 4C DNA content. Importantly, similar proportions of cells in these clusters are also observed in unirradiated discs. We are mining the gene expression patterns in these clusters with the goal of estimating their location in the cell cycle and will include those data in the revised manuscript.

The EdU data in Figure 1 is very interesting, especially the persistence in the hinge. The authors speculate that this may be due to cells staying in S phase or performing a higher level of repair-related DNA synthesis. If so, wouldn't you expect 'High PCNA' cells to overlap with the hinge clusters in Figures 6G-G'? Again, no new experiments are needed. Just a more thorough discussion of the data.

We have found that the locations of elevated PCNA expression do not always correlate with the location of EdU incorporation either by examining scRNA-seq data or by using HCR to detect PCNA. PCNA expression is far more widespread. We intend to present additional data that address this point and also a more thorough discussion in the revised manuscript.

Trbl/G2/M cluster shows Ets21C induction, while the pattern of Ets21C induction as detected by HCR in Figures 5H-I appears in localized clusters. I thought G2/M cells are not spatially confined. Are Ets21C+ cells in Figure 5 in G2/M? Can the overlap be confirmed, for example, by co-staining for Trbl or a G2/M marker with Ets21C?

The data show that the high_-trbl_ cells are higher in Ets21C transcripts relative to other cell-cycle-based clusters after irradiation. This does not imply that high-trbl-cells in all regions of the disc upregulate Ets21C equally. Ets21C expression is likely heterogeneous in both ways – by location in the disc and by cell-cycle state. We will attempt to look for co-localization as suggested by the reviewer.

Induction of dysf in some but not all discs is interesting. What were the proportions? Any possibility of a sex-linked induction that can be addressed by separating male and female larvae?

We can separate the cells in our dataset into male and female cells by expression of lncRNA:roX1/2. When we do this, we see X-ray induced dysf expressed similarly in both male and female cells. We think that it is therefore unlikely that this difference in expression can be attributed to cell sex. We are investigating other possibilities such as the maturity of discs.

I agree with this part because having a "good" design is hard to judge and can vary from person to person. Some people may believe that a good design is one that is able to generate a lot of profits and help make an organization successful financially. Others may think that a good design has to be unique, creative, and stand out from competitors. I think that those are some elements that designers may think about when creating designs, but I think it all comes back to user research and understanding their needs. I view a good design as one that meets the needs of the users and is accessible to everyone. However, this is still an unclear definition because it is difficult to know which user needs to be prioritized and which is why design can be so complex.

Welcome back, and in this lesson, I want to cover the high-level architecture of Amazon Lex. Amazon Lex is a product that allows you to create interactive chatbots. For most areas of study and for solutions architects working in the real world, you only need a basic level of understanding, and that's exactly what this video will provide. If you need to know anything beyond this, the course you're studying will likely include follow-up videos to this one. If not, don't worry—this video will cover everything that you need. Now let's jump in and get started.

Amazon Lex is a back-end service. It's not something you're likely to use from a user perspective. Instead, you'll use it to add capabilities to your application. Lex provides text or voice conversational interfaces. For the exam, remember “Lex for voice” or “Lex for Alexa.” If you're familiar with Amazon voice products, just know that Lex powers those products—it provides the conversational capability. It's what lets the lady in the tube answer your questions.

Lex provides two main bits of functionality. First is automatic speech recognition (ASR), which is simply speech-to-text. Now, I say “simple,” but doing this well is exceptionally difficult. If any of you have tried using Siri, Apple’s voice assistant, you may have noticed how often it gets things wrong compared to the Alexa product. That’s because Siri doesn’t do ASR as well as Lex. And for any lawyers listening—this is just my opinion.

Lex also provides natural language understanding (NLU) services, which allow it to discover your intent and even perform intent chaining. Imagine the act of ordering a pizza. You might start the conversation by saying, “Can I order a pizza please?” or “I want to order a pizza,” or even “A large pepperoni pizza, please.” The intent—the thing you want to do—is ordering pizza, and it's Lex's job to determine that. But what about your next sentence? “Make that an extra large, please.” Lex needs to understand that this second statement relates to the first. As humans, this is easy—we're good at natural language processing. Computers historically haven't been, but Lex enables voice and text understanding in your applications without needing to code that functionality yourself. You simply integrate Lex, and it does the hard work for you.

As a service, Lex scales well and integrates with other AWS products such as Amazon Connect. It’s quick to deploy and uses a pay-as-you-go pricing model, meaning it only costs when you’re actively using it. This makes it ideal for event-driven or serverless architectures. In terms of use cases, Lex can help you build chatbots—the kind that pop up on websites asking if you need help—or automated support chats for logging tickets. You can also build voice assistants that respond when you ask for something, just like the lady in the tube. Use cases also include Q&A bots or enterprise productivity bots—basically, any interactive bot that accepts text or voice and performs a service.

Let’s now review some of the key Lex concepts. Lex provides bots that are designed to interactively converse in one or more languages. I previously mentioned the term "intent." This represents an action the user wants to perform—things like ordering a pizza, ordering a milkshake, or getting a side of fries. In addition to intents, we have the concept of utterances. When creating an intent, you can provide sample utterances—these are ways an intent might be expressed. So to order a pizza, milkshake, or fries, a user might say “Can I order,” “I want to order,” or “Give me a.” These are all different ways of expressing or uttering an intent.

Along with configuring utterances, you also need to tell Lex how to fulfill the intent, and this is often done using Lambda integration. If Lex understands that the user wants to order a pizza, it needs a way to initiate that process—Lambda functions are typically used for this purpose. Lambda works especially well in event-driven architectures, making it a natural complement to Lex. Additionally, Lex includes the concept of a slot, which you can think of as a parameter for an intent. These might include the size of the pizza (small, medium, or large), the type of crust (normal or cheesy), and other similar details. You can configure slots as required parameters that Lex must gather from the user during the interaction.

Just to reiterate, Lex is a product you won’t usually interact with directly through the console. It’s something you’ll architect into your applications. If you want to provide interactive voice assistance via a chat or voice-capable bot, you’ll use Amazon Lex. So remember this for the exam.

With that being said, that is everything I wanted to cover in this video. Go ahead and complete the video, and when you're ready, I’ll look forward to you joining me in the next.

The final section unified all the concepts for my understanding. Real learning about race coupled with identity becomes a transformative process even though it creates emotional difficulty that pushes students toward development. The teacher promotes students to evaluate school learning effects on their daily lives beyond classrooms. The process of transformative education demonstrates knowledge acquisition as only one aspect because it primarily shifts our worldview and self-understanding.

Welcome back, and in this lesson, I want to cover the FSx products, specifically FSx for Windows File Server. FSx is a shared file system product, but it handles the implementation in a very different way than, say, EFS, which we've covered earlier in the course. FSx for Windows File Server is one of the core components of the range of services that AWS provides to support Windows environments in AWS. For a fair amount of AWS history, its support of Windows environments was pretty bad; it just didn't seem to be a priority. Now this changed with FSx for Windows File Server, which provides fully managed native Windows File Servers or, more specifically, file shares. You're provided with file shares as your unit of consumption. The servers themselves are hidden, which is similar to how RDS is architected, but instead of databases, you get file shares.

Now, it's a product designed for integration with Windows environments. It's a native Windows file system; it's not an emulated file server. It can integrate with either managed Active Directory or self-managed Active Directory, and this can be running inside AWS or on-premises. This is a critical feature for enterprises who already have their own Active Directory provision. It is a resilient and highly available system, and it can be deployed in either single or multi-AZ mode. Picking between the two controls the network interfaces available and used to access the product. It uses elastic network interfaces inside the VPC. The backend, even in single AZ mode, uses replication within that availability zone to ensure that it's resilient to hardware failure. However, if you pick multi-AZ, then you get a fully multi-AZ, highly available solution.

It can also perform a full range of different types of backups, which include both client-side and AWS-side features. I'll talk about that later in the lesson. From an AWS side, it can perform both automatic and on-demand backups. Now, file systems that are created inside the FSx product are accessible within a VPC. But also, and this is how more complex environments are supported, they can be accessed over peering connections, VPN connections, and even accessed over physical direct connects. So if you're a large enterprise with a dedicated private link into a VPC, you can access FSx file systems over Direct Connect.

Now, in the exam, when you’re faced with any questions that talk about shared file systems, you need to be looking to identify any Windows-related keywords. Look for things like native Windows file systems, look for things like Active Directory or Directory Service integration, and look for any of the more advanced features, which I’ll talk about over the remainder of this lesson. Essentially, your job in the exam is to pick when to use FSx versus EFS because these are both network shared file systems that you’ll find on the exam. Generally, EFS tends to be used for shared file systems for Linux EC2 instances as well as Linux on-premises servers, whereas FSx is dedicated to Windows environments, so that's the main distinction between these two different services.

So let's have a look visually at how a typical implementation of FSx for Windows File Server might look for an organization like Animals for Life. We start with a familiar architecture. We have a VPC on the left and a corporate network on the right, and these networks are connected with Direct Connect or VPN, with some on-premises staff members. Inside the VPC, we have two availability zones (A and B), and in each of those availability zones, we have two different private subnets. FSx uses Active Directory for its user store, so logically, we start with a directory, which can either be a managed directory delivered as a service from AWS or something that is on-premises.

Now, this is important: FSx can integrate with both, and it doesn’t actually need an Active Directory service defined inside the Directory Services product. Instead, it can connect directly to Active Directory running on-premises. This is critical to understand because it means it can integrate with a completely normal implementation of Active Directory that most large enterprises already have. As I already mentioned, FSx can be deployed either in single AZ or multi-AZ mode, and in both of those, it needs to be connected to some form of directory for its user store. Once deployed, you can create a network share using FSx, and this can be accessed in the normal way using the double backslash, DNS name, and share notation that you'll be familiar with if you use Windows environments. For example, a file system ID dot animalsforlife.org, followed by a slash and "cat pics." In this example, "cat pics" is the actual share.

Using this access path, the file system can be accessed from other AWS services that use Windows-based storage. An example of this is Workspaces, which is a virtual desktop service similar to Citrix available inside AWS. When you deploy Workspaces into a VPC, not only does it require a directory service to function, but for any shared file system needs, it can also use FSx. The most important thing to remember about FSx is that it is a native Windows file system. It supports things like deduplication, the distributed file system (DFS), which is a way Windows can group file shares together and scale out for a more managed file share structure at scale. It supports at-rest encryption using KMS, and it also lets you enforce encryption in transit. Shares are accessed using the SMB protocol, which is standard in Windows environments, and FSx even allows for volume shadow copies. In this context, volume shadow copies allow users to see multiple file versions and initiate restores from the client side.

So that’s really important to understand: if you’re utilizing an FSx share from a Windows environment, you can right-click on a file or folder, view previous versions, and initiate file-level restores without having to use AWS or engage with a system administrator. That’s something that’s provided along with the FSx product as long as it’s integrated with Windows environments—you get that capability. Now, from a performance perspective, FSx is highly performant. The performance delivered can range from anywhere from 8 megabytes per second to 2 gigabytes per second. It can deliver hundreds of thousands of IOPS and less than one millisecond latency, so it can scale up to whatever performance requirements your organization has.

Now, for the exam, you don't need to be aware of the implementation details. I’m trying to focus really on the topics and services that you need for the exam in this course. So when things do occur, I want to teach you more information than you may require for the exam, but there are a lot of topics or features of different services that you only require a high-level overview of, and this is one of those topics. So, what I want to do now is go through some keywords or features that you should be on the lookout for when you see any exam questions that you think might be related to FSx.

The first of these is DFS, a Windows feature that allows users to perform file and folder-level restores. This is one of the features that's provided and is unique to FSx, meaning that if you have any users of Workspaces and they use files and folders on an FSx share, they can right-click, view previous versions, and restore from a user-driven perspective without having to engage a system administrator. Another thing to be aware of is that FSx provides native Windows file systems that are accessible over SMB. If you see SMB mentioned in the exam, it’s probably going to be FSx as the default correct answer. Remember, the EFS file system uses the NFS protocol and is only accessible from Linux EC2 instances or Linux on-premises servers. If you see any mention of SMB, then you can be almost certain that it’s a Windows environment question and involves FSx.

Another key feature provided by FSx is that it uses the Windows permission model, so if you're used to managing permissions for folders or files on Windows file systems, you'll be used to exactly how FSx handles permissions. This is provided natively by the product specifically to support Windows environments in AWS. Next is that the product supports DFS, the distributed file system. If you see that mentioned, either its full name or DFS, then you know that this is going to be related to FSx. DFS is a way that you can natively scale out file systems inside Windows environments. You can either group file shares together in one enterprise-wide structure or use DFS for replication or scaling out performance. It’s a really capable distributed file system.

Now, if you see any questions that talk about the provision of a native Windows file server, but where the admin overhead of running a self-managed EC2 instance running something like Windows Server is not ideal, then you know that it's going to be FSx. FSx provides you with the ability to provision a native Windows file server with file shares but without the admin overhead of managing that server yourself. Lastly, the product is unique in the sense that it delivers these file shares, which can also be integrated with either directory service or your own active directory directly. These are really important things to remember for the exam, and they’ll help you select between other products and FSx.

Again, I don’t expect you to get many questions on FSx. I do know of at least one or two unique questions in the exam, but even if it only gets you that one extra mark, it can be the difference between a pass and a fail. So try your best to remember all the key features I’ve explained throughout this lesson. But at that point, that is everything I wanted to cover in this theory-only lesson. Go ahead, complete this video, and then when you're ready, I look forward to you joining me in the next.

Welcome back.

Over the next few lessons, I'm going to be covering Storage Gateway in more depth, focusing on the types of architectures it can support. The key to exam success when it comes to Storage Gateway is understanding when you would use each of the modes, as each has its own specific situation where it should or shouldn't be used. In this lesson, I'll start off with the Storage Gateway running in Volume Stored mode and Volume Cached mode—so let's jump in and get started.

Storage Gateway normally runs as a virtual machine on-premises, although it can be ordered as a hardware appliance. However, it's much more common to use the virtual machine version of this product. It acts as a bridge between storage that exists on-premises or in a data center and AWS. Locally, it presents storage using iSCSI (a SAN and NAS protocol), NFS (commonly used by Linux environments to share storage over a network), and SMB (used within Windows environments). On the AWS side, it integrates with EBS, S3, and the various types of Glacier.

As a product, Storage Gateway is used for tasks such as migrations from on-premises to AWS, extending a data center into AWS, and addressing storage shortages by leveraging AWS storage. It can implement storage tiering, assist with disaster recovery, and replace legacy tape media backup solutions. For the exam, you need to identify the correct type of Storage Gateway for a given scenario—and that's what I want to help you with in this set of lessons.

As a quick visual refresher, a Storage Gateway is typically deployed as a virtual appliance on-premises. Architecturally, you might also have some Network Attached Storage (NAS) or a Storage Area Network (SAN) running on-premises. These storage systems are used by a collection of servers—also running on-premises. The servers probably have their own local disks, but for primary storage, they're likely to connect to the SAN or NAS equipment.

These storage systems (SANs or NASs) generally use the iSCSI protocol, which presents raw block storage over the network as block devices. The servers see them as just another type of storage device to create a file system on and use normally. This is a traditional architecture in many businesses. What's also common, especially for smaller businesses, is limited funding for backups or effective disaster recovery, prompting them to consider AWS as a solution to rising operational costs or as an alternative to maintaining their own data centers.

So how does Storage Gateway work? Volume Gateway works in two different modes: Cached mode and Stored mode. They are quite different and offer distinct advantages. First, let's look at Stored mode. In this mode, the virtual appliance presents volumes over iSCSI to servers running on-premises, functioning similarly to NAS or SAN hardware. These volumes appear just like those presented by NAS or SAN devices, allowing servers to create file systems on top of them as they normally would.

In Gateway Stored mode, these volumes consume local capacity. The Storage Gateway has local storage, which serves as the primary location for all the volumes it presents over iSCSI. This is a critical point for the exam—when you're using Storage Gateway in Volume Stored mode, everything is stored locally. All volumes presented to servers are stored on on-premises local storage.

In this mode, Storage Gateway also has a separate area called the upload buffer. Any data written to the local volumes is temporarily written to this buffer and then asynchronously copied into AWS via the Storage Gateway endpoint—a public endpoint accessible over a normal internet connection or a public VIF using Direct Connect. The data is copied into S3 in the form of EBS snapshots. Conceptually, these are snapshots of the on-premises volumes, occurring constantly in the background without human intervention. That's the architecture of Storage Gateway running in Volume Stored mode. Think about the architecture and what it enables, because this is what's important for the exam.

This mode is excellent for doing full disk backups of servers. You're using raw volumes on the on-premises side, and by asynchronously backing them up as EBS snapshots, you get a reliable full disk backup solution with strong RPO and RTO characteristics. Volume Gateway in Stored mode is also great for disaster recovery, since EBS snapshots can be used to create new EBS volumes. In theory, you could provision a full copy of an on-premises server in AWS using just these snapshots.

However—and this is important for the exam—this mode doesn't support extending your data center capacity. The primary location for data using this mode is on-premises. For every volume presented, there's a full copy of the data stored locally. If you're facing capacity issues, this mode won't help. But if you need low-latency data access, this mode is ideal, as the data resides locally. It also works well for full disk backups or disaster recovery scenarios.

I emphasize “full disk” here because in the next lessons, I’ll cover other Storage Gateway modes that also help with backups. Volume Gateway deals in volumes—raw disks presented over iSCSI. Some key facts worth knowing (though not required to memorize for the exam): in Volume Stored mode, you can have 32 volumes per gateway, with up to 16 TB per volume, for a total of 512 TB per gateway.

Now let’s turn to Volume Gateway in Cached mode, which suits different scenarios. Cached mode shares the same basic architecture: the Storage Gateway still runs as a virtual appliance (or physical in some cases), local servers are still presented with volumes via iSCSI, and the Gateway still communicates with AWS via the Storage Gateway endpoint, which remains a public endpoint using either internet or Direct Connect.

The major difference is the location of the primary data. In Cached mode, the main storage location is AWS—specifically S3—rather than on-premises. The Storage Gateway now only has local cache, while the primary data for all presented volumes resides in S3. This distinction is crucial: in Volume Stored mode, the data is stored locally; in Cached mode, it’s stored in AWS and only cached locally.

Importantly, when we say the data is in S3, it's actually in an AWS-managed area of S3, visible only through the Storage Gateway console. You can’t browse it in a regular S3 bucket because it stores raw block data, not files or objects. You can still create EBS snapshots from it, just like in Stored mode.

So the key difference between Stored and Cached modes is the location of the data. Stored mode keeps everything on-premises, using AWS only for backups. Cached mode stores data in S3, caching only the frequently accessed portions locally. This offers substantial architectural benefits: since only cached data is stored locally, you can manage hundreds of terabytes through the gateway while using only a small local cache. This enables an architecture called data center extension.

For example, imagine an on-premises facility with limited space and rising storage needs. Instead of investing in more hardware, the business can extend into AWS. Storage in AWS appears local, but it's actually hosted in the cloud. While Volume Stored and Cached modes are similar in using raw volumes and supporting EBS snapshots, only Cached mode enables extending data center capacity.

Stored mode is for backups, DR, and migration. It ensures local LAN-speed access, but requires full data storage locally. Cached mode allows AWS to act as primary storage, storing frequently accessed data locally, enabling cost-effective capacity extension while maintaining low-latency access for hot data. Less frequently accessed data may load more slowly, but it allows huge scalability. In Cached mode, a single gateway can handle up to 32 volumes at 32 TB each—up to 1 PB of data.

In summary, both modes work with volumes (raw block storage), but Stored mode stores everything locally and uses AWS only for backups, while Cached mode stores data in AWS and caches hot data locally, supporting data center extension. For the exam, if you see the keyword “volume” in a Storage Gateway question, you’re dealing with Volume mode. Deciding between Stored and Cached will depend on whether the scenario focuses on backup/DR/migration or on extending capacity.

That wraps up the theory for this lesson. In the next lesson, I’ll cover another mode of Storage Gateway: Tape mode, also known as VTL mode. Go ahead and complete this lesson, and when you’re ready, I look forward to having you join me in the next.

Welcome back. In this lesson, I want to talk about AWS Direct Connect. A Direct Connect (DX) is a physical connection into an AWS region. If you order this via AWS, the connection is either 1 gig, 10 gig, or 100 gig at the time of creating this lesson. There are other ways to provision slower speeds, but I'll be covering those in a dedicated lesson later in this section of the course. The connection is between a business premises, a Direct Connect (DX) location, and finally an AWS region. I’ll show this architecture visually on the next screen.

Conceptually, think of three different physical locations: your business premises, where you have a customer premises router; a DX location, where you also have other equipment such as a DX router and maybe some servers; and finally an AWS region, such as US East 1. When you order a DX connection, what you're actually ordering is a network port at the DX location. AWS provides a port allocation and authorizes you to connect to that port, which I’ll detail soon. However, a Direct Connect ordered directly from AWS doesn’t actually provide a connection of any kind—it’s just a physical port. It’s up to you to connect to this directly or arrange the connection to be extended via a third-party communications provider.

The port has two costs: an hourly cost based on the DX location and the speed of the port, and a charge for outbound data transfer. Inbound data transfer is free of charge. There are a couple of important things to keep in mind about Direct Connect. First is the provisioning time—AWS will take time to allocate a port, and once allocated, you’ll need to arrange the connection into that port at the DX location. If you haven’t already connected the DX location to your business network, you might be looking at weeks or months of extra time for the physical laying of cables between the DX location and your business premises. Keep that in mind.

Since it’s a physical cable, there’s no built-in resilience—if the cable is cut, it’s cut. You can design in resilience by using multiple Direct Connects, but that’s something you have to layer on top. Direct Connect provides low latency because data isn’t transiting across the public internet like with a VPN. It also provides consistent latency, as you’re using a single physical cable at best or a small number of private networking links at worst. If you need low and consistent latency for an application, Direct Connect is the way to go. In addition, it’s also the best way to achieve the highest speeds for hybrid networking within AWS. As mentioned, it can be provisioned with 1, 10, or 100 gigabit speeds, and since it’s a dedicated port, you’re very likely to achieve the maximum possible speed.

Compare that to an IPsec VPN, which uses encryption and therefore incurs processing overhead while transiting over the public internet. Direct Connect will give you higher, more consistent speeds. Lastly, Direct Connect can be used to access both AWS private services running in a VPC and AWS public services. However, it cannot be used to access the public internet unless you add a proxy or another networking appliance to handle that for you.

Visually, the architecture of Direct Connect starts on the right with your business premises, where you'll have some kind of customer premises router or firewall. This might be the same router connected to your internet connection or a new, dedicated DX-capable router, which I’ll explain more about in an upcoming lesson. Additionally, you’ll have some staff, in this case, Bob and Julie. In the middle, we have a DX location. This is often confusing, as it’s not a location actually owned by AWS—it’s not an AWS building. It’s usually a large regional data center where AWS rents space, and your business might also rent space alongside other businesses.

Inside this DX location is an AWS cage—an area owned by AWS containing one or more DX routers known as AWS DX routers, which are the endpoints of the Direct Connect service. You might also rent space in this DX location, known as the customer cage. If you’re a large organization, you might rent this space directly, housing some of your infrastructure and a router known as the customer DX router. If you’re a smaller organization, this cage might belong to a communications partner—this is called the comms partner cage. If you don’t have space in a DX location, the communications partner does and can extend connections from this DX location to your business premises.

The key thing to understand about Direct Connect is that it's a port allocation. When you order a Direct Connect from AWS to a specific DX location, you’re allocated a DX port. This must be physically connected using a fiber optic cable to another port in the DX location—either your router in your cage or a communications partner’s router in the same DX location. In either case, you’ll have a corresponding port within the DX location, whether on your own equipment or that of a comms provider. Between these two ports, you’ll need to order a cross connect.

The cross connect is a physical connection between the AWS DX port in the AWS cage and your or your provider’s port within the DX location. This concept is crucial, whether you have equipment in the DX location or purchase access through a communications partner. From the partner, you'll be allocated a port within the DX location, and it is to this port that the cross connect is linked. This is the cable that connects the AWS DX port to your router or a communications partner’s router. If you're using a communications partner, this link can then be extended to your customer premises. But in all cases, you must have a port within either a customer cage or comms partner cage at the DX location to establish a cross connect with AWS’s DX port.

On the left side, we have an AWS region—such as AP Southeast 2—with a VPC containing a private subnet and services. We also have the AWS public zone and example services such as SQS, Elastic IP addresses, and S3. The AWS region is AWS-owned infrastructure, which may or may not be in the same facility as the DX location but is always connected with multiple high-speed resilient network connections. Conceptually, you can think of the region as always being connected to one or more local DX locations.

That’s the physical architecture, and I’ll go into more detail in upcoming lessons elsewhere in the course. Logically, we configure virtual interfaces—called VIFs—over this single physical connection. There are three types of VIFs. First are transit VIFs, which have specific use cases that I’ll explain in detail later. Second are public VIFs, used to access AWS public space services. A public VIF runs over the full Direct Connect path—from your customer router to your DX router, then into the AWS DX router, and finally into the public AWS region. Third are private VIFs, which also run over Direct Connect but connect into virtual private gateways attached to a VPC, giving you access to private AWS services.

That’s everything I wanted to cover in this lesson. Go ahead and complete it, and when you're ready, I look forward to you joining me in the next one.

Welcome back. This is part two of this lesson, and we’re going to continue immediately from the end of part one. So let's get started.

Now, the previous architecture can be evolved by using queues. A queue is a system that accepts messages. Messages are sent onto a queue and can be received or polled off the queue. In many queues, there's ordering, meaning that in most cases, messages are received off the queue in a first-in, first-out (FIFO) architecture, though it's worth noting that this isn't always the case.

Using a queue-based decoupled architecture, CatTube would look something like this: Bob would upload his newest video of whiskers laying on the beach to the upload component. Once the upload is complete, instead of passing this directly onto the processing tier, it does something slightly different. It stores the master 4K video inside an S3 bucket and adds a message to the queue detailing where the video is located, as well as any other relevant information, such as what sizes are required. This message, because it’s the first message in the queue, is architecturally at the front of the queue. At this point, the upload tier, having uploaded the master video to S3 and added a message to the queue, finishes this particular transaction. It doesn’t talk directly to the processing tier and doesn't know or care if it’s actually functioning. The key thing is that the upload tier doesn't expect an immediate answer from the processing tier. The queue has decoupled the upload and processing components.

It's moved from a synchronous style of communication where the upload tier expects and needs an immediate answer and waits for that answer, to asynchronous communications. Here, the upload tier sends the message and can either wait in the background or just continue doing other things while the processing tier does its job. While this process is going on, the upload component is probably getting additional videos being uploaded, and they’re added to the queue along with the whiskers video processing job. Other messages that are added to the queue are behind the whiskers job because there is an order in this queue: it is a FIFO queue.

At the other side of the queue, we have an auto-scaling group, which has been configured with a minimum size of 0, a desired size of 0, and a maximum size of 1,337. Currently, it has no instances provisioned, but it has auto-scaling policies that provision or terminate instances based on what's called the queue length, which is the number of items in the queue. Because there are messages on the queue added by the upload tier, the auto-scaling group detects this and increases the desired capacity from 0 to 2. As a result, instances are provisioned by the auto-scaling group. These instances start polling the queue and receive messages that are at the front of the queue. These messages contain the data for the job and the location of the S3 bucket and the object in that bucket. Once these jobs are received from the queue by these processing instances, they can retrieve the master video from the S3 bucket.

The jobs are processed by the instances, and once they are completed, the messages are deleted from the queue, leaving only one job in the queue. At this point, the auto-scaling group may decide to scale back because of the shorter queue length, so it reduces the desired capacity from 2 to 1, which terminates one of the processing instances. The instance that remains polls the queue and receives the last message. It completes the processing of that message, performs the transcoding on the videos, and leaves zero messages in the queue. The auto-scaling group realizes this and scales back the desired capacity from 1 to 0, resulting in the termination of the last processing EC2 instance.

Using a queue architecture to place a queue between two application tiers decouples those tiers. One tier adds jobs to the queue and doesn’t care about the health or the state of the other tier. The other tier can read jobs from the queue, and it doesn't care how they got there. This is unlike the previous example where application load balancers were used between tiers. While this did allow for high availability and scaling, the upload tier in the previous example still synchronously communicated with one instance of the processing tier. With the queue architecture, no communication happens directly between the components. The components are decoupled and can scale independently and freely. In this case, the processing tier uses a worker fleet architecture that can scale anywhere from zero to a near-infinite number of instances based on the length of the queue.

This is a really powerful architecture because of the asynchronous communications it uses. It's an architecture commonly used in applications like CatTube, where customers upload things for processing, and you want to ensure that a worker fleet behind the scenes can scale to perform that processing. You might be asking why this matters in the context of event-driven architectures, and I’m getting there, I promise.

If you continue breaking down a monolithic application into smaller and smaller pieces, you'll eventually end up with a microservice architecture, which is a collection of, as the name suggests, microservices. Microservices do individual things very well. In this example, we have the upload microservice, the processing microservice, and the store and manage microservice. A full application like CatTube might have hundreds or even thousands of these microservices. They might be different services, or there might just be many copies of the same service, like in this example, which is fortunate because it's much easier to diagram. The upload service is a producer, the processing node is a consumer, and the data store and manage microservice performs both roles.

Logically, producers produce data or messages, and consumers, as the name suggests, consume data or messages. There are also microservices that can do both things. The things that services produce and consume architecturally are events. Queues can be used to communicate events, as we saw with the previous example, but larger microservices architectures can get complex quickly. Services need to exchange data between partner microservices, and if we do this with a queue architecture, we'll logically have many queues. While this works, it can be complicated. Keep in mind that a microservice is just a tiny self-sufficient application. It has its own logic, its own store of data, and its own input/output components.

Now, if you hear the term "event-driven architecture," I don’t want you to be too apprehensive. Event-driven architectures are simply a collection of event producers, which might be components of your application that directly interact with customers, parts of your infrastructure like EC2, or systems monitoring components. These are bits of software that generate or produce events in reaction to something. If a customer clicks submit, that might be an event. If an error occurs during the upload of the whiskers holiday video, that's an event. Producers are things that produce events, and the inverse of this is consumers—pieces of software that are ready and waiting for events to occur. When they see an event they care about, they take action. This might involve displaying something for a customer, dispatching a human to resolve an order packing issue, or retrying an upload.

Components or services within an application can be both producers and consumers. Sometimes a component might generate an event, for example, a failed upload, and then consume events to force a retry of that upload. The key thing to understand about event-driven architectures is that neither the producers nor the consumers are sitting around waiting for things to occur. They're not constantly consuming resources or running at 100% CPU load, waiting for things to happen. Producers generate events when something occurs, such as when a button is clicked, an upload works, or when it doesn’t work. These producers produce events, but consumers aren’t waiting around for those events. They have those events delivered, and when they receive an event, they take an action, then stop. They're not constantly consuming resources.

Applications would be really complex if every software component or service needed to be aware of every other component. If every application component required a queue between it and every other component to put events into and access them from, the architecture would be really complicated. Best practice event-driven architectures have what's called an event router, a highly available central exchange point for events. The event router has an event bus, which you can think of as a constant flow of information. When events are generated by producers, they're added to this event bus, and the router can deliver them to event consumers.

The WordPress system we’ve used so far has been running on an EC2 instance, which is essentially a consistent allocation of resources. Whether the WordPress system is under low load or large load, we’re still billed for that EC2 instance, consuming resources. Now, imagine a system with lots of small services all waiting for events. If events are received, the system springs into action, allocating resources and scaling components as needed. It deals with those events, then returns to a low or no resource usage state, which is the default. Event-driven architectures only consume resources when needed. There’s nothing constantly running or waiting for things to happen. We don’t constantly poll, hoping for something to happen. We have producers that generate events when something happens. For example, on Amazon.com, when you click "order," it generates an event, and actions are taken based on that event. But Amazon.com doesn’t constantly check your browser every second to see if you've clicked "submit."

So, in summary, a mature event-driven architecture only consumes resources while handling events. When events are not occurring, it doesn’t consume resources. This is one of the key components of a serverless architecture, which I’ll talk about more later in this section.

I know this has been a lot of theory, but I promise you, as you continue through the course, it will really make sense why I introduced this theory in detail at this point. It will help you with the exam, too. In the rest of this section, we’ll be covering more AWS-specific and practical topics, but they’ll all rely on your knowledge of this evolution of systems architecture.

Thanks for watching this video. You can go ahead and finish it off, and when you’re ready, I look forward to you joining me in the next lesson.

Author response:

The following is the authors’ response to the original reviews

eLife Assessment

The authors present an algorithm and workflow for the inference of developmental trajectories from single-cell data, including a mathematical approach to increase computational efficiency. While such efforts are in principle useful, the absence of benchmarking against synthetic data and a wide range of different single-cell data sets make this study incomplete. Based on what is presented, one can neither ultimately judge if this will be an advance over previous work nor whether the approach will be of general applicability.

We thank the eLife editor for the valuable feedback. Both benchmarking against other methods and validation on a synthetic dataset (“dyntoy”) are indeed presented in the Supplementary Note, although this was not sufficiently highlighted in the main text, which has now been improved.

Our manuscript contains benchmarking against a challenging synthetic dataset in Figure 1; furthermore, both the synthetic dataset and the real-world thymus dataset have been analyzed in parallel using currently available TI tools (as detailed in the Supplementary Note). z other single-cell datasets (single-cell RNA-seq) were added in response to the reviewers' comments.

One of the reviewers correctly points out that tviblindi goes against the philosophy of automated trajectory inference. This is correct; we believe that a new class of methods, complementary to fully automated approaches, is needed to explore datasets with unknown biology. tviblindi is meant to be a representative of this class of methods—a semi-automated framework that builds on features inferred from the data in an unbiased and mathematically well-founded fashion (pseudotime, homology classes, suitable low-dimensional representation), which can be used in concert with expert knowledge to generate hypotheses about the underlying dynamics at an appropriate level of detail for the particular trajectory or biological process.

We would also like to mention that the algorithm and the workflow are not the sole results of the paper. We have thoroughly characterized human thymocyte development, where, in addition to expected biological endpoints, we found and characterized an unexpected activated thymic T-reg endpoint.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors present tviblindi, a computational workflow for trajectory inference from molecular data at single-cell resolution. The method is based on (i) pseudo-time inference via expecting hitting time, (ii) sampling of random walks in a directed acyclic k-NN where edges are oriented away from a cell of origin w.r.t. the involved nodes' expected hitting times, and (iii) clustering of the random walks via persistent homology. An extended use case on mass cytometry data shows that tviblindi can be used elucidate the biology of T cell development.

Strengths:

- Overall, the paper is very well written and most (but not all, see below) steps of the tviblindi algorithm are explained well.

- The T cell biology use case is convincing (at least to me: I'm not an immunologist, only a bioinformatician with a strong interest in immunology).

We thank the reviewer for feedback and suggestions that we will accommodate, we respond point-by-point below

Weaknesses:

- The main weakness of the paper is that a systematic comparison of tviblindi against other tools for trajectory inference (there are many) is entirely missing. Even though I really like the algorithmic approach underlying tviblindi, I would therefore not recommend to our wet-lab collaborators that they should use tviblindi to analyze their data. The only validation in the manuscript is the T cell development use case. Although this use case is convincing, it does not suffice for showing that the algorithms's results are systematically trustworthy and more meaningful (at least in some dimension) than trajectories inferred with one of the many existing methods.

We have compared tviblindi to several trajectory inference methods (Supplementary note section 8.2: Comparison to state-of-the-art methods, namely Monocle3 (v1.3.1) Cao et al. (2019), Stream (v1.1) Chen et al. (2019), Palantir (v1.0.0) Setty et al. (2019), VIA (v0.1.89) Stassen et al. (2021), StaVia (Via 2.0) Stassen et al. (2024), CellRank 2 (v2.06) Weiler et al. (2024)  and PAGA (scanpy==1.9.3) Wolf et al. (2019). We added thorough and systematic comparisons to the other algorithms mentioned by reviewers. We included extended evaluation on publicly available datasets (Supplementary Note section 10).

Also, in the meantime we have successfully used tviblindi to investigate human B-cell development in primary immunodeficiency (Bakardjieva M, et al. Tviblindi algorithm identifies branching developmental trajectories of human B-cell development and describes abnormalities in RAG-1 and WAS patients. Eur J Immunol. 2024 Dec;54(12):e2451004. doi: 10.1002/eji.202451004.).

- The authors' explanation of the random walk clustering via persistent homology in the Results (subsection "Real-time topological interactive clustering") is not detailed enough, essentially only concept dropping. What does "sparse regions" mean here and what does it mean that "persistent homology" is used? The authors should try to better describe this step such that the reader has a chance to get an intuition how the random walk clustering actually works. This is especially important because the selection of sparse regions is done interactively. Therefore, it's crucial that the users understand how this selection affects the results. For this, the authors must manage to provide a better intuition of the maths behind clustering of random walks via persistent homology.

In order to satisfy both reader types: the biologist and the mathematician, we explain the mathematics in detail in the Supplementary Note, section 4. We improved the Results text to better point the reader to the mathematical foundations in the Supplementary Note.  

- To motivate their work, the authors write in the introduction that "TI methods often use multiple steps of dimensionality reduction and/or clustering, inadvertently introducing bias. The choice of hyperparameters also fixes the a priori resolution in a way that is difficult to predict." They claim that tviblindi is better than the original methods because "analysis is performed in the original high-dimensional space, avoiding artifacts of dimensionality reduction." However, in the manuscript, tviblindi is tested only on mass cytometry data which has a much lower dimensionality than scRNA-seq data for which most existing trajectory inference methods are designed. Since tviblindi works on a k-NN graph representation of the input data, it is unclear if it could be run on scRNA-seq data without prior dimensionality reduction. For this, cell-cell distances would have to be computed in the original high-dimensional space, which is problematic due to the very high dimensionality of scRNA-seq data. Of course, the authors could explicitly reduce the scope of tviblindi to data of lower dimensionality, but this would have to be stated explicitly.

In the manuscript we tested the framework on the scRNA-seq data from Park et al 2020 (DOI: 10.1126/science.aay3224). To illustrate that tviblindi can work directly in the high-dimensional space, we applied the framework successfully on imputed 2000 dimensional data. Furthermore we successfully used tviblindi to investigate bone marrow atlas scRNA-Seq dataset Zhang et al. (2024) and atlas of mouse gastrulation Pijuan-Sala et al. (2019). The idea behind tviblindi is to be able to work without the necessity to use non-linear dimensionality reduction techniques, which reduce the dimensionality to a very low number of dimensions and whose effects on the data distribution are difficult to predict. On the other hand the use of (linear) dimensionality reduction techniques which effectively suppress noise in the data such as PCA is a good practice (see also response to reviewer 2). We have emphasized this in the revised version and added the results of the corresponding analysis (see Supplementary note, section 9).

- Also tviblindi has at least one hyper-parameter, the number k used to construct the k-NN graphs (there are probably more hidden in the algorithm's subroutines). I did not find a systematic evaluation of the effect of this hyper-parameter.

Detailed discussion of the topic is presented in the Supplementary Note, section 8.1, where Spearman correlation coefficient between pseudotime estimated using k=10 and k=50 nearest neighbors was 0.997.   The number k however does affect the number of candidate endpoints. But even when larger k causes spurious connection between unrelated cell fates, the topological clustering of random walks allows for the separation of different trajectories. We have expanded the “sensitivity to hyperparameters” section 8.1 also in response to reviewer 2.

Reviewer #2 (Public Review):

Summary:

In Deconstructing Complexity: A Computational Topology Approach to Trajectory Inference in the Human Thymus with tviblindi, Stuchly et al. propose a new trajectory inference algorithm called tviblindi and a visualization algorithm called vaevictis for single-cell data. The paper utilizes novel and exciting ideas from computational topology coupled with random walk simulations to align single cells onto a continuum. The authors validate the utility of their approach largely using simulated data and establish known protein expression dynamics along CD4/CD8 T cell development in thymus using mass cytometry data. The authors also apply their method to track Treg development in single-cell RNA-sequencing data of human thymus.

The technical crux of the method is as follows: The authors provide an interactive tool to align single cells along a continuum axis. The method uses expected hitting time (given a user input start cell) to obtain a pseudotime alignment of cells. The pseudotime gives an orientation/direction for each cell, which is then used to simulate random walks. The random walks are then arranged/clustered based on the sparse region in the data they navigate using persistent homology.

We thank the reviewer for feedback and suggestions that we have accommodated, we responded point-by-point below.

Strengths:

The notion of using persistent homology to group random walks to identify trajectories in the data is novel.

The strength of the method lies in the implementation details that make computationally demanding ideas such as persistent homology more tractable for large scale single-cell data. This enables the authors to make the method more user friendly and interactive allowing real-time user query with the data.

Weaknesses:

The interactive nature of the tool is also a weakness, by allowing for user bias leading to possible overfitting for a specific data.

tviblindi is not designed as a fully automated TI tool (although it implements a fully automated module), but as a data driven framework for exploratory analysis of unknown data. There is always a risk of possible bias in this type of analysis - starting with experimental design, choice of hyperparameters in the downstream analysis, and an expert interpretation of the results. The successful analysis of new biological data involves a great deal of expert knowledge which is difficult to a priori include in the computational models. 

tvilblindi tries to solve this challenge by intentionally overfitting the data and keeping the level of resolution on a single random walk. In this way we aim to capture all putative local relationships in the data. The on-demand aggregation of the walks using the global topology of the data allows researchers to use their expert knowledge to choose the right level of detail (as demonstrated in the Figure 4 of the manuscript) while relying on the topological structure of the high dimensional point cloud. At all times tviblindi allows to inspect the composition of the trajectory to assess the variance in the development, possible hubs on the KNN-graph etc.

The main weakness of the method is lack of benchmarking the method on real data and comparison to other methods. Trajectory inference is a very crowded field with many highly successful and widely used algorithms, the two most relevant ones (closest to this manuscript) are not only not benchmarked against, but also not sited. Including those that specifically use persistent homology to discover trajectories (Rizvi et.al. published Nat Biotech 2017). Including those that specifically implement the idea of simulating random walks to identify stable states in single-cell data (e.g. CellRank published in Lange et.al Nat Meth 2022), as well as many trajectory algorithms that take alternative approaches. The paper has much less benchmarking, demonstration on real data and comparison to the very many other previous trajectory algorithms published before it. Generally speaking, in a crowded field of previously published trajectory methods, I do not think this one approach will compete well against prior work (especially due to its inability to handle the noise typical in real world data (as was even demonstrated in the little bit of application to real world data provided).

We provided comparisons of tviblindi and vaevictis in the Supplementary Note, section 8.2, where we compare it to Monocle3 (v1.3.1) Cao et al. (2019), Stream (v1.1) Chen et al. (2019), Palantir (v1.0.0) Setty et al. (2019), VIA (v0.1.89) Stassen et al. (2021),  StaVia (Via 2.0) Stassen et al. (2024), CellRank 2 (v2.06) Weiler et al. (2024)  and PAGA (scanpy==1.9.3) Wolf et al. (2019). We added thorough and systematic comparisons to the other algorithms mentioned by reviewers. We included extended evaluation on publicly available datasets (Supplementary Note section 10).

Beyond general lack of benchmarking there are two issues that give me particular concern. As previously mentioned, the algorithm is highly susceptible to user bias and overfitting. The paper gives the example (Figure 4) of a trajectory which mistakenly shows that cells may pass from an apoptotic phase to a different developmental stage. To circumvent this mistake, the authors propose the interactive version of tviblindi that allows users to zoom in (increase resolution) and identify that there are in fact two trajectories in one. In this case, the authors show how the author can fix a mistake when the answer is known. However, the point of trajectory inference is to discover the unknown. With so much interactive options for the user to guide the result, the method is more user/bias driven than data-driven. So a rigorous and quantitative discussion of robustness of the method, as well as how to ensure data-driven inference and avoid over-fitting would be useful.

Local directionality in expression data is a challenge which is not, to our knowledge, solved. And we are not sure it can be solved entirely, even theoretically. The random walks passing “through” the apoptotic phase are biologically infeasible, but it is an (unbiased) representation of what the data look like based on the diffusion model. It is a property of the data (or of the panel design), which has to be interpreted properly rather than a mistake. Of note, except for Monocle3 (which does not provide the directionality) other tested methods did not discover this trajectory at all.

The “zoom in” has in fact nothing to do with “passing through the apoptosis”. We show how the researcher can investigate the suggested trajectory to see if there is an additional structure of interest and/or relevance. This investigation is still data driven (although not fully automated). Anecdotally in this particular case this branching was discovered by a bioinformatician, who knew nothing about the presence of beta-selection in the data.  

We show that the trajectory of apoptosis of cortical thymocytes consists of 2 trajectories corresponding to 2 different checkpoints (beta-selection and positive/negative selection). This type of a structure, where 2 (or more) trajectories share the same path for most of the time, then diverge only to be connected at a later moment (immediately from the point of view of the beta-selection failure trajectory) is a challenge for TI algorithms and none of tested methods gave a correct result. More importantly there seems to be no clear way to focus on these kinds of structures (common origin and common fate) in TI methods.

Of note, the “zoom in” is a recommended and convenient method to look for an inner structure, but it does not necessarily mean addition of further homological classes. Indeed, in this case the reason that the structure is not visible directly is the limitation of the dendrogram complexity (only branches containing at least 10% of simulated random walks are shown by default). In summary, tviblindi effectively handled all noise in the data that obscured biologically valid trajectories for other methods. We have improved the discussion of the robustness in the current version.  

Second, the paper discusses the benefit of tviblindi operating in the original high dimensions of the data. This is perhaps adequate for mass cytometry data where there is less of an issue of dropouts and the proteins may be chosen to be large independent. But in the context of single-cell RNA-sequencing data, the massive undersampling of mRNA, as well as high degree of noise (e.g. ambient RNA), introduces very large degree of noise so that modeling data in the original high dimensions leads to methods being fit to the noise. Therefore ALL other methods for trajectory inference work in a lower dimension, for very good reason, otherwise one is learning noise rather than signal. It would be great to have a discussion on the feasibility of the method as is for such noisy data and provide users with guidance. We note that the example scRNA-seq data included in the paper is denoised using imputation, which will likely result in the trajectory inference being oversmoothed as well.

We agree with the reviewer. In our manuscript we wanted to showcase that tviblindi can directly operate in high-dimensional space (thousands of dimensions) and we used MAGIC imputation for this purpose. This was not ideal. More standard approach, which uses 30-50 PCs as input to the algorithm resulted in equivalent trajectories. We have added this analysis to the study (Supplementary note, section 9).

In summary, the fact that tviblindi scales well with dimensionality of the data and is able to work in the original space does not mean that it is always the best option. We have added a corresponding comment into the Supplementary note.  

Reviewer #3 (Public Review):

Summary:

Stuchly et al. proposed a single-cell trajectory inference tool, tviblindi, which was built on a sequential implementation of the k-nearest neighbor graph, random walk, persistent homology and clustering, and interactive visualization. The paper was organized around the detailed illustration of the usage and interpretation of results through the human thymus system.

Strengths:

Overall, I found the paper and method to be practical and needed in the field. Especially the in-depth, step-by-step demonstration of the application of tviblindi in numerous T cell development trajectories and how to interpret and validate the findings can be a template for many basic science and disease-related studies. The videos are also very helpful in showcasing how the tool works.

Weaknesses:

I only have a few minor suggestions that hopefully can make the paper easier to follow and the advantage of the method to be more convincing.

(1) The "Computational method for the TI and interrogation - tviblindi" subsection under the Results is a little hard to follow without having a thorough understanding of the tviblindi algorithm procedures. I would suggest that the authors discuss the uniqueness and advantages of the tool after the detailed introduction of the method (moving it after the "Connectome - a fully automated pipeline".

We thank the reviewer for the suggestion and we have accommodated it to improve readability of the text.

Also, considering it is a computational tool paper, inevitably, readers are curious about how it functions compared to other popular trajectory inference approaches. I did not find any formal discussion until almost the end of the supplementary note (even that is not cited anywhere in the main text). Authors may consider improving the summary of the advantages of tviblindi by incorporating concrete quantitative comparisons with other trajectory tools.

We provided comparisons of tviblindi and vaevictis in the Supplementary Note, section 8.2, where we compare it to Monocle3 (v1.3.1) Cao et al. (2019), Stream (v1.1) Chen et al. (2019), Palantir (v1.0.0) Setty et al. (2019), VIA (v0.1.89) Stassen et al. (2021),  StaVia (Via 2.0) Stassen et al. (2024), CellRank 2 (v2.06) Weiler et al. (2024)  and PAGA (scanpy==1.9.3) Wolf et al. (2019). We added thorough and systematic comparisons to the other algorithms mentioned by reviewers. We included extended evaluation on publicly available datasets (Supplementary Note section 10).

(2) Regarding the discussion in Figure 4 the trajectory goes through the apoptotic stage and reconnects back to the canonical trajectory with counterintuitive directionality, it can be a checkpoint as authors interpret using their expert knowledge, or maybe a false discovery of the tool. Maybe authors can consider running other algorithms on those cells and see which tracks they identify and if the directionality matches with the tviblindi.

We have indeed used the thymus dataset for comparison of all TI algorithms listed above. Except for Monocle 3 they failed to discover the negative selection branch (Monocle 3 does not offer directionality information). Therefore, a valid topological trajectory with incorrect (expert-corrected) directionality was partly or entirely missed by other algorithms. 

(3) The paper mainly focused on mass cytometry data and had a brief discussion on scRNA-seq. Can the tool be applied to multimodality data such as CITE-seq data that have both protein markers and gene expression? Any suggestions if users want to adapt to scATAC-seq or other epigenomic data?

The analysis of multimodal data is the logical next step and is the topic of our current research. At this moment tviblindi cannot be applied directly to multimodal data. It is possible to use the KNN-graph based on multimodal data (such as weighted nearest neighbor graph implemented in Seurat) for pseudotime calculation and random walk simulation. However, we do not have a fully developed triangulation for the multimodal case yet. 

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Suggestions for improved or additional experiments, data or analyses:

-  Benchmark against existing trajectory inference methods.

-  Benchmark on scRNA-seq data or an explicit statement that, unlike existing methods, tviblindi is not designed for such data.

We provided comparisons of tviblindi and vaevictis in the Supplementary Note, section 8.2, where we compare it to Monocle3 (v1.3.1) Cao et al. (2019), Stream (v1.1) Chen et al. (2019), Palantir (v1.0.0) Setty et al. (2019), VIA (v0.1.89) Stassen et al. (2021),  StaVia (Via 2.0) Stassen et al. (2024), CellRank 2 (v2.06) Weiler et al. (2024)  and PAGA (scanpy==1.9.3) Wolf et al. (2019). We added thorough and systematic comparisons to the other algorithms mentioned by reviewers. We included extended evaluation on publicly available datasets (Supplementary Note section 10).

-  Systematic evaluation of the effetcs of hyper-parameters on the performance of tviblindi (as mentioned above, there is at least one hyper-parameter, the number k to construct the k-NN graphs).

This is described in Supplementary Note section 8.1

Recommendations for improving the writing and presentation:

-  The GitHub link to the algorithm which is currently hidden in the Methods should be moved to the abstract and/or a dedicated section on code availability.

-  The presentation of the persistent homology approach used for random walk clustering should be improved (see public comment above).

This is described extensively in Supplementary Note  

-  A very minor point (can be ignored by the authors): consider renaming the algorithm. At least for me, it's extremely difficult to remember.

We choose to keep the original name

Minor corrections to the text and figures:

-  Labels and legend texts are too small in almost all figures.

Reviewer #2 (Recommendations For The Authors):  

(1) On page 3: "(2) Analysis is performed in the original high-dimensional space avoiding artifacts of dimensionality reduction." In mass cytometry data where there is no issue of dropouts, one may choose proteins such that they are not correlated with each other making dimensionality reduction techniques less relevant. But in the context of an unbiased assays such as single-cell RNA-sequencing (scRNA-seq), one measures all the genes in a cell so dimensionality reduction can help resolve the redundancy in the feature space due to correlated/co-regulated gene expression patterns. This assumption forms the basis of most methods in scRNA-seq. More importantly, in scRNA-seq data the dropouts and ambient molecules in mRNA counts result in so much noise that modeling cells in the full gene expression is highly problematic. So the authors are requested to discuss in detail how they would propose to deal with noise in scRNA-seq data.

On this note, the authors mention in Supplementary Note 9 (Analysis of human thymus single-cell RNA-seq data): "Imputed data are used as the input for the trajectory inference, scaled counts (no imputation) are shown in line plots". The line plots indicate the gene expression trends along the obtained pseudotime. The authors use MAGIC to impute the data, and we request the authors to mention this in the Methods section (currently one must look through the code on Supplementary Note 1.3 to find this). Data imputation in single-cell RNA-seq data are intended to enable quantification of individual gene expression distribution or pairwise gene associations. But when all the genes in an imputed data are used for visualization, clustering or trajectory inference, the averaging effect will compound and result in severely smoothed data that misses important differences between cell states. Especially, in the case of MAGIC, which uses a transition matrix raised to a power, it is over-smoothing of the data to use a transition matrix smoothed data to obtain another transition matrix to calculate the hitting time (or simulate random walks). Second, the authors' proposal to use scaled counts to study gene trends cannot be generalized to other settings due to drop out issue. Given the few genes (and only one branch) that are highlighted in Figure 7D-G and Figure 31 in Supplementary Note, it is hard to say if scaling raw values would pick up meaningful biology robustly here for other branches.

We recommend that this data be reanalyzed with non-imputed data used for trajectory inference and imputed gene expression used for line plots.

As stated above in the public review, we reanalyzed the scRNA Seq data using a more standard approach (first 50 principal components). We have also analyzed two additional scRNA Seq datasets (Section 1 and section 10 of Supplementary Note)

On the same note, the authors use Seurat's CellCycleScoring to obtain the cell cycle phase of each cell and later use ScaleData to regress them out. While we agree that it is valuable to remove cell cycle effect from the data for trajectory inference (and has been used previously in other methods), the regression approach employed in Seurat's ScaleData is not appropriate. It is an aggressive approach that severely changes expression pattern of many genes and can result in new artifacts (false positives) in the data. We recommend the authors to explore this more and consider using a more principled alternatives such as fscLVM (https://genomebiology.biomedcentral.com/articles/10.1186/s13059-017-1334-8). 

Cell cycle correction is an open problem (Heumos, Nat Rev Genetics, 2023)

Here we use an (arguably aggressive) approach to make the presentation more straightforward. The cells we are interested here (end #6) are not dividing and the regression does not change the conclusion drawn in the paper

(2) The figures provided are extremely low in resolution that it is practically impossible to correctly interpret a lot of the conclusion and references made in the figure (especially Figure 3 in the main text).

Resolution of the Figures was improved

(3) There are many aspects of the method that enable easy user biases and can lead to substantial overfitting of the data.

a. On page 7: "The topology of the point cloud representing human T-cell development is more complex ... and does not offer a clear cutoff for the choice of significant sparse regions. Interactive selection allows the user to vary the resolution and to investigate specific sparse regions in the data iteratively." This implies that the method enables user biases to be introduced into the data analysis. While perhaps useful for exploration, quantitative trajectory assessment using such approach can be faulty when the user (A) may not know the underlying dynamics (B) forces preconceived notion of trajectory.

The authors should consider making the trajectory inference approach less dependent on interactive user input and show that the trajectory results are robust to any choices the user may make. It may also help if the authors provide an effective guide and mention clearly what issues could result due to the use of such thresholds.

As explained in the response in public reviews, tviblindi is not designed as a fully automated TI tool, but as a data driven framework for exploratory analysis of unknown data. 

There is always a risk of possible bias in this type of analysis - starting with experimental design, choice of hyperparameters in the downstream analysis, and an expert interpretation of the results. The successful analysis of new biological data involves a great deal of expert knowledge which is difficult to a priori include in the computational models.  To specifically address the points raised by the reviewer:

“(A) may not know the underlying dynamics” - tviblindi is designed to perform exploratory analysis of the unknown underlying dynamics. We showcase in the study how this can be performed and we highlight possible cases which can be resolved expertly (spurious connections (doublets), different scales of resolution (beta selection)). Crucially, compared to other TI methods, tviblindi offers a clear mechanism on how to discover, focus and resolve these issues which would (and do) contaminate the trajectories discovered fully automatically by tested methods (cf. the beta selection, or the development of plasmacytoid dendritic cells (PDCs) (Supplementary note, section 10.1).

“(B) forces preconceived notion of trajectory” - user interaction in tviblindi does not force a preconceived notion of the trajectory. The random walks are simulated before the interactive step in an unbiased manner. During the interactive step the user adjusts trajectory specific resolution - incorrect choice of the resolution may result in either merging distinct trajectories into one or over separating the trajectories (which is arguably much less serious). However the interactive step is designed to deal with exactly this kind of challenge. We showcase (e.g. beta selection, or PDCs development) how to address the issue - tviblindi allows us to investigate deeper structure in any considered trajectory.

Thus, tviblindi represents a new class of methods that is complementary to fully automated trajectory inference tools. It offers a semi-automated tool that leverages features derived from data in an unbiased and mathematically rigorous manner, including pseudotime, homology classes, and appropriate low-dimensional representations. These can be integrated with expert knowledge to formulate hypotheses regarding the underlying dynamics, tailored to the specific trajectory or biological process under investigation.

b. In Figure 4, the authors discuss the trajectory of cells emanating from CD3 negative double positive stage and entering apoptotic phase and mention tviblindi may give "the false impression that cells may pass through an apoptotic phase into a later developmental stage" and propose that the interactive version of tviblindi can help user zoom into (increase resolution) this phenomenon and identify that there are in fact two trajectories in one. Given this, how do the other trajectories in the data change if a user manually adjusts the resolution? A quantification of the robustness is important. Also, it appears that a more careful data clean up could avoid such pitfalls where the algorithm infers trajectory based on mixed phenotype and the user would not have to manually adjust the resolution to obtain clear biological conclusion. We not that the original publication of this data did such "data clean up" using simple diffusion map based dimensionality reduction which the authors boast they avoid. There is a reason for this dimensionality reduction (distinguishing signal from noise), even in CyTOF data, let alone its importance in single cell data.

The reviewer is concerned about two different, but intertwined issues we wish to untangle here. First, data clean-up is typically done on the premise that dead cells are irrelevant and they are a source of false signals. In the case of the thymocytes in the human thymus this premise is not true. Apoptotic cells are a legitimate (actually dominant) fate of the development and thus need to be represented in the TI dataset. Their biological behavior is however complex as they stop expressing proteins and thus lose their surface markers gradually, as dictated by the particular protein degradation kinetics. So can we clean up dead and dying cells better? Yes, but we don't want to do it since we would lose cells we want to analyze. Second, do trajectories change when we zoom into the data? No, only the level of detail presented visually changes. Since we calculate 5000 trajectories in the dataset, we need to aggregate them already for the hierarchical clustering visualization. Note that Figure 4, panel A highlights 159 trajectories selected in V. group. Zooming in means that the hierarchy of trajectories within V. group is revealed (panel D, groups V.a and Vb.) and can be interpreted on the vaevictis and lineplot graphs (panel E, F). 

c. In the discussion, the authors write "[tviblindi] allows the selection and grouping of similar random walks into trajectories based on visual interaction with the data". This counters the idea of automated trajectory inference and can lead to severe overfitting.

As explained in reply to Q3, our aim was NOT to create a fully automated trajectory inference tool. Even more, in our experience we realized that all current tools are taking this fully  automated approach with a search for an “ideal” set of hyperparameters. This, in our experience,  leads to a “blackbox” tool that is difficult to interpret for the expert in the biological field. To respond to this need we designed a modular approach where the results of the TI are presented and the expert can interact with them to focus the visualization and to derive interpretation. Our interactive concept is based on 15 years of experience with the data analysis in flow cytometry, where neither manual gating nor full automation is the ultimate solution but smart integration of both approaches eventually wins the game.

Thus, tviblindi represents a new class of methods that is complementary to fully automated trajectory inference tools.  It offers a semi-automated tool that leverages features derived from data in an unbiased and mathematically rigorous manner. These features include pseudotime, homology classes, and appropriate low-dimensional representations. These features can be integrated with expert knowledge to formulate hypotheses regarding the underlying dynamics, tailored to the specific trajectory or biological process under investigation.

d. The authors provide some comment on the robustness to the relaxation parameter for witness complex construction in Supplementary Note Section 8.1.2 but it is limited given the importance of this parameter and a more thorough investigation is recommended. We request the authors to provide concrete examples with figures of how changing alpha2 parameter leads to simplicial complexes of different sizes and an assessment of contexts in which the parameter is robust and when not (in both simulated and publicly available real data). Of note, giving the users a proper guide for parameter choice based on these examples and offering them ways to quantify robustness of their results may also be valuable.

Section 8 in Supplementary Note was extended as requested.

e. The authors are requested for an assessment of possible short-circuits (e.g. cells of two distantly related phenotypes that get connected erroneously in the trajectory) in the data, and how their approach based on persistent homology deals with it.

If a short circuit results in a (spurious) alternative trajectory, the persistent homology approach allows us to distinguish it from genuine trajectories that do not follow the short circuit. This prevents contamination of the inferred evolution by erroneous connections. The ability to distinguish and separate distinct trajectories with the same fate is a major strength of this approach (e.g., the trajectory through doublets or the trajectories around checkpoints in thymocytes’ evolution).

(4) The authors propose vaevictis as a new visualization tool and show its performance compared to the standard UMAP algorithm on a simulated data set (Figure 1 in Supplementary Notes). We recommend a more comprehensive comparison between the two algorithms on a wide array of publicly available single-cell datasets. As well as comparison to other popular dimensionality reduction approaches like force directed layouts, which are the most widely used tool specifically to visualize trajectories.

We added Section 10 to Supplementary Note that presents multiple comparisons of this kind. It is important to note that tviblindi works independently of visualization and any preferred visualization can be used in the interactive phase (multiple visualisation methods are implemented).

(5) In Supplementary Note 8.2, the authors compare tviblindi against the other methods. We recommend the authors to quantify the comparison or expand on their assesments in real biological data. For example, in comparison against Palantir and VIA the authors mention "... discovers candidate endpoints in the biological dataset but lacks toolbox to interrogate subtle features such as complex branching" and "fails to discover subtle features (such as Beta selection)" respectively. We recommend the authors to make these comparisons more precise or provide quantification. While the added benefit of interactive sessions of tviblindi may make it more user friendly, the way tviblindi appears to enable analysis of subtle features (e.g. Figure 1H) should be possible in Palantir or VIA as well.

We extended the comparisons and presented them in Section 8 and 10 in Supplementary Note.  

(6) The notion of using random walk simulations to identify terminal (and initial states) has been previously used in single-cell data (CellRank algorithm: https://www.nature.com/articles/s41592-021-01346-6). We request the authors to compare their approach to CellRank.

We compared our algorithm to the CellRank successor CellRank 2 (see section 8.2, Supplementary Note)

(7) The notion of using persistent homology to discover trajectories has been previously used in single cell data https://pubmed.ncbi.nlm.nih.gov/28459448/. we request a comparison to this approach

The proposed algorithm was not able to accommodate the large datasets we used.

scTDA (Rizvi, Camara et al. Nat. Biotechnol. 2017) has not been updated for 6 years. It is not suited for complex atlas-sized datasets both in terms of performance and utility, with its limited visualization tools. It also lacks capabilities to analyze individual trajectories.

(8) In Figure 3B, the authors visualize the endpoints and simulated random walks using the connectome. There is no edge from start to the apoptotic cells here. It is not clear why? If they are not relevant based on random walks, can the user remove them from analysis? Same for the small group of pink cells below initial point.

The connectome is a fully automated approach (similar to PAGA) which gives a basic overview of the data. It is not expected to be able to compete with the interactive pipeline of tviblindi for the same reasons as the fully automated methods (difficult to predict the effect of hyperparameters).

(9) In Supplementary Figure 3, in relation to "Variants of trajectories including selection processes" the author mention that there is a spurious connection between CD4 single positive, and the doublet set of cells. The authors mention that the presence of dividing cells makes it difficult to remove the doublets. We request the authors to discuss why. For example, the authors seem to have cell cycle markers (e.g. Ki67, pH3, Cyclin) and one would think that coupled with DNA intercalator 191/193lr one could further clean-up the data. Can the authors employ alternative toolkits such as doublet detection methods?

To address this issue, we do remove doublets with illegitimate cell barcodes (e.g. we remove any two cells from two samples with different barcode which present with double barcode). Although there are computational doublet removal approaches for mass cytometry (Bagwell, Cytometry A 2020), mostly applied to peripheral blood samples (where cell division is not present under steady state immune system conditions), these are however not well suited for situations where dividing samples occur (Rybakowska P, Comput Struct Biotechnol J. 2021), which is the case of our thymocyte samples. Furthermore, there are other situations where doublet formation is not an accident, but rather a biological response (Burel JG, Cytometry A (2020). Thus, the doublet cell problem is similar to the apoptotic cell problem discussed earlier.

We could remove cells with the double DNA signal, but this would remove not only accidental doublets but also the legitimate (dividing) cells. So the question is how to remove the illegitimate doublets but not the legitimate?

Of note, the trajectory going through doublets does not affect the interpretation of other trajectories as it is readily discriminated by persistent homology and thus random walks passing through this (spurious) trajectory do not contaminate the markers’ evolution inferred for legitimate trajectories.

We therefore prefer to remove only the barcode illegitimate and keep all others in analysis, using the expert analysis step also to identify (using the cell cycle markers plus other features) the artificially formed doublets and thus spurious connections.

(10) The authors should discuss how the gene expression trend plots are made (e.g. how are the expression averaged? Rolling mean?).

The development of those markers is shown as a line plot connecting the average values of a specific marker within a pseudotime segment. By default, the pseudotime values are divided into uniform segments (each containing the same number of points) whose number can be changed in the GUI. To focus on either early or late stages of the development, the segment division can be adjusted in GUI. See section 6 of the Supplementary Note.

Reviewer #3 (Recommendations For The Authors):

The overall figures quality needs to be improved. For example, I can barely see the text in Figure 3c.

Resolution of the Figures was improved

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

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Reply to the reviewers

Manuscript number: RC-2024-02825

Corresponding author(s): Padinjat, Raghu

Key to revision plan document:

Black: reviewer comments

Red: response to reviewer comment-authors

Blue: specific changes that will be done in a revision-authors

1. General Statements [optional]

We thank the reviewers for their detailed comments on our manuscript and appreciating the novelty, quality and thoroughness of the work. Detailed responses to individual queries and revision plans are indicated below.

2. Description of the planned revisions

Reviewer 1:

Summary The study by Sharma et al uses iPSC and neural differentiation in 2D and 3D to investigate how mutation in the OCRL gene affects neural differentiation and neurons. Mutation in the OCRL gene the cause of Lowe Syndrome (LS), a neurodevelopmental disorder. Neural cultures derived from LS patient iPSCs exhibited reduced excitability and increased glial markers expression. Additional data show increased levels of DLK1, cleaved Notch protein, and HES5 indicate upregulated Notch signaling in OCRL mutated neural cells. Treatment of brain organoids with a PIP5K inhibitor restored calcium signalling in neurons. These findings describe new dysregulated phenotypes in neural cultures of OCRL mutated cell shedding light on the underlaying caus of Lowe Syndrome.

Major comments

1. In general, I think the use of iNeurons usually means direct reprogramming from a somatic cell to neurons without the iPSC stage. Could be confusing to use this term for iPSC derived neurons. Thank you for pointing this out. We agree and will remove this term and replace it with a more suitable one in the revised manuscript.

Please add at least one more replicate of WP cell line to the single nuclei RNAseq.

There is no cell line called WP1 in the manuscript. We believe the reviewer was likely referring to WT1 (wild-type 1).

10xgenomics guidelines highlight that the statistical power of a multiome experiment relies on several factors including sequencing depth, total number of cells per sample, sample size and number of cells per cell type of interest (10xgenomics). In this study, we performed a multiome experiment and obtained high-quality reads from 20,000 nuclei for each sample for both the modalities: snRNA seq and snATAC seq. The multiome kit recommends a lower limit is 10,000 nuclei per sample. Thus the number of cells sampled per cell line is double the suggested minimum. Therefore, and consistent with other single-cell seq studies already published, our study followed the approach where biological replicates were not included ( for e.g see PMID: 39487141, GSE238206; PMID: 31651061; PMID: 32109367, GSE144477; PMID: 40056913, GSE279894; PMID: 38280846 GSE250386; PMID: 36430334, GSE213798; PMID: 33333020, GSE123722; PMID: 32989314, GSE145122; PMID: 38711218, GSE243015, PMID: 38652563, GSE236197). Furthermore, single-cell RNA-seq inherently treats each individual cell as as a replicate (Satija lab guidelines, PMID: 29567991; Wellcome Sanger Institute), reducing the necessity for additional biological replicates. Overall this appears to be the current standard in the field which we have followed.

Importantly, we took additional steps to validate the predictions our single-nuclei RNA-seq findings experimentally. For this we used a 3D brain organoid system. We confirmed key observations noted initially in 2D neural stem cells using a brain organoid model. This approach allowed us to confirm key predictions from the single cell sequencing data set. For example, in Lowe Syndrome patient derived organoids and OCRL-KO organoids, we noted increased DLK1 levels (Fig5.C-D, H-I) as well as increased GFAP+ cells and gene expression in brain organoids (Fig.S4E,F). These complementary approaches strengthen our confidence in the biological relevance of our findings from the single nuclei sequencing experiments.

The WT1 and the patient lines are rarely analysed together with the WT2 and KO lines, thus it is tricky to understand if the KO line is mimicking the patient lines? Please, add more merged analyses. Co-analysing all lines:

(i)would show if the KO line is more similar to the patient lines or to the WT1 or somewhere in between.

1. ii) Could answer questions about the variation in phenotypes between the genetic backgrounds. iii) Elucidate how much variability there is between the two WT lines in your assays. If the two WT lines vary much then conclusions about phenotypes in the patients and KO lines might need to be rethought? The reviewer is right is noting that throughout the manuscript we have analysed the patient lines with WT1 and the KO line with WT2. This was a conscious decision which we believe is the correct one for the following reasons:

It is well recognized and discussed in the literature that genetic background can be a key factor contributing to phenotypes observed in cells differentiated from iPSC (Anderson et al., 2021, PMID: 33861989; Brunner et al., 2023, PMID: 36385170; Hockemeyer and Jaenisch, 2016, PMID: 27152442; Soldner and Jaenisch, 2012, PMID: 30340033; Volpato and Webber, 2020, PMID: 31953356). Therefore, as a matter of abundant precaution, in this study we have tried to use the closest possible genetically matched control lines for analysis.

The patient lines used in this study for Lowe syndrome were all derived from a family in India of Indian ethnic origin. Therefore, in order to reduce the potential impact of genetic background contributing to potential phenotypes, we have used a control line derived from an individual of Indian ethnic background; this line has previously been developed and published by our group (PMID: 29778976 DOI: 10.1016/j.scr.2018.05.001). By contrast, the OCRLKO line was generated using the control line NCRM5 (WT2); this line is derived from a Caucasian male (RRID: CVCL_1E75). Therefore, whenever we have analyzed OCRLKO, we have used NCRM5 as the control; throughout the manuscript, NCRM5 is referred to as WT2.

However, in deference to the reviewer’s concerns we have performed a few analyses to compare the extent of variability between the two control lines.

Figure Legend: Replotted [Ca2+]i transients data from LS patient lines, OCRLKO and two control cell lines WT1 and WT2. (A) There is no statistical difference in the frequency of [Ca2+]i transients between WT 1 and WT2. Test used-Mann Whitney test. (B) Plot with WT1 and WT2 data combined versus all three LS lines and OCRLKO combined. Test used-Mann Whitney test. (C) WT1 and WT2 combined plotted against three individual patient lines and OCRLKO. Statistical test used One-way ANOVA. (total neurons analysed: WT1:808; WT2:267; LSP2:150; LSP3:462; LSP4:463; OCRLKO:411)

(i) We compared the frequency of calcium transients between neurons of age 30 DIV between WT1 and WT2 (Panel A above). We found no significant difference between these.

Additionally, as suggest we combined the data from both control lines into a single set and that from all the LSP patient lines and OCRLKO into another one (Panel B above). At the end of the analysis the difference between control and OCRL depleted cells remains. Please note the large number of cells studied in each genotype.

We also combined both control lines into a single control data set and compared it to each patient line and OCRLKO. We find that each patient line and OCRLKO is still significantly different from the control set (panel C above).

We did not find that OCRLKO to be significantly different from LSP2 or LSP4, indicating that the OCRLKO line closely aligns with the patient-derived lines, supporting the idea that the observed phenotype is primarily disease-driven rather than background-dependent. However, we did observe a significant difference between LSP3 and OCRLKO, highlighting some degree of inter-patient variability. Therefore, the key point is that the disease phenotype remains stable across different backgrounds, reinforcing the idea that the observed differences are driven by OCRL loss rather than background variability. This will be discussed in the revision.

(ii) In our RTPCR assay for HES5, when WT1 and WT2 are plotted together, there is no significant difference observed (panel A below). Similarly, western blotting data for cNotch (panel C) and DLK1 (panel B) of pooled WT1 and WT2 together on one plot shows no significant difference (Unpaired t-test, Welch’s correction). Overall, based on the above data, WT1 and WT2 are not statistically different.

Figure legend: Comparison of control lines WT1 and WT2. (A) comparison of HES5 transcripts. (B) Western blot for DLK1 levels. (C) Western blot for cleaved notch protein levels. Statistical test: Unpaired t-test, Welch’s correction.

Please include more discussion and rational around the link between the expression pattern of OCRL and the various phenotypes shown. From the RNAseq data performed at the NSC state where the expression of OCRL is lower than in neurons there are considerable differences in cell type distribution between lines. How can this skew cell type distribution affect downstream differentiation and neuronal function?

We would like to highlight that we did not perform bulk RNAseq in NSC and neurons; rather, we performed snRNA seq in NSCs (Fig3). The data in Fig.1E is mined from a publicly available resource dataset (Sidhaye et.al., 2023, PMID: 36989136) as mentioned in line 155, which is an integrated proteomics and transcriptomics generated from iPSC-derived human brain organoids at different stages of development in-vitro.

Fig 1D and 1E do indeed show lower levels of OCRL expression in NSC compared to neurons. However, it is important to bear in mind that even though OCRL may be expressed at relatively low levels during the NSC stage, its enzymatic activity could still have a substantial impact. Therefore, even at low expression levels, OCRL could be modulating the PI(4,5)P2 pool in ways that significantly influence cellular functions, especially during early stages of neurodevelopment that alter cell-fate decisions thereby affecting neuronal excitability.

Our working model posits that loss of OCRL leads to increased levels of PI(4,5)P2 which upregulates Notch pathway thereby leading to an increase in its downstream effector HES5. HES5 is a known transcription factor influencing gliogenesis and thus leading to a precocious glial shift in OCRL deficient NSCs as seen in our multiome dataset. This temporal perturbation in differentiation affects maturation of LS/OCRL-KO neurons and/or astrocytes leading to a defective neuronal excitability.

Also, OCRL is expressed also at the iPSC state as shown in Figure 1I, do you see any phenotypes in iPSC? If not, explain how that could be.

Yes, OCRL is indeed expressed in iPSCs as shown in Figure 1I. In an earlier paper from our lab that described the generation of these patient derived iPSC from Lowe syndrome patients (Akhtar et.al 2022 PMID: 35023542), we have reported that PIP2 levels are elevated at the iPSC stage as well as NSC stage in OCRL patient lines. We have not performed a detailed analysis of the iPSC stage for these lines as the focus of our investigation was primarily on the later stages of differentiation, particularly in neural progenitors and differentiated neurons. However, in response to the reviewer’s questions on why there are no obvious phenotypes at the iPSC we would suggest that this is due to compensation from the activity of other genes of the 5-phosphatse family. In support of this, we would cite our previous study (Akhtar et.al 2022 PMID: 35023542), in which we show that in LS patient derived lines, at the iPSC Stage, at least six other 5-phosphatases are upregulated.

There is not enough data in the manuscript to show mechanistic links between OCRL, DLK1 and Notch so be aware not to overstate the conclusions.

We appreciate the reviewer’s constructive comment regarding the mechanistic links between OCRL, DLK1, and Notch. Treatment of organoids and neurons with UNC-3230 PIP5K1C inhibitor rescues the observed phenotypes suggesting a role for a PIP2 dependent process, this process itself remains to be identified. We will adjust the wording in the manuscript during the revision to ensure that this comes through and the conclusions do not appear overstated.

Line 173, please describe what mutation in the OCRL these patients have, is it a biallelic deletion? Is the protein totally absents? Please show western blot analyses of the protein in the patient lines.

The patients from whom these LS lines were generated, the nature of the OCRL allele in them and the status of OCRL protein have all been previously been described in detail in a paper from our lab. This paper (Akhtar et.al 2022 PMID: 35023542) has been cited in the present manuscript at the very first occasion that the lines are described (Line 174, references 26 and 27). In addition, in the present manuscript, the protein status of OCRL in all the three patient lines is shown with a Western blot in Figure 3C.

Would be good with a bit of clinical explanation of these patients? Do they have the same level of severity? Are there any differences between their clinical symptoms? This could be interesting to link to differences in cellular phenotypes.

The clinical details of each patient are described in a preprint from our lab (Pallikonda et.al., 2021 bioRxiv 2021.06.22.449382).The potential reasons for the difference in severity, a very interesting scientific question, is also addressed in this preprint. Currently experimental analysis to support the proposed likely reasons is ongoing in our lab. We feel those analysis are beyond the scope of this manuscript and will be published later this year as a separate study.

As described in in ref 26 and 27, LSP patients have a mutation in exon 8 leading to a stop codon. We mimicked this by CRISPR based genome editing to introduce a stop codon and protein truncation in exon 8 to generate of WT2 to OCRLKO. This is also described in supplementary Fig 1 of the present manuscript and the technical details of line generation are fully described in the materials and methods.

Like the patient lines OCRLKO is a protein null allele-this is shown by Western blot in Fig 2D. Also in OCRLKO, the PIP2 levels are elevated (Fig 2E) recapitulating what has been described by us in (Akhtar et.al 2022 PMID: 35023542). We will explicitly state this detail around line 185.

Figure 1I, could the protein levels at the different stages be quantified?

Yes, we can and will do it in the revision

Figure 3A, there seem to be much more cells in LSP2, making it tricky to compare with the other cell lines. Density during differentiation can affect the cell fate. Please, provide images from the different lines that are comparable with similar density.

We controlled for cell density by seeding equal number of cells 50,000 cells/cm2 for all the genotypes, as mentioned in the material and methods. However, heterogeneity between lines during terminal differentiation is well-established, leading to crowding in some genotypes while not in others. Additionally, different growth rates during terminal differentiation also leads to crowded neural cultures as a function of genotype. Therefore, to complement our immunostaining data, we have provided western blot analyses showing increased GFAP protein levels in LS patient lines compared to controls. We will provide images from different lines that are comparable in density during the revision.

Please provide quantification to the statement that there is fewer number of S100B cells in the LSP lines.

As we haven’t quantified the number of S100B cells, we will remove that statement.

Figure 3B, the images show cells very different, and it is tricky to compare similarities and differences, please provide images that look more similar to each other. Avoid images with clusters of cells or make sure to select representative images with clusters from each cell line. If the clustering is a phenotype explain and quantify that. Make sure the density is similar in all pictures.

We will provide images of matched density during the revision. Also see response to comment above.

Line 2018, the statement "In the same cultures, there was no change in the staining pattern of the neuronal markers MAP2 and CTIP2 (Fig 3B)" is not strengthened by the figure. Please provide new pictures or data to prove the statement.

As CTIP2 staining is inherently observed in either clumps or sparsely distributed regions across WT1 and LSP genotypes, we will replace the CTIP2 marker with TBR1, which is also a deep layer cortical marker (layer VI-V), as shown below. Using this additional marker for neurons, we continue to see no change in staining pattern of neuronal markers MAP2 and TBR1. Corresponding images for each genotype are optically zoomed-in images of individual neurons positive for MAP2 and TBR1. Scale bar=50µm, 20µm.

Figure 3E, please describe all markers in the picture, thus also MAP2, S100B, CTIP2 and draw conclusions. Try to show comparable pictures.

This will be attended in the revision

Fig 3D and G, what are the replicates? please explain.

Each point represents a single neural induction done on iPSCs to generate NSCs and then terminally differentiated 30DIV cultures. Experiments were done across 3-6 independent neural inductions. This detail will be included in the revised figure legend.

Figure 4 A, C, there is a large difference in the ratio of different cell types between the different cell lines, also between the LSP2 and LSP3. This would indicate either that the genetic background affects the phenotype to a large extent or that there is large variability between rounds of differentiation. To understand how much variability that comes from the differentiation and culturing: another replicate of WP cell from another donor (WT2) should be included (single nuclei RNAseq). Confirm that three independed rounds of differentiation of the WT1, WT2, LSP2, LSP3, LSP4, and OCRL-KO result in similar outcome when it comes to cell type distribution. Could be done with qPCR marker.

For scientific reasons explained in response to the reviewer’s comment #2 we feel it is not necessary to perform replicates of the single nucleus multiome seq. However to allay the reviewer’s concern of variability between differentiations leading to a conclusion of altered cell state we present the following three suggestions for a revised manuscript:

• We will perform multiple differentiations from iPSC to NSC and test the altered cell state using Q-PCR for transcripts of glial lineage markers.

• Shown below are western blot analyses for WT1, LSP2, LSP3 and LSP4 NSCs (left). Analyses were done from 4 independent rounds of neural inductions and exhibit a significant increase in the levels of a astrocytic fate-determinant marker NF1A in LSP NSCs wrt to WT1 (Mann Whitney test used to measure statistical significance). Each point represents sample from an independent neural differentiation.

• We would also like to highlight that we have already demonstrated increased GFAP levels in LS patient derived differentiated cultures and OCRLKO. These data, quantified in Fig 3D are done using samples derived from multiple differentiations of iPSC to NSC and then terminally differentiated. Thus the phenotype of enhanced glial cells in LS derived cultures, is most likely a consequence of the increased number of glial precursor cells is seen across multiple differentiations.

Line 309, "astrocytic transcripts NF1A and GFAP was elevated" It is unclear from this sentence in which cell lines NF1A and GFAP is elevated? Please explain.

We acknowledge the incompleteness in the statement. We will add the complete statement explaining the graphs. The levels of astrocytic transcripts NF1A and GFAP were elevated in LSP3 and LSP4 compared to WT1.

Figure 5C, E, G, there is a large variation of Notch and Hes5 expression between the different

This comment is incomplete.

Figure 5H, unclear which of the bands that is DLK1 and how the bands relate to the quantification. The band at 50 kDa seems to be stronger in the WT2 than in the OCRL-KO but in the quantification in Figure 5I, it shows 2x more in the KO. Thus, the other way around.

The datasheet of DLK1 antibody used (Abcam ab21682; RRID_AB731965) describes bands seen at 50,48, 45 and 15kDa. We have quantified the bands at 50kDa and 48-45kDa for all the genotypes. This will be explicitly stated in the revised figure legend.

Figure 6, please show that the inhibitor is inhibiting PIP5KC.

Have you titered the added concentration of the inhibitor?

Figure legend: Fields of view from WT1 derived NSC expressing the plasma membrane PIP2 reporter. Plasma membrane distribution of the probe indicating PIP2 levels is shown in (A) untreated cells (B) treatment with 10mM and (C) 50mM UNC-3230 PIP5K1C inhibitor. Scale bar=50µm (D) Quantification of plasma membrane PIP2 levels using this reporter. Y-axis shows probe levels at PM; X-axis shows treatment conditions.

Yes, we used a previously generated plasma membrane PH-PLC::mCherry reporter WT1-NSCs (Akhtar et.al., 2021) and carried out a dose-response experiment using 10mM and 50mM of the UNC-3230 PIP5K1C inhibitor as shown above. We quantified intensity of PI(4,5)P2::mCherry at the plasma membrane and plotted the mean intensity. We observed a significant decrease in plasma PI(4,5)P2 levels at 50mM (Statistical used: Mann Whitney test) but not 10mM and therefore we selected that concentration for our experiments.

Figure 6B, why do the calcium data for the WT2+1Ci look so different to the other, the dots are much more spread and seem to fewer replicates that for the other sample, please explain.

We had only analysed a few replicates for WT2+1Ci genotype. We analysed the remaining replicates and have updated the data as shown below. The revised data set resolves the reviewer’s concern. The revised data set will be included in the revision.

Figure 6F, there is no significant differences between the bars but the statement in the text (sentence starts on line 332) indicate it is, please update the figure or remove the statement.

We added more replicates (now total is 7-10 biological replicates each with 15-20 organoids) and updated the figure (panel B) is shown below. The differences between treated and untreated of OCRLKO are significant whereas there is no significant difference between wild type, treated and untreated (statistical test: Mann Whitney test).

Revised figure will be included in the revision

Figure 6G, the HES5 expression seem to behave very similar in both WT2 and OCRL-KO cells when the inhibitor is used. What does this mean? Seems to not be linked to OCRL. Explain.

Thank you for your comment. In our initial experiment (shown in original version of manuscript), we observed a reduction in HES5 expression upon inhibitor treatment in both WT2 and OCRL-KO cells. However, to ensure robustness of our findings, we repeated the experiment across multiple, additional independent organoid differentiation batches. In this redone experiment, we no longer observe the previous trend. Instead, we see no significant changes in WT2 on inhibitor treatment, while OCRLKO cells show a reduction in HES5 expression upon inhibitor treatment (Panel A). Similarly, the protein levels of cNotch and DLK1 are not different between WT2 and WT2+1Ci (panel B and C). This strongly suggests loss of OCRL leading to elevated levels of PIP2 perturbs Notch pathway, resulting in higher cNotch and thereby increased effector expression of HES5. New data set will be included in the revision.

Minor comments

The panels in Figure 6 are not completely referred to correctly in the text, please check. Double check that all figure panels are referred to properly in the text

Yes, we will correct it in the revised manuscript.

Reviewer #1 (Significance (Required)): The manuscript is an interesting addition to the in vitro iPSC derived cellular modelling of neurodevelopmental disorder. Strengths: The use of both patient iPSC lines and CRISPR edited lines The use of both monolayer and 3D cultures We thanks the reviewer for their detailed critique. Addressing these has helped improve the manuscript. We thank the reviewer for appreciating the strengths of the manuscript. Weaknesses: the significance decrease a bit due too few replicates (only 1 WT line in each experiment) and the variability between the patients' cell lines. We thank the reviewer for this comment. As explained above we have added substantially more data and revised the analysis which should remove this concern.

Reviewer 2:

This paper describes the effects of loss of OCRL (the Lowe syndrome protein) upon the function and differentiation of neurones, using an in vitro iPSC model system. Cells derived from three related Lowe syndrome patients and an OCRL knockout, generated using CRISPR, were used for these experiments. The results show that upon loss of OCRL, differentiation of stem cells into neurones is reduced, with an increased number of cells adopting glial and astrocytic fates. The neurones that are generated have reduced calcium transients and electrical activity. Gene expression data combined with biochemical analysis indicate altered Notch activity, which may account for the altered cell fate data seen in the in vitro differentiation model. Finally, rescue of cell fate and neuronal activity is seen upon knockdown of a PIP5K, which indicates that these phenotypes are due to the elevated PIP2 levels seen on the OCRL-deficient cells.

The results provide new insights into the pathogenesis of Lowe syndrome. I found the paper to be well done, and the data supports the conclusions of the authors. I have a few comments below that may improve the manuscript:

We thank the reviewer for summarizing the comprehensive nature of our study and appreciating the value of our study in providing new insights into the pathogenesis of Lowe syndrome with respect to the brain. Thank you for appreciating that our study is well done, and that the data supports the conclusions of the authors.

Major points

1. The UMAP and ATAC-Seq data indicate different maps for the two different Lowe syndrome patient-derived cells (Fig 4 and Fig S3). This suggests that the cells are quite different, and therefore that changes seen in one Lowe syndrome patient may not be applicable to the others. I think this heterogeneity has important implications for the paper i.e. how general are findings obtained? Several different glioblast types are described (numbered 1-5)- how different or similar are these? We are unclear what the reviewer means by “ the UMAP and ATAC seq data indicate different maps…….”.

UMAP is a technique for visually representing data generated by single cell analysis methods be it RNAseq or ATAC seq. Perhaps what the reviewer means is that the UMAP generated from RNA seq and ATAC seq data looks different from each other.

We would like to reiterate that the UMAP generated from single cell RNA seq data is based on the complement of transcripts in each cell of the analysis compared to an existing single cell RNAseq data set, whereas the UMAP generated from ATACseq is generated from regions of open chromatin detected in and around genes and therefore presumably also reflecting ongoing gene expression. In principle the two analyses for any set of cells should indicate overall clustering into similar groups on UMAPs generated using both data sets, if the ATACseq based read out of transcription largely maps the RNAseq based read out of differences in transcription. However, it may not be reasonable to expect them to be identical. This is indeed what we see for our data set, and this has been represented in Fig 4E. The cell clusters detected based on GEX (gene expression i.e single cell RNA seq) analysis are plotted against the cells clusters detected from ATACseq data using a confusion matrix. As can be seen from this panel (Fig 4E), a very large fraction of cells falls on the diagonal indicated a large degree of similarity between clusters detected by both methods (GEX and ATACseq) of analysis. This can be reiterated more strongly during the revision by strengthening this statement.

The PIP5K inhibitor seems to have a very strong effect on both WT and KO cells in terms of Notch activity (Fig 5G). This strongly suggests the effects of this inhibitor are not through OCRL and that changes in PIP2 induced by the inhibitor override those of OCRL. Thus, the experiments shown in Fig 5 seem not to be due to a rescue of OCRL activity as such.

We think reviewer means Fig 6G and our response is as follows:

In our initial experiment (shown in the current version of manuscript), we observed a reduction in HES5 expression upon inhibitor treatment in both WT2 and OCRLKO cells. However, to ensure robustness of our findings, we repeated the experiment across multiple, additional independent organoid differentiation batches. In this redone experiment, we no longer observe the previous trend. Instead, we see no significant changes in WT2 on inhibitor treatment, while OCRLKO cells show a reduction in HES5 expression upon inhibitor treatment (Panel A). Similarly, the protein levels of cNotch and DLK1 are not different between WT2 and WT2+1Ci (panel B and C). This strongly suggests loss of OCRL leading to elevated levels of PIP2 perturbs Notch pathway, resulting in higher cNotch and thereby increased effector expression of HES5. The figures updated with the new data will be included in the revision.

Minor points

1. The main text needs to say what synapsin is and why it was analysed. In Fig 1I, synapsin abundance declines at 90 days. This appears quite strange. The authors should comment on it in the text. We will add a line about use of synapsin in the western. Synapsin is only used qualitatively to highlight mature neuronal culture age, as was done in Sidhaye et.al PMID: 36989136.

In the revised main text, we will add the following explanation: "We also analyzed the expression of synapsin-1, a synaptic vesicle protein that serves as a marker for mature synapses and functional neuronal networks. The presence of synapsin-1 indicates the development of synaptic connections in our cultures, providing evidence of neuronal maturation."

.

The decline and thereby variability in synapsin-1 protein levels has been reported before. Regarding the decline in synapsin-1 at 90 days, we can add the following discussion:

"We observed a decline in synapsin-1 levels at 90 days in vitro (DIV) compared to earlier time points. This pattern has been previously reported in iPSC-derived neuronal models (Togo et.al PMID: 34629097 and Nazir et.al PMID: 30342961). Such variability in synapsin-1 expression over extended culture periods may reflect the dynamic nature of synaptic remodeling and maturation processes in vitro. It's important to note that synapsin-1 levels can fluctuate due to various factors, including culture conditions and the heterogeneity of neuronal populations present at different time points."

In Fig 2A and 3B there are clumps of green cells (CTIP2 positive). I am concerned that the lack of uniformity in the cell distribution could impact other analysis performed, where certain fields of view have been analysed e.g. by imaging or electrophysiology e.g. calcium measurements.

To address the reviewers concern about uniformity, in the revised manuscript, we will provide/replace the representative images of deep layer markers along with MAP2 from all genotypes showing the areas selected for analysis to demonstrate that data collection was performed in comparable regions across all experimental conditions. As answered in the response to reviewer 1, comment 11.

The clumps of neurons (as seen in Fig2A) poses challenges for obtaining high-quality seals during patch-clamp recordings. To address this, we primarily selected areas with sparsely distributed neurons for electrophysiology experiments. This approach ensured robust recordings. To address this, we can provide a clarification in the Methods section to explicitly state that neurons used for all patch-clamp recordings were chosen from regions where cells were sparsely distributed.

In case of calcium imaging experiments, we focused on both crowded and sparse fields of views across genotypes to avoid potential biases introduced by clumped cells. However, it is to be noted that during the stages of terminal differentiation there are NSCs undergoing proliferation, which makes the neuronal culture denser. We can provide video files as a supplementary material to demonstrate the types of areas used for calcium imaging experiments. Additionally, we will include a statement in the Methods section specifying that regions with uniform neuronal distribution were selected for calcium imaging to ensure consistency in our analysis.

In Fig 2J and 2K are the differences between sampels significant? The error bars are huge.

From line 204-209, we have not used the word “significantly different”. We acknowledge that the error bars in Figures 2J and 2K are indeed large, which is not uncommon in electrophysiological recordings from iPSC-derived neurons due to their inherent variability. We have intentionally refrained from claiming statistical significance for these specific comparisons. Instead, we describe the data as showing a pattern or trend of reduced currents in OCRLKO neurons compared to WT2. To improve clarity, we propose to add a statement in the results section acknowledging the variability in these measurements and explaining our interpretation of the data as a trend rather than a statistically significant difference.

In Fig S4- it would be good to show gene expression analysis and GFAP staining

We are not completely sure what this comment means. However the present figure shows double staining with GFAP and S100beta. These will be split and shown separately to enhance clarity.

Fig 5A needs more annotation- fold change comparing what to what?

We will add the annotation “fold change wrt to WT1”.

There should be more information provided in the main text relating to DLK1. For example, it is shown to be secreted, but no information is provided on whether this is expected. Secreted? The DLK1 blot in Fig 5F is not convincing.

We will add more information relating to DLK1 and secretion status.

DLK1 is a non-canonical notch ligand that is indeed known to be secreted by neighboring cells to either activate/inhibit notch pathway. While we acknowledge the blot could have been better, however, variability in the blot could arise due to differences in secretion efficiency, or protein stability in the cell culture media that could have led to inconsistencies across LSP genotypes. However, as shown in the blot, the OCRLKO shows a clear enrichment of secreted-DLK1 compared to WT2.

We have performed the western blot analyses across two independent differentiations of organoids from WT1, LSP2, LSP3, LSP4, WT2, OCRL-KO iPSCs in phenol-free neurobasal-A medium, and quantified secreted protein. We then loaded 40mg of protein per genotype. Shown below is the quantification. The quantification of mean intensity of DLK1 band shows a moderate increase in LSP2, and substantial increase in LSP3 and LSP4 organoids as compared to WT1. While OCRL-KO a substantial increase compared to its control, WT2. A revised figure will be used in the revision.

Rationale for choosing PIP5K1C

PIP5K1C is one of the major regulators maintaining appropriate levels of the synaptic pool of PI(4,5)P2, synaptic transmission and synaptic vesicle trafficking (Hara et al., 2013 PMID: 23802628; Morleo et al., 2023 PMID: 37451268; Wenk et al., 2001 PMID: 11604140). Therefore, we were interested in rescuing the physiological phenotype, we chose PIP5K1C. Additionally, in initial experiments we found that inhibiting PIP5K1B using ISA-2011B killed the organoids or lead to detachment of 2D neuronal cultures.

Fig 6D is confusing. I suspect the figure labelling is not correct- it does not correlate with the graphs.

We apologise for the error and will correct this.

Reviewer #2 (Significance (Required)):

This paper is significant because it provides important new information on the neurological features of Lowe syndrome. The approach is novel in terms of studying this condition. The findings are likely to be of interest to clinicians, cell biologists, neurobiologists and those studying human development. My expertise is in membrane traffic and OCRL/Lowe syndrome. I am not a neurobiologist.

We thank the reviewer for appreciating the importance of our study, novelty of findings and newof our approach we have used. We would light to highlight that while extensive work has been done with respect to the renal phenotype of Lowe syndrome, the brain phenotypes have remained largely a black box. This is in part because mouse knockouts of OCRL have failed to recapitulate the brain related clinical phenotypes displayed by Lowe syndrome patients (for e.g. PMID: 30590522; PMCID: PMC6548226; DOI: 10.1093/hmg/ddy449). Our study of brain development defects in Lowe syndrome depleted cells provides the first insight into the cellular and developmental changes in this disorder.

Reviewer 3:

This paper by Sharma et al describes findings in an iPSC model of Lowe Syndrome. This is an important line of research because no mouse models phenocopy the neurodevelopmental aspects of the condition. They identified a potential role of Notch signaling in pathogenesis, a potentially druggable target. However, several issues need to be addressed.

We thank the reviewer for appreciating the importance of our study in covering the basis of the neurodevelopmental phenotype of Lowe syndrome. Due to a lack of a mouse model, there was previously no understanding of how the clinical features related to the brain arise.

Major issues

1. The sample size is very small, which is understandable to some extent given the expense and difficulty doing research using iPSCs. However, there are a couple of opportunities to improve the sample size. For example, in the analysis of DLK1 and other proteins shown in Figure 5, the analysis amounts to a single control vs the 3 patient lines, and a single control vs the KO line. The separation is justified because a complete KO of the gene might result in differences compared to hypomorphic mutation that apparently affects the 3 cases. However, there is no reason why WT1 and WT2 shouldn't be combined. They are both random controls. This might not affect the results of the other proteins analyzed, NOTCH and HES5, but the significance of DLK1 could change. Nature of the allele in LS patient lines

There is a misconception in the reviewer comment that the OCRL allele in the three Lowe syndrome lines is a hypomorph. This is not correct. In the patients from whom these LS lines were generated, the nature of the OCRL allele and the status of OCRL protein in cells have been previously described in detail in a peer-reviewed, published paper from our lab. This paper (Akhtar et.al 2022 PMID: 35023542) has been cited in the present manuscript at the very first occasion that the LS patient lines are described (Line 174, references 26 and 27). As described in in ref 26 and 27, LSP patients have a mutation in exon 8 leading to a stop codon. This results in a protein null allele of OCRL in all three patient lines. This has been shown in Fig 1B of Akhtar et.al 2022 by immunofluorescence using an OCRL specific antibody (PMID: 35023542). It has also been demonstrated by Western blot using an OCRL specific antibody for all three LS patient lines in Fig 3C and 5C of the present manuscript. The nature of the allele will be highlighted more clearly in the revision.

*Combining WT1 and WT2 *

We are not in favour of combining WT1 and WT2. The reason for this is as follows.

It is well recognized and discussed that genetic background can be a key factor contributing to phenotypes observed in cells differentiated from iPSC (Anderson et al., 2021, PMID: 33861989; Brunner et al., 2023, PMID: 36385170; Hockemeyer and Jaenisch, 2016, PMID: 27152442; Soldner and Jaenisch, 2012, PMID: 30340033; Volpato and Webber, 2020, PMID: 31953356). As a result, it is recommended that a line closely matched for genetic background be used when assessing the validity of observed phenotypes. The patient lines used in this study for Lowe syndrome were all derived from a family in India of Indian ethnic origin. Therefore, in order to reduce the impact of genetic background contributing to potential phenotypes, we have used a control line (referred to in this manuscript as WT1) derived from an individual of Indian ethnic background; this line has previously been developed and published by our group (PMID: 29778976 DOI: 10.1016/j.scr.2018.05.001).”

In the case of OCRLKO we have genome edited NCRM5 (a white Caucasian male control line) to introduce a stop codon in exon 8 to mimic the truncation seen in our LS patient lines. This allele is also protein null as shown by Western blot using an OCRL specific antibody. The data is shown in Fig 2D of the present manuscript. Therefore, we reiterate that all the LS patient lines in this study and OCRLKO are protein null alleles.

Status of DLK1 levels

We have performed a combined analysis of DLK1 levels in the two control lines and all the patient lines as well as OCRLKO. As shown below the result remains unchanged, namely that DLK1 levels are elevated in OCRL depleted cells in this model system.

Figure legend: Quantification of DLK1 protein levels in control, LS patient and OCRLKO iPSC lines. Western blot intensities for each patient line and OCRLKO were normalized to GAPDH and then to the respective internal WT control (WT1 or WT2) resulting in fold-change values. For statistical analysis across genotypes, normalized fold-change values from different gels were pooled post hoc. All statistical testing was performed on fold-change values. Statistical test used: Mann Whitney test. (A) Values for WT1 and WT2 have been combined and plotted against individual values for three patient lines and OCRLKO (B) Values for WT1 and WT2 have been combined and plotted against combined values for all three LSP lines and OCRLKO.

Reviewer comment: DLK1 expression brings up another point. This, along with MEG3 and MEG8 are imprinted genes, two of the top differentially expressed genes in this study. However, these findings can be questioned by the well-known phenomenon that the expression of some imprinted genes may not be properly maintained during iPSC reprogramming. Thus, the differential expression of these imprinted genes might be due to a reprogramming artifact rather than the effects of OCRL per se. Analyzing both controls together could mitigate this objection. However, even if it does, the potential dysregulation of imprinted genes in the development of iPSCs should be acknowledged and addressed.

We are aware that the DLK1 locus is imprinted. However, we feel that reprogramming artifacts are very unlikely to explain the observed changes in DLK1 levels.

It is important to note that the patient lines and WT1 were not directly re-programmed from White blood cells to iPSC and then used for differentiation and analysis. As detailed in our previous peer-reviewed publications WT1 (PMID: 29778976) and the patient LSP lines (PMID: 35023542) were first converted to lymphoblastoid cell lines and subsequently reprogrammed into iPSC.

We think that re-programming induced imprinting changes are unlikely to be responsible for the elevated levels of DLK1 seen in LS patient lines. The reason is as follows:

We compared DLK1 levels in WT2 and OCRLKO which is a CRISPR edited line that introduces a stop codon in exon 8. NCRM-5/WT2 was derived from CD34+ cord blood cells. What we found is that levels of DLK1 are elevated in OCRLKO compared to WT2. Since OCRLKO was generated by genome editing WT2, it must be the case that the level of imprinting of the DLK-DIO3 locus is comparable if not identical between the two lines. Therefore, the difference in DLK1 levels between WT2 and OCRLKO cannot be a consequence of different imprinting status of the DLK1 locus between these two lines. Rather, it strongly suggests a causal link to OCRL deficiency. Following on from this, the DLK1 levels are elevated in patient lines compared to the OCRLKO. We will highlight and discuss and explain this in the revised version.

Similarly, in the calcium signaling experiment shown in fig.2, the KO and patient lines are justifiably separated. However, again, why not combine both controls in the comparison with the patient samples?

The data has been reanalyzed and presented as requested by the reviewer. There is no change in the conclusion.

For the reasons described above, it remains our preference to present each set of lines with the appropriate control; i.e WT1 and the three LS patient lines and WT2 with OCRLKO. However, as the reviewer has asked for it, we also present below analysis in which WT1 and WT2 and combined and LS patient lines and OCRLKO are combined. The replotted data is shown below. The essential conclusion shown in the main manuscript remains, namely that [Ca2+]i transients in LS depleted developing neurons is lower than in wild type.

Figure Legend: Replotted [Ca2+]i transients from LS patient lines, OCRLKO and two control cell lines WT1 and WT2 (A) There is no statistical difference in the frequency of [Ca2+]i transients between WT 1 and WT2. Test used-Mann Whitney test. (B) Plot with WT1 and WT2 data combined v all three LS lines and OCRLKO combined. Test used-Mann Whitney test. (C) WT1 and WT2 combined plotted against three individual patient lines and OCRLKO. Statistical test used One-way ANOVA. (total neurons analyzed: WT1:808; WT2:267; LSP2:150; LSP3:462; LSP4:463; OCRLKO:411)

Regarding the hypomorphic nature of the patient-specific iPSC, I do not see the OCRL variant that was found in the family. Please correct me if I missed that, and if it was omitted, it should be included. I suspect that the variant generates a hypomorphic OCRL protein because the authors show expression in Figure 1D. Hypomorphic OCRL mutations compared with complete KO could show differences in molecular phenotypes, as found in Barnes et al. (PMID: 30147856) in an analysis of F-actin and WAVE-1 expression.

Nature of the allele in LS patient lines

There is a misconception in the reviewer’s comment that the OCRL allele in the three Lowe syndrome lines is a hypomorph. This is incorrect. In the patients from whom these LS lines were generated, the nature of the OCRL allele in them and the status of OCRL protein have all previously been described in detail in a peer-reviewed, published paper from our lab. This paper (Akhtar et.al 2022 PMID: 35023542) has been cited in the present manuscript at the very first occasion that the LS patient lines are described (Line 174, references 26 and 27). As described in in ref 26 and 27, LSP patients have a mutation in exon 8 leading to a stop codon. This results in a protein null allele of OCRL in all three patient lines. This has been shown in Fig 1B of Akhtar et.al 2022 by immunofluorescence using an OCRL specific antibody (PMID: 35023542). It has also been demonstrated by Western blot using an OCRL specific antibody for all three LS patient lines in Fig 3C and 5C of the present manuscript.

The data presented in Fig.1D, E is a publicly available resource data PMID: 36989136 as mentioned in line 155, which is an integrated proteomics and transcriptomics generated from control iPSC-derived human brain organoids at different stages of development in-vitro.

Minor issue

The authors use the term mental retardation on line 102 to describe the cognitive phenotype in Lowe Syndrome. Medical, legal, and advocacy groups have abandoned this term because it is viewed as offensive. It is being replaced by intellectual disability, although this term also is problematic. In any event, many conferences on autism and intellectual disabilities are attended by families, and high-functioning cases sometimes address an audience of scientists. They would object to the use of this term if presented in a talk by one of the co-authors.

Thank you. We will rephrase this line.

3. Description of the revisions that have already been incorporated in the transferred manuscript

Not applicable at this stage. The above is a revision plan.

4. Description of analyses that authors prefer not to carry out

We prefer to not carry out replicates of the single cell multiome analysis. As explained above the state of the art in the single cell analysis field is to not do so. The scientific reasons as to why such replicates are not required have been explained in the response to the reviewer comment.

Author response:

Reviewer 1 (Public Review):

“Summary:

In this paper, the authors aimed to test the ability of bumblebees to use bird-view and ground-view for homing in cluttered landscapes. Using modelling and behavioural experiments, the authors showed that bumblebees rely most on ground-views for homing.

Strengths:

The behavioural experiments are well-designed, and the statistical analyses are appropriate for the data presented.

Weaknesses:

Views of animals are from a rather small catchment area.

Missing a discussion on why image difference functions were sufficient to explain homing in wasps (Murray and Zeil 2017).

The artificial habitat is not really 'cluttered' since landmarks are quite uniform, making it difficult to infer ecological relevance.”

Thank you for your thorough evaluation of our study. We aimed to investigate local homing behaviour on a small scale, which is ecologically relevant given that the entrance of bumblebee nests is often inconspicuously hidden within the vegetation. This requires bees to locate their nest entrance using views within a confined area. While many studies have focused on larger scales using radar tracking (e.g. Capaldi et al. 2000; Osborne et al. 2013; Woodgate et al. 2016), there is limited understanding of the mechanisms behind local homing on a smaller scale, especially in dense environments.

We appreciate your suggestion to include the study by Murray and Zeil (2017) in our discussion. Their research explored the catchment areas of image difference functions on a larger spatial scale with a cubic volume of 5m x 5m x 5m. Aligned with their results, we found that image difference functions pointed towards the location of the objects surrounding the nest when the images were taken above the objects. However, within the clutter, i.e. the dense set of objects surrounding the nest, the model did not perform well in pinpointing the nest position.

We agree with your comment about the term "clutter". Therefore, we will refer to our landmark arrangement as a "dense environment" instead. Uniformly distributed objects do indeed occur in nature, as seen in grasslands, flower meadows, or forests populated with similar plants.

Reviewer 2 (Public Review):

Summary:

In a 1.5m diameter, 0.8m high circular arena bumblebees were accustomed to exiting the entrance to their nest on the floor surrounded by an array of identical cylindrical landmarks and to forage in an adjacent compartment which they could reach through an exit tube in the arena wall at a height of 28cm. The movements of one group of bees were restricted to a height of 30cm, the height of the landmark array, while the other group was able to move up to heights of 80cm, thus being able to see the landmark array from above.

During one series of tests, the flights of bees returning from the foraging compartment were recorded as they tried to reach the nest entrance on the floor of the arena with the landmark array shifted to various positions away from the true nest entrance location. The results of these tests showed that the bees searched for the net entrance in the location that was defined by the landmark array.

In a second series of tests, access to the landmark array was prevented from the side, but not from the top, by a transparent screen surrounding the landmark array. These tests showed that the bees of both groups rarely entered the array from above, but kept trying to enter it from the side.

The authors express surprise at this result because modelling the navigational information supplied by panoramic snapshots in this arena had indicated that the most robust information about the location of the nest entrance within the landmark array was supplied by views of the array from above, leading to the following strong conclusions:

line 51: "Snapshot models perform best with bird's eye views"; line 188: "Overall, our model analysis could show that snapshot models are not able to find home with views within a cluttered environment but only with views from above it."; line 231: "Our study underscores the limitations inherent in snapshot models, revealing their inability to provide precise positional estimates within densely cluttered environments, especially when compared to the navigational abilities of bees using frog's-eye views." Strengths:

The experimental set-up allows for the recording of flight behaviour in bees, in great spatial and temporal detail. In principle, it also allows for the reconstruction of the visual information available to the bees throughout the arena.

The experimental set-up allows for the recording of flight behaviour in bees, in great spatial and temporal detail. In principle, it also allows for the reconstruction of the visual information available to the bees throughout the arena.

Weaknesses:

Modelling:

Modelling left out information potentially available to the bees from the arena wall and in particular from the top edge of the arena and cues such as cameras outside the arena. For instance, modelled IDF gradients within the landmark array degrade so rapidly in this environment, because distant visual features, which are available to bees, are lacking in the modelling. Modelling furthermore did not consider catchment volumes, but only horizontal slices through these volumes.

When we started modelling the bees’ homing based on image-matching, we included the arena wall. However, the model simulations pointed only coarsely towards the clutter but not toward the nest position. We hypothesised that the arena wall and object location created ambiguity. Doussot et al. (2020) showed that such a model can yield two different homing locations when distant and local cues are independently moved. Therefore, we reduced the complexity of the environment by concentrating on the visual features, which were moved between training and testing. (Neither the camera nor the wall were moved between training and test). We acknowledge that this information should have been provided to substantiate our reasoning. As such, we will include model results with the arena wall in the revised paper.

As we wanted to investigate if bees would use ground views or bird’s eye views to home in a dense environment, we think the catchment volumes would provide qualitatively similar, though quantitatively more detailed information as catchment slices. Our approach of catchment slices is sufficient to predict whether ground or bird' s-eye views perform better in leading to the nest, and we will, therefore, not include further computations of catchment volumes.

Behavioural analysis:

The full potential of the set-up was not used to understand how the bees' navigation behaviour develops over time in this arena and what opportunities the bees have had to learn the location of the nest entrance during repeated learning flights and return flights.

Without a detailed analysis of the bees' behaviour during 'training', including learning flights and return flights, it is very hard to follow the authors' conclusions. The behaviour that is observed in the tests may be the result of the bees' extended experience shuttling between the nest and the entry to the foraging arena at 28cm height in the arena wall. For instance, it would have been important to see the return flights of bees following the learning flights shown in Figure 17.

Basically, both groups of bees (constrained to fly below the height of landmarks (F) or throughout the height of the arena (B)) had ample opportunities to learn that the nest entrance lies on the floor of the landmark array. The only reason why B-bees may not have entered the array from above when access from the side was prevented, may simply be that bumblebees, because they bumble, find it hard to perform a hovering descent into the array.

A prerequisite for studying the learning flight in a given environment is showing that the bees manage to return to their home. Here, our primary goal was to demonstrate this within a dense environment. While we understand that a detailed analysis of the learning and return flights would be valuable, we feel this is outside the scope of this particular study.

Multi-snapshot models have been repeatedly shown to be sufficient to explain the homing behaviour in natural as well as artificial environments. A model can not only be used to replicate but also to predict a given outcome and shape the design of experiments. Here, we used the models to shape the experimental design, as it does not require the entire history of the bee's trajectory to be tested and provides interesting insight into homing in diverse environments.

Our current knowledge of learning flights did not permit these investigations of bee training. Firstly, our setup does not allow us to record each inbound and outbound flight of the bumblebees during training. Doing so would require blocking the entire colony for extended time periods, potentially impairing the motivation of the bees to forage or the survival and development of the colony. Secondly, the exact locations where bees learn or if and whether they continuously learn by weighting the visual experience based on their positions and orientations is not always clear. It makes it difficult to categorise these flights accurately in learning and return flights. Additionally, homing models remain elusive on the learning mechanisms at play during the learning flights. Therefore, we believe that continuous effort must be made to understand bees' learning and homing ability. We felt it was necessary first to establish that bees could navigate back to the nest in a dense, cluttered environment. With this understanding, we are currently conducting a detailed study of the bees' learning flights in various dense environments and provide these results in a separate article.

While we acknowledge that the bees had ample opportunities to learn the location of the nest entrance, we believe that their behaviour of entering the dense environment at a very low altitude cannot be solely explained by extended experience. It is possible that the bees could have also learned to enter at the edge of the objects or above the objects before descending within the clutter.

General:

The most serious weakness of the set-up is that it is spatially and visually constrained, in particular lacking a distant visual panorama, which under natural conditions is crucial for the range over which rotational image difference functions provide navigational guidance. In addition, the array of identical landmarks is not representative of natural clutter and, because it is visually repetitive, poses un-natural problems for view-based homing algorithms. This is the reason why the functions degrade so quickly from one position to the next (Figures 9-12), although it is not clear what these positions are (memory0-memory7).

In conclusion, I do not feel that I have learnt anything useful from this experiment; it does suggest, however, that to fully appreciate and understand the homing abilities of insects, there is no alternative but to investigate these abilities in the natural conditions in which they have evolved.

We respectfully disagree with the evaluation that our study does not provide new insights due to the controlled lab conditions. Both field and lab research are absolutely necessary and should feed each other. Dismissing the value of controlled lab experiments would overlook the contributions of previous lab-based research, which has significantly advanced our understanding of animal behaviour. It is only possible to precisely define the visual test environments under laboratory conditions and to identify the role of these components for the behaviour through targeted variation of individual components of the environment. These results should guide field-based experiments for validation.

Our lab settings are a kind of abstraction of natural situations focusing on those aspects that are at the centre of the research question. Our approach here was that bumblebees have to find their inconspicuous nest hole in nature, which is difficult to find in often highly dense environments, and ultimately on a spatial scale in the metre range. We first wanted to find out if bumblebees can find their nest hole under the particularly challenging condition that all objects surrounding the nest hole are the same. This was not yet clear. Uniformly distributed objects may, however, also occur in nature, as seen with visually inconspicuous nest entrances of bumblebees in grass meadows, flower meadows, or forests with similar plants. We agree that the term "clutter" is not well-defined in the literature and will refer to our environment as a "dense environment."

Despite the lack of a distant visual panorama, or also UV light, wind, or other confounding factor inherent to field work, the bees successfully located the nest position even when we shifted the dense environment within the flight arena. We used rotational-image difference functions based on snapshots taken around the nest position to predict the bees' behaviour, as this is one of the most widely accepted and computationally most parsimonious

mechanisms for homing. This approach also proved effective in our more restricted conditions, where the bees still managed to pinpoint their home.

Author response:

The following is the authors’ response to the original reviews

Reviewer 1 (Public Review):

Summary:

In this paper, the authors aimed to test the ability of bumblebees to use bird-view and ground-view for homing in cluttered landscapes. Using modelling and behavioural experiments, the authors showed that bumblebees rely most on ground-views for homing.

Strengths:

The behavioural experiments are well-designed, and the statistical analyses are appropriate for the data presented.

Weaknesses:

Views of animals are from a rather small catchment area.

Missing a discussion on why image difference functions were sufficient to explain homing in wasps (Murray and Zeil 2017).

The artificial habitat is not really 'cluttered' since landmarks are quite uniform, making it difficult to infer ecological relevance.

Thank you for your thorough evaluation of our study. We aimed to investigate local homing behaviour on a small spatial scale, which is ecologically relevant given that the entrance of bumblebee nests is often inconspicuously hidden within the vegetation. This requires bees to locate their nest hole within a confined area. While many studies have focused on larger spatial scales using radar tracking (e.g. Capaldi et al. 2000; Osborne et al. 2013; Woodgate et al. 2016), there is limited understanding of the mechanisms behind local homing, especially in dense environments as we propose here.

We appreciate your suggestion to include the study by Murray and Zeil (2017) in our discussion. Their research explored the catchment areas of image difference functions on a larger spatial scale with a cubic volume of 5m x 5m x 5m. Aligned with their results, we found that image difference functions pointed towards the location of the objects surrounding the nest when the images were taken above the objects. However, within the clutter, i.e. the dense set of objects surrounding the nest, the model did not perform well in pinpointing the nest position.

See the new discussion at lines 192-197

We agree with your comment about the term "clutter". Therefore, we referred to our landmark arrangement as a "dense environment" instead. Uniformly distributed objects do indeed occur in nature, as seen in grasslands, flower meadows, or forests populated with similar plants.

See line 20 and we changed the wording throughout the manuscript and figures.

Reviewer 1 (Recommendations): 

The manuscript is well written, nicely designed experiments and well illustrated. I have a few comments below.

It would be useful to discuss known data of learning flights in bumblebees, and the height or catchment area of their flights. This will allow the reader to compare your exp design to the natural learning flights.

In our study, we first focused on demonstrating the ability to solve a homing task in a dense environment. As we observed the bees returning within the dense environment and not from above it (contrary to the model predictions), we investigated whether they flew above it during their first flights. The bees did indeed fly above, demonstrating their ability to ascend and descend within the constellation of objects (see Supplementary Material Fig. 22).

In nature, the learning flight of bumblebees may cover several decametres, with the loops performed during these flights increasing with flight time (e.g. Osborne et al. 2013; Woodgate et al. 2016). A similar pattern can be observed on a smaller spatial scale (e.g. Philippides et al. 2013). Similar to the loops that extend over time, the bees gradually gain altitude (Lobecke et al., 2018). However, these observations come from studies where few conspicuous objects surround the nest entrance.

Although our study  focussed on the performance in goal finding in cluttered environments, we now also address the issue of learning flights in the discussion, as learning flights are the scaffolding of visual learning. We have already conducted several learning flight experiments to fill the knowledge gap mentioned above. These will allow us in a forthcoming paper to compare learning flights in this environment with the existing literature (Sonntag et al., 2024).

We added a reference to this in the discussion (lines 218-219 and 269-272)

Include bumblebee in the title rather than 'bees'.

We adapted the title accordingly:

“Switching perspective: Comparing ground-level and bird’s-eye views for bumblebees navigating dense environments”

I found switching between bird-views and frog-views to explain bee-views slightly tricky to read. Why not use 'ground-views', which you already have in the title?

We agree and adapted the wording in the manuscript according to this suggestion.

I am not convinced there is evidence here to suggest the bees do not use view-based navigation, because of the following: In L66: unclear what were the views centred around, I assume it is the nest. Is 45cm above the ground the typical height gained by bumblebees during learning flight? The clutter seems to be used more as an obstacle that they are detouring to reach the goal, isn't it?

Based on many previous studies, view-based navigation can be assumed to be one of the plausible mechanisms bees use for homing (Cartwright & Collett, 1987; Doussot et al., 2020; Lehrer & Collett, 1994; Philippides et al., 2013; Zeil, 2022). In our tests, when the dense environment was shifted to a different position in the flight arena, almost no bees searched at the real location of the nest entrance but at the fictive new location within the dense environment, indicating that the bees assumed  the nest to be located within the dense environment, and therefore  that vision played a crucial role for homing. We thus never meant that the bees were not using view-based navigation. We clarified this point in the revised manuscript.

See lines 247-248, 250-259, added visual memory to schematic in Fig. 6

In our model simulations, the memorised snapshots were centred around the nest. However, we found that a multi-snapshot model could not explain the behaviour of the bees. This led us to suggest that bees likely employ acombination of multiple mechanisms for navigation.

We refined paragraph about possible alternative homing mechanisms. See lines  218-263

The height of learning flights has not been extensively investigated in previous studies, and typical heights are not well-documented in the literature. However, from our observations of the first outbound flights of bumblebees within the dense environment, we noted that they quickly increased their altitude and then flew above the objects. Since the objects had a height of 0.3 metres, we chose 0.45 metres as a height above the objects for our study.

Furthermore, the nest is positioned within the arrangement of objects, making it a target the bees must actively find rather than detour around.

I think a discussion to contrast your findings with Murray and Zeil 2017 will be useful. It was unclear to me whether the flight arena had UV availability, if it didn't, this could be a reason for the difference.

We referred to this study in the discussion of the revised paper (see our response to the public review). Lines 192-197

As in most lab studies on local homing, the bees did not have UV light available in the arena. Even without this, they were successful in finding their nest position during the tests. We clarified that in the revised manuscript. See line 334-336

Figure 2A, can you add a scale bar?

We added a scale bar to the figure showing the dimensions of the arena. See Fig. 2

The citation of figure orders is slightly off. We have Figure 5 after Figure 2, without citing Figures 3 and 4. Similarly for a few others.

We carefully checked the order of cited figures and adapted them.

Reviewer 2 (Public Review):

Summary:

In a 1.5m diameter, 0.8m high circular arena bumblebees were accustomed to exiting the entrance to their nest on the floor surrounded by an array of identical cylindrical landmarks and to forage in an adjacent compartment which they could reach through an exit tube in the arena wall at a height of 28cm. The movements of one group of bees were restricted to a height of 30cm, the height of the landmark array, while the other group was able to move up to heights of 80cm, thus being able to see the landmark array from above.

During one series of tests, the flights of bees returning from the foraging compartment were recorded as they tried to reach the nest entrance on the floor of the arena with the landmark array shifted to various positions away from the true nest entrance location. The results of these tests showed that the bees searched for the net entrance in the location that was defined by the landmark array.

In a second series of tests, access to the landmark array was prevented from the side, but not from the top, by a transparent screen surrounding the landmark array. These tests showed that the bees of both groups rarely entered the array from above, but kept trying to enter it from the side.

The authors express surprise at this result because modelling the navigational information supplied by panoramic snapshots in this arena had indicated that the most robust information about the location of the nest entrance within the landmark array was supplied by views of the array from above, leading to the following strong conclusions: line 51: "Snapshot models perform best with bird's eye views"; line 188: "Overall, our model analysis could show that snapshot models are not able to find home with views within a cluttered environment but only with views from above it."; line 231: "Our study underscores the limitations inherent in snapshot models, revealing their inability to provide precise positional estimates within densely cluttered environments, especially when compared to the navigational abilities of bees using frog's-eye views."

Strengths:

The experimental set-up allows for the recording of flight behaviour in bees, in great spatial and temporal detail. In principle, it also allows for the reconstruction of the visual information available to the bees throughout the arena.

The experimental set-up allows for the recording of flight behaviour in bees, in great spatial and temporal detail. In principle, it also allows for the reconstruction of the visual information available to the bees throughout the arena.

Weaknesses:

Modelling:

Modelling left out information potentially available to the bees from the arena wall and in particular from the top edge of the arena and cues such as cameras outside the arena. For instance, modelled IDF gradients within the landmark array degrade so rapidly in this environment, because distant visual features, which are available to bees, are lacking in the modelling. Modelling furthermore did not consider catchment volumes, but only horizontal slices through these volumes.

When we started modelling the bees’ homing based on image-matching, we included the arena wall. However, the model simulations pointed only coarsely towards the dense environment but not toward the nest position. We hypothesised that the arena wall and object location created ambiguity. Doussot et al. (2020) showed that such a model can yield two different homing locations when distant and local cues are independently moved. Therefore, we reduced the complexity of the environment by concentrating on the visual features, which were moved between training and testing (neither the camera nor the wall were moved between training and test). We acknowledge that this information should have been provided to substantiate our reasoning. As such, we included model results with the arena wall in the supplements of the revised paper. See lines 290-293, Figures S17-21

We agree that the catchment volumes would provide quantitatively more detailed information as catchment slices. Nevertheless, since our goal was  to investigate if bees would use ground views or bird's eye views to home in a dense environment, catchment slices, which provide qualitatively similar information as catchment volumes, are sufficient to predict whether ground or bird's-eye views perform better in leading to the nest. Therefore, we did not include further computations of catchment volumes. (ll. 296-297)

Behavioural analysis:

The full potential of the set-up was not used to understand how the bees' navigation behaviour develops over time in this arena and what opportunities the bees have had to learn the location of the nest entrance during repeated learning flights and return flights.

Without a detailed analysis of the bees' behaviour during 'training', including learning flights and return flights, it is very hard to follow the authors' conclusions. The behaviour that is observed in the tests may be the result of the bees' extended experience shuttling between the nest and the entry to the foraging arena at 28cm height in the arena wall. For instance, it would have been important to see the return flights of bees following the learning flights shown in Figure 17. Basically, both groups of bees (constrained to fly below the height of landmarks (F) or throughout the height of the arena (B)) had ample opportunities to learn that the nest entrance lies on the floor of the landmark array. The only reason why B-bees may not have entered the array from above when access from the side was prevented, may simply be that bumblebees, because they bumble, find it hard to perform a hovering descent into the array.

A prerequisite for studying the learning flight in a given environment is showing that the bees manage to return to their home. Here, our primary goal was to demonstrate this within a dense environment. While we understand that a detailed analysis of the learning and return flights would be valuable, we feel this is outside the scope of this particular study.

Multi-snapshot models have been repeatedly shown to be sufficient to explain the homing behaviour in natural as well as artificial environments(Baddeley et al., 2012; Dittmar et al., 2010; Doussot et al., 2020; Möller, 2012; Wystrach et al., 2011, 2013; Zeil, 2012). A model can not only be used to replicate but also to predict a given outcome and shape the design of experiments. Here, we used the models to shape the experimental design, as it does not require the entire history of the bee's trajectory to be tested and provides interesting insight into homing in diverse environments.

Since we observed behavioural responses different from the one suggested by the models, it becomes interesting to look at the flight history. If we had found an alignment between the model and the behaviour, looking at thehistory would have become much less interesting. Thus our results raise an interest in looking at the entire flight history, which will require not only effort on the recording procedure, but as well conceptually. At the moment the underlying mechanisms of learning during outbound, inbound, exploration, or orientation flight remains evasive and therefore difficult to test a hypothesis. A detailed description of the flight during the entire bee history would enable us to speculate alternative models to the one tested in our study, but would remain limited in testing those.

While we acknowledge that the bees had ample opportunities to learn the location of the nest entrance, we believe that their behaviour of entering the dense environment at a very low altitude cannot be solely explained by extended experience. It is possible that the bees could have also learned to enter at the edge of the objects or above the objects before descending within the dense environment.

General:

The most serious weakness of the set-up is that it is spatially and visually constrained, in particular lacking a distant visual panorama, which under natural conditions is crucial for the range over which rotational image difference functions provide navigational guidance. In addition, the array of identical landmarks is not representative of natural clutter and, because it is visually repetitive, poses un-natural problems for view-based homing algorithms. This is the reason why the functions degrade so quickly from one position to the next (Figures 9-12), although it is not clear what these positions are (memory0-memory7).

In conclusion, I do not feel that I have learnt anything useful from this experiment; it does suggest, however, that to fully appreciate and understand the homing abilities of insects, there is no alternative but to investigate these abilities in the natural conditions in which they have evolved.

We respectfully disagree with the evaluation that our study does not provide new insights due to the controlled laboratory conditions. Both field and laboratory research are necessary and should complement each other. Dismissing the value of controlled lab experiments would overlook the contributions of previous lab-based research, which has significantly advanced our understanding of animal behaviour. It is only possible to precisely define the visual test environments under laboratory conditions and to identify the role of the components of the environment for the behaviour through targeted variation of them. These results yield precious information to then guide future field-based experiments for validation.

Our laboratory settings are a kind of abstraction of natural situations focusing on those aspects that are at the centre of the research question. Our approach here was based on the knowledge that bumblebees have to find their inconspicuous nest hole in nature, which is difficult to find in often highly dense environments, and ultimately on a spatial scale in the metre range. We first wanted to find out if bumblebees can find their nest hole under the particularly challenging condition that all objects surrounding the nest hole are the same. This was not yet clear. Uniformly distributed objects may, however, also occur in nature, as seen with visually inconspicuous nest entrances of bumblebees in grass meadows, flower meadows, or forests with similar plants. We agree that the term "clutter" is not well-defined in the literature and now refer to the  environment as a "dense environment."

We changed the wording throughout the manuscript and figures.

Despite the lack of a distant visual panorama, or also UV light, wind, or other confounding factors inherent to field work conditions, the bees successfully located the nest position even when we shifted the dense environment within the flight arena. We used rotational-image difference functions based on snapshots taken around the nest position to predict the bees' behaviour, as this is one of the most widely accepted and computationally most parsimonious assessments of catchment areas in the context of local homing. This approach also proved effective in our more restricted conditions, where the bees still managed to pinpoint their home.

Reviewer 2 (Recommendations):

(1) Clarify what is meant by modelling panoramic images at 1cm intervals (only?) along the x-axis of the arena.

The panoramic images were taken along a grid with 0.5cm steps within the dense environment and 1cm steps in the rest of the arena. A previous study (Doussot et al., 2020) showed successful homing of multi-snapshot models in an environment of similar scale with a grid with 2cm steps. Therefore, we think that our scaling is sufficiently fine. We apologise for the missing information in the method section and added it to the revised manuscript. See lines 286-287

(2) In Figures 9-12 what are the memory0 to memory7 locations and reference image orientations? Explain clearly which image comparisons generated the rotIDFs shown.

Memory 0 to memory 7 are examples of the eight memorised snapshots, which are aligned in the nest direction and taken around the nest. In the rotIDFs shown, we took memory 0 as a reference image, and compared the 7 others by rotating them against memory 0. We clarified that in the revised manuscript.

See revised figure caption in Fig. S9 – 16

(3) Figure 9 seems to compare 'bird's-eye', not 'frog's-eye' views.

We apologise for that mistake and carefully double-checked the figure caption.

See revised figure caption Fig. S9

(4) Why do you need to invoke a PI vector (Figure 6) to explain your results?

Since the bees were able to home in the dense environment without entering the object arrangement from above but from the side, image matching alone could not explain the bees’ behaviour. Therefore, we suggest, as an hypothesis for future studies, a combination of mechanisms such as a home vector. Other alternatives, perhaps without requiring a PI vector, may explain the bees’ behaviour, and we will welcome any future contributions from the scientific community.

References

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Capaldi, E. A., Smith, A. D., Osborne, J. L., Farris, S. M., Reynolds, D. R., Edwards, A. S., Martin, A., Robinson, G. E., Poppy, G. M., & Riley, J. R. (2000).

Ontogeny of orientation flight in the honeybee revealed by harmonic radar. Nature, 403. https://doi.org/10.1038/35000564

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Dittmar, L., Stürzl, W., Baird, E., Boeddeker, N., & Egelhaaf, M. (2010). Goal seeking in honeybees: Matching of optic flow snapshots? Journal of Experimental Biology, 213(17), 2913–2923. https://doi.org/10.1242/jeb.043737

Doussot, C., Bertrand, O. J. N., & Egelhaaf, M. (2020). Visually guided homing of bumblebees in ambiguous situations: A behavioural and modelling study. PLoS Computational Biology, 16(10). https://doi.org/10.1371/journal.pcbi.1008272

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Lobecke, A., Kern, R., & Egelhaaf, M. (2018). Taking a goal-centred dynamic snapshot as a possibility for local homing in initially naïve bumblebees. Journal of Experimental Biology, 221(2), jeb168674. https://doi.org/10.1242/jeb.168674

Möller, R. (2012). A model of ant navigation based on visual prediction. Journal of Theoretical Biology, 305, 118–130. https://doi.org/10.1016/j.jtbi.2012.04.022

Murray, T., & Zeil, J. (2017). Quantifying navigational information: The catchment volumes of panoramic snapshots in outdoor scenes. PLOS ONE, 12(10), e0187226. https://doi.org/10.1371/journal.pone.0187226

Osborne, J. L., Smith, A., Clark, S. J., Reynolds, D. R., Barron, M. C., Lim, K. S., & Reynolds, A. M. (2013). The ontogeny of bumblebee flight trajectories: From Naïve explorers to experienced foragers. PLoS ONE, 8(11). https://doi.org/10.1371/journal.pone.0078681

Philippides, A., de Ibarra, N. H., Riabinina, O., & Collett, T. S. (2013). Bumblebee calligraphy: The design and control of flight motifs in the learning and return flights of Bombus terrestris. Journal of Experimental Biology, 216(6), 1093–1104. https://doi.org/10.1242/jeb.081455

Sonntag, A., Lihoreau, M., Bertrand, O. J. N., & Egelhaaf, M. (2024). Bumblebees increase their learning flight altitude in dense environments. bioRxiv, 2024.10.14.618154. https://doi.org/10.1101/2024.10.14.618154

Woodgate, J. L., Makinson, J. C., Lim, K. S., Reynolds, A. M., & Chittka, L. (2016). Life-long radar tracking of bumblebees. PLoS ONE, 11(8). https://doi.org/10.1371/journal.pone.0160333

Wystrach, A., Mangan, M., Philippides, A., & Graham, P. (2013). Snapshots in ants? New interpretations of paradigmatic experiments. Journal of Experimental Biology, 216(10), 1766–1770. https://doi.org/10.1242/jeb.082941

Wystrach, A., Schwarz, S., Schultheiss, P., Beugnon, G., & Cheng, K. (2011). Views, landmarks, and routes: How do desert ants negotiate an obstacle course? Journal of Comparative Physiology A: Neuroethology, Sensory, Neural, and Behavioral Physiology, 197(2), 167–179. https://doi.org/10.1007/s00359-010-0597-2

Zeil, J. (2012). Visual homing: An insect perspective. Current Opinion in Neurobiology, 22(2), 285–293. https://doi.org/10.1016/j.conb.2011.12.008

Zeil, J. (2022). Visual navigation: Properties, acquisition and use of views. Journal of Comparative Physiology A. https://doi.org/10.1007/s00359-022-01599-2

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

Summary:

The manuscript titled "Household clustering and seasonal genetic  variation of Plasmodium falciparum at the community-level in The Gambia" presents a valuable genetic spatio-temporal analysis of  malaria-infected individuals from four villages in The Gambia, covering  the period between December 2014 and May 2017. The majority of samples  were analyzed using a SNP barcode with the Spotmalaria panel, with a  subset validated through WGS. Identity-by-descent (IBD) was calculated  as a measure of genetic relatedness and spatio-temporal patterns of the  proportion of highly related infections were investigated. Related  clusters were detected at the household level, but only within a short  time period.

Strengths:

This study offers a valuable dataset, particularly due to its  longitudinal design and the inclusion of asymptomatic cases. The  laboratory analysis using the Spotmalaria platform combined and  supplemented with WGS is solid, and the authors show a linear  correlation between the IBD values determined with both methods,  although other studies have reported that at least 200 SNPs are required for IBD analysis. Data-analysis pipelines were created for (1) variant  filtering for WGS and subsequent IBD analysis, and (2) creating a  consensus barcode from the spot malaria panel and WGS data and  subsequent SNP filtering and IBD analysis.

Weaknesses:

Further refining the data could enhance its impact on both the scientific community and malaria control efforts in The Gambia.

(1) The manuscript would benefit from improved clarity and better  explanation of results to help readers follow more easily. Despite  familiarity with genotyping, WGS, and IBD analysis, I found myself  needing to reread sections. While the figures are generally clear and  well-presented, the text could be more digestible. The aims and  objectives need clearer articulation, especially regarding the rationale for using both SNP barcode and WGS (is it to validate the approach with the barcode, or is it to have less missing data?). In several analyses, the purpose is not immediately obvious and could be clarified.

The text of the manuscript has now been thoroughly revised. But please let us know if a specific section remains unclear.

(2) Some key results are only mentioned briefly in the text without  corresponding figures or tables in the main manuscript, referring only  to supplementary figures, which are usually meant for additional detail, but not main results. For example, data on drug resistance markers  should be included in a table or figure in the main manuscript.

We agree with the reviewer suggesting to move the prevalence of drug resistance markers from supplementary figures (previously Figure S8) to the main manuscript (now Figure 5). If other Figure/Table should be moved to the main manuscript please let us know.

(3) The study uses samples from 2 different studies. While these are  conducted in the same villages, their study design is not the same,  which should be addressed in the interpretation and discussion of the  results. Between Dec 2014 and Sept 2016, sampling was conducted only in 2 villages and at less frequent intervals than between Oct 2016 to May  2017. The authors should assess how this might have impacted their  temporal analysis and conclusions drawn. In addition, it should be  clarified why and for exactly in which analysis the samples from Dec  2016 - May 2017 were excluded as this is a large proportion of your  samples.

We have clarified which set of samples was used in our Results (Lines 293-295, 316-319). While two villages were recruited halfway through the study, two villages (J and K, Figure 1C) consistently provided data for each transmission season. Importantly, our temporal analysis accounts for these differences by grouping paired barcodes based on their respective locations (Figure 3B). Despite variations in sampling frequency, we still observe a clear overall decline in relatedness between the ‘0-2 months’ and ‘2-5 months’ groups, both of which include barcodes from all four villages.

(4) Based on which criteria were samples selected for WGS? Did the  spatiotemporal spread of the WGS samples match the rest of the genotyped samples? I.e. were random samples selected from all times and places,  or was it samples from specific times/places selected for WGS?

All P. falciparum positive samples were sent for genotyping and whole genome sequencing, ensuring no selection bias. However, only samples with sufficient parasite DNA were successfully sequenced. We have updated the text (Line 129-130) and added a supplementary figure (Figure S4) to show the sample collection broken down by type of data (barcode or genome). High quality genomes are distributed across all time points.

(5) The manuscript would benefit from additional detail in the methods section.

Please see our response in the section “Recommendation for the authors”.

(6) Since the authors only do the genotype replacement and build  consensus barcode for 199 samples, there is a bias between the samples  with consensus barcode and those with only the genotyping barcode. How  did this impact the analysis?

While we acknowledge the potential for bias between samples with a consensus barcode (based on WGS) and those with genotyping-only barcodes, its impact is minimal. WGS does indeed produce a more accurate barcode compared to SNP genotyping, but any errors in the genotyping barcodes were mitigated by excluding loci that systematically mismatched with WGS data (see Figure S3). Additionally, the use of WGS improved the accuracy of 51 % (216/425) of barcodes, which strengthens the overall quality and validity of our analysis.

(7) The linear correlation between IBD-values of barcode vs genome is  clear. However, since you do not use absolute values of IBD, but a  classification of related (>=0.5 IBD) vs. unrelated (<0.5), it  would be good to assess the agreement of this classification between the 2 barcodes. In Figure S6 there seem to be quite some samples that would be classified as unrelated by the consensus barcode, while they have  IBD>0.5 in the Genome-IBD; in other words, the barcode seems to be  underestimating relatedness.

a. How sensitive is this correlation to the nr of SNPs in the barcode?

We measured the agreement between the two classifications using specificity (0.997), sensitivity (0.841) and precision (0.843) described in the legend of Figure S8. To further demonstrate the good agreement between the two methods, we calculated a Cohen’s kappa value of 0.839 (Lines 226, 290), indicative of a strong agreement (McHugh 2012). As expected, the correlation between IBD values obtained by both methods improves (higher Cohen’s kappa and R²) as the cutoff for the minimal number of comparable and informative loci per barcode pair is raised (data not shown).

(8) With the sole focus on IBD, a measure of genetic relatedness, some of the conclusions from the results are speculative.

a. Why not include other measures such as genetic diversity, which  relates to allele frequency analysis at the population level (using, for example, nucleotide diversity)? IBD and the proportion of highly  related pairs are not a measure of genetic diversity. Please revise the  manuscript and figures accordingly.

We agree with the fact that IBD is not a direct measure of genetic diversity, even though both are related (Camponovo et al., 2023). More precisely, IBD is a measure of the level of inbreeding in the population (Taylor et al., 2019). We have updated our manuscript by replacing “genetic diversity” with “genetic relatedness” or “inbreeding/outcrossing” when appropriate. Nucleotide diversity would be relevant if we wanted to compare different settings, e.g. Africa vs Asia, however this is not the case here.

b. Additionally, define what you mean by "recombinatorial genetic  diversity" and explain how it relates to IBD and individual-level  relatedness.

We considered the term ‘recombinatorial genetic diversity’ to be equivalent to the level of inbreeding in the population. Because this expression is rather uncommon, we decided to drop it from our manuscript and replace it with “inbreeding/outcrossing”.

c. Recombination is one potential factor contributing to the loss of  relatedness over time. There are several other factors that could  contribute, such as mobility/gene flow, or study-specific limitations  such as low numbers of samples in the low transmission season and many  months apart from the high transmission samples.

Indeed, the loss of relatedness could be attributed not only to the recombination of local cases but also to new parasites introduced by imported malaria cases. As we stated in our manuscript, previous studies have shown a limited effect of imported cases on maintaining transmission (Lines 72-74). Nevertheless, we cannot definitely exclude that imported cases have an effect on inbreeding levels, since we do not have access to genetic data of surrounding parasites at the time of the study. We updated the discussion accordingly (Lines 497-501).

d. By including other measures such as linkage disequilibrium you could  further support the statements related to recombination driving the loss of relatedness.

This commendable suggestion is actually part of an ongoing project focusing on the sharing of IBD fragments and how it correlates with linkage disequilibrium. However, we believe that this analysis would not fit in the scope of our manuscript which is really about spatio-temporal effects on parasite relatedness at a local scale.

(9) While the authors conclude there is no seasonal pattern in the  drug-resistant markers, one can observe a big fluctuation in the dhps  haplotypes, which go down from 75% to 20% and then up and down again  later. The authors should investigate this in more detail, as dhps is  related to SP resistance, which could be important for seasonal malaria  chemoprofylaxis, especially since the mutations in dhfr seem near-fixed  in the population, indicating high levels of SP resistance at some of  the time points.

As the reviewer noted, the DHPS A437G haplotype appears to decrease in prevalence twice throughout our study: from the 2015 and 2016 high transmission seasons to the subsequent 2016 and 2017 low transmission seasons. Seasonal Malaria Chemoprophylaxis (SMC) was carried out in the area through the delivery of sulfadoxine–pyrimethamine plus amodiaquine to children 5 years old and younger during high transmission seasons. As DHPS A437G haplotype has been associated with resistance to sulfadoxine, its apparent increase in prevalence during high transmission seasons could be resulting from the selective pressure imposed on parasites. After SMC, the decrease in prevalence observed during low transmission seasons could be caused by a fitness cost of the mutation favouring wild-type parasites over resistant ones. We updated our manuscript to reflect this relevant observation (Lines 400-405).

(10) I recommend that raw data from genotyping and WGS should be deposited in a public repository.

Genotyping data is available in the supplementary table 4 (Table S4). Whole genome sequencing is accessible in a European Nucleotide Archive public repository with the identifiers provided in supplementary table 5 (Table S5). We added references to these tables in the manuscript (Lines 249-250).

Reviewer #2 (Public review):

Summary:

Malaria transmission in the Gambia is highly seasonal, whereby periods  of intense transmission at the beginning of the rainy season are  interspersed by long periods of low to no transmission. This raises  several questions about how this transmission pattern impacts the  spatiotemporal distribution of circulating parasite strains. Knowledge  of these dynamics may allow the identification of key units for targeted control strategies, the evaluation of the effect of selection/drift on  parasite phenotypes (e.g., the emergence or loss of drug resistance  genotypes), and analyze, through the parasites' genetic nature, the  duration of chronic infections persisting during the dry season. Using a combination of barcodes and whole genome analysis, the authors try to  answer these questions by making clever use of the different  recombination rates, as measured through the proportion of genomes with  identity-by-descent (IBD), to investigate the spatiotemporal relatedness of parasite strains at different spatial (i.e., individual, household,  village, and region) and temporal (i.e., high, low, and the  corresponding the transitions) levels. The authors show that a large  fraction of infections are polygenomic and stable over time, resulting  in high recombinational diversity (Figure 2). Since the number of  recombination events is expected to increase with time or with the  number of mosquito bites, IBD allows them to investigate the  connectivity between spatial levels and to measure the fraction of  effective recombinational events over time. The authors demonstrate the  epidemiological connectivity between villages by showing the presence of related genotypes, a higher probability of finding similar genotypes  within the same household, and how parasite-relatedness gradually  disappears over time (Figure 3). Moreover, they show that transmission  intensity increases during the transition from dry to wet seasons  (Figure 4). If there is no drug selection during the dry season and if  resistance incurs a fitness cost it is possible that alleles associated  with drug resistance may change in frequency. The authors looked at the  frequencies of six drug-resistance haplotypes (aat1, crt, dhfr, dhps,  kelch13, and mdr1), and found no evidence of changes in allele  frequencies associated with seasonality. They also find chronic  infections lasting from one month to one and a half years with no  dependence on age or gender.

The use of genomic information and IBD analytic tools provides the  Control Program with important metrics for malaria control policies, for example, identifying target populations for malaria control and  evaluation of malaria control programs.

Strength:

The authors use a combination of high-quality barcodes (425 barcodes  representing 101 bi-allelic SNPs) and 199 high-quality genome sequences  to infer the fraction of the genome with shared Identity by Descent  (IBD) (i.e. a metric of recombination rate) over several time points  covering two years. The barcode and whole genome sequence combination  allows full use of a large dataset, and to confidently infer the  relatedness of parasite isolates at various spatiotemporal scales.

Reviewer #3 (Public review):

Summary

This study aimed to investigate the impact of seasonality on the malaria parasite population genetic. To achieve this, the researchers conducted a longitudinal study in a region characterized by seasonal malaria  transmission. Over a 2.5-year period, blood samples were collected from  1,516 participants residing in four villages in the Upper River Region  of The Gambia and tested the samples for malaria parasite positivity.  The parasites from the positive samples were genotyped using a genetic  barcode and/or whole genome sequencing, followed by a genetic  relatedness analysis.

The study identified three key findings:

(1) The parasite population continuously recombines, with no single genotype dominating, in contrast to viral populations;

(2) The relatedness of parasites is influenced by both spatial and temporal distances; and

(3) The lowest genetic relatedness among parasites occurs during the  transition from low to high transmission seasons. The authors suggest  that this latter finding reflects the increased recombination associated with sexual reproduction in mosquitoes.

The results section is well-structured, and the figures are clear and  self-explanatory. The methods are adequately described, providing a  solid foundation for the findings. While there are no unexpected  results, it is reassuring to see the anticipated outcomes supported by  actual data. The conclusions are generally well-supported; however, the  discussion on the burden of asymptomatic infections falls outside the  scope of the data, as no specific analysis was conducted on this aspect  and was not stated as part of the aims of the study. Nonetheless, the  recommendation to target asymptomatic infections is logical and  relevant.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) The manuscript would benefit from additional detail in the methods section.

a. Refer to Figure 1 when you describe the included studies and sample processing.

We added the reference to Figure 1 (Line 131).

b. While you describe each step in the pipeline, you do not specify the  tools, packages, or environment used (the GitHub link is also  non-functional). A graphic representation of the pipeline, with more  bioinformatic details than Supplementary Figure S1, would be helpful.  Add references to used tools and software created by others.

The GitHub link has been updated and is now functional. We find Figure S1 already heavy in details, adding in more would be detrimental to our will of it being an easily readable summary of our pipeline. Readers seeking in-depth explanation of our pipeline might be more interested in reading the methods section instead. We are very much committed to credit the authors of the tools that were essential for us to create our analysis pipeline. The two most relevant tools that we used are hmmIBD and the Fws calculation, which were both cited in the methods (Lines 148-152, 214-215).

c. What changed in the genotyping protocol after May 2016? Does it not  lead to bias in the (temporal) analysis by leaving these loci in for  samples collected before May 2016 and making them 'unknown' for the  majority of samples collected after this date?

These 21 SNPs all clustered in 1 of the 4 multiplexes used for molecular genotyping, which likely failed to produce accurate base calls. We updated the text to include this information (Lines 198-200).

The rationale behind the discarding of these 21 SNPs for barcodes sampled after May 2016 was that they were consistently mismatching with the WGS SNPs, probably due to genotyping error as mentioned above. However, by replacing these unknown positions in the molecular barcodes with WGS SNPs, 141 samples did recover some of these 21 SNPs with the accurate base calls (Figure S3A). Additionally, we added an extra analysis to assess the agreement between barcodes and WGS data (Figure S3B).

d. Related to this, how are unknown and mixed genotypes treated in the  binary matrix? How is the binary matrix coded? Is 0 the same as the  reference allele? So all the missing and mixed are treated as  references? How many missing and mixed alleles are there, how often does it occur and how does this impact the IBD analysis?

We acknowledge that the details that we provided regarding the IBD analysis were confusing. hmmIBD requires a matrix that contains positive or null integers for each different allele at a given loci (all our loci were bi-allelic, thus only 0 and 1 were used) and -1 for missing data. In our case, we set missing and mixed alleles to -1, which were then ignored during the IBD estimation. The corresponding text was updated accordingly (Lines 173-175).

e. By excluding households with less than 5 comparisons, are you not preselecting households with high numbers of cases, and therefore higher likelihood of transmission within the household?

All participants in each household were sampled at every collection time point. This sampling was unbiased towards likelihood of transmission. Excluding pairs of households with less than 5 comparisons was necessary to ensure statistical robustness in our analyses. Besides, this does not necessarily restrict the analysis to only households with a high number of cases as it is the total number of pairs between households that must equal 5 at least (for instance these pairs would pass the cutoff: household with 1 case vs household with 5 cases; household with 2 cases vs household with 3 cases).

(2) Since the authors only do the genotype replacement and build  consensus barcode for 199 samples, there is a bias between the samples  with consensus barcode and those with only the genotyping barcode. How  did this impact the analysis?

See (6) in the Public Review.

a. It would be good to get a better sense of the distribution of the nr  of SNPs in the barcode. The range is 30-89, and 30 SNPs for IBD is  really not that much.

Adding the range of the number of available SNPs per barcode is indeed particularly relevant. We added a supplementary figure (Figure S5) showing the distribution of homozygous SNPs per barcode, showing that a very small minority of barcodes have only 30 SNPs available for IBD (average of 65, median of 64).

b. Did you compare the nr of SNPs in the consensus vs. only genotyped  barcodes? Is there more missing data in the genotype-only barcodes?

We added a supplementary figure (Figure S5) with the distribution of homozygous SNPs in consensus (216 samples) and molecular (209 samples) barcodes. Consensus barcodes have more homozygous SNPs (average 76, median 82) than molecular barcodes (average of 54, median of 53), showing the improvement resulting from using whole genome sequencing data.

c. How was the cut-off/sample exclusion criteria of 30 SNPs in the barcode determined?

As described above (Public review section 7.a.), we removed pairs of barcodes with less than 30 comparable loci (and 10 informative loci) because this led to a good agreement between IBD values obtained from barcodes and genomes while still retaining a majority of pairwise IBD values.

d. Was there more/less IBD between sample pairs with a consensus barcode vs those with genotype-only barcodes?

We separated pairwise IBD values into two groups: “within consensus” and “within molecular”. The percentages of related barcodes (IBD ≥ 0.5) was virtually identical between “within consensus” (1.88 %) and “within molecular” (1.71 %) groups (χ² = 1.33, p value > 0.24).

(3) Line 124 adds a reference for the PCR method used.

We have updated this information: varATS qPCR (Line 121).

(4) Line 126, what is MN2100ff? Is this the catalogue number of the  cellulose columns? Please clarify and add manufacturer details.

MN2100ff was a replacement for CF11. We added a link to the MalariaGen website describing the product and the procedure (Lines 124-125).

(5) Line 143: Figure S7 is the first supplementary figure referenced. Change the order and make this Figure S1?

The numbering of figures is now fixed.

(6) Line 154: How many SNPs were in the vcf before filtering?

There were 1,042,186 SNPs before filtering. This information was added to the methods (Line 168).

(7) Line 156: Why is QUAL filtered at 10000? This seems extremely high.  (I could be mistaken, but often QUAL above 50 or so is already fine, why discard everything below 10000?). What is the range of QUAL scores in  your vcf?

We used the QUAL > 10000 to make our analyses less computationally intensive while keeping enough relevant genetic information. We agree that keeping variants with extremely high values of QUAL is not relevant above a certain threshold as it translates into infinitesimally low probabilities (10^-(QUAL/10)) of the variant calling being wrong. We then decided to use a minimal population minor allele frequency (MAF) of 0.01 to keep a variant as this will make the IBD calculation more accurate (Taylor et al., 2019). The variant filtering was carried out with the MAF > 0.01 filter, resulting in 27,577 filtered SNPs with a minimal QUAL of 132. With a cutoff of 3000 available SNPs, we retrieved all 199 genomes previously obtained with the QUAL > 10000 condition. The methods have been updated accordingly (Lines 166-170).

(8) Line 161-165: How did you handle the mixed alleles in the hmmIBD  analysis for the WGS data? Did you set them as 0 as you do later on for  the consensus barcode?

Mixed alleles and missing data were ignored. This translated into a value of -1 for the hmmIBD matrix and not 0 as we incorrectly stated previously. We updated our manuscript with this correct information (Lines 173-175).

(9) Line 168-171: How many SNPs do you have in the WGS dataset after all the filtering steps? If the aim of the IBD with WGS was to validate the IBD-analysis with the barcode, wouldn't it make sense to have at least  200 loci (as shown in Taylor et al to be required for hmmIBD) in the WGS data? What proportion of comparisons were there with only 100 pairs of  loci? This seems like really few SNPs from WGS data.

There were 27,577 SNPs overall in the 199 high quality genomes. In our analysis, we make the distinction between comparable and informative loci. For two loci to be comparable, they both have to be homozygous. To be informative, they must be comparable and at least one of them must correspond to the minor allele in the population. We borrowed this term and definition from hmmIBD software which yields directly the number of informative loci per pair. By keeping pairs with at least 100 informative SNPs, we aimed to reduce the number of samples artificially related because only population major alleles are being compared. Pairs of genomes had between 1073 and 27466 of these, way above the recommended 200 loci in Taylor et al. (2019). We added more details on comparable and informative sites (Lines 152-160).

(10) Line 178: why remove the 12 loci that are absent from the WGS? Are  these loci also poorly genotyped in the spotmalaria panel?

As our goal is to validate the reliability of molecular genotyped SNPs, these 12 loci have to be removed. Especially because we did find a consistent discrepancy between genotyped and WGSed SNPs, which cannot be tested if these SNPs are absent from the genomes.

(11) Line 180-182: What do you mean by this sentence: "Genomic barcodes  are built using different cutoffs of within-sample MAF and aligned  against molecular barcodes from the same isolates." Is this the analysis presented in the supplementary figure and resulting in the cut-off of  MAF 0.2? Please clarify.

A loci where both alleles are called can result from two distinct haploïd genomes present or from an error occurring during sequencing data acquisition or processing. To distinguish between the two, we empirically determined the cutoff of within-sample MAF above which the loci can be considered heterozygous and below which only the major allele is kept. The corresponding figure was indeed Figure S2 (referenced in next sentence Lines 192-195). We clarified our approach in the methods (Lines 190-192) and legends of Figures S2 and Figure S3.

(12) Line 191: How often was there a mismatch between WGS and SNP barcode?

We added a panel (Figure S3B) showing the average agreement of each SNP between molecular genotyping and WGS. We highlighted the 21 discrepant SNPs showing a lower agreement only for samples collected after May 2016.

(13) Line 201-204: This part is unclear (as above for the WGS): did you  include sample pairs with more than 10 paired loci? But isn't 10 loci  way too few to do IBD analysis?

We included pairs of samples with at least 30 comparable loci and 10 informative paired loci (refer to our answer to comment 8 for the difference between the two). We added more details regarding comparable and informative sites (Lines 152-160). Indeed, using fewer than 200 loci leads to an IBD estimation that is on average off by 0.1 or more (Taylor et al., 2019). However we showed that the barcode relatedness classification based on a cutoff of IBD (related when above 0.5, unrelated otherwise) was close enough to our gold standard using genomes (each pair having more than 1000 comparable sites). Because we use this classification approach rather than the exact value of barcode-estimated IBD in our study, our 30 minimum comparable sites cutoff seems sufficient.

(14) Lines 206-207: which program did you use to analyse Fws?

We did not use any program, we computed Fws according to Manske et al. (2012) methods.

(15) Line 233: "we attempted parasite genotyping and whole genome  sequencing of 522 isolates over 16 time points" => This is confusing, you did not do WGS of 522 samples, only 199 as mentioned in the next  sentence.

We attempted whole genome sequencing on 331 isolates and molecular genotyping on 442 isolates with 251 isolates common between the two methods. We updated our text to clarify this point (Lines 247-252).

(16) Lines 256-259: Add a range of proportions or some other summary  statistic in this section as you are only referring here to  supplementary figures to support these statements.

The text has been updated (Lines 271-274).

(17) Line 260: check the formatting of the reference "Collins22" as the rest of the document references are numbered.

Fixed.

(18) Figure 2/3:

a. You could also inspect relatedness at the temporal level, by  adjusting the network figure where the color is village and shape is  time (month/year).

Although visualising the effect of time on the parasite relatedness network would be a valuable addition, we did not find any intuitive and simple way of doing so. Using shapes to represent time might end up being more confusing than helpful, especially because the sampling was not done at fixed intervals.

b. To further support the statement of clustering at the household  level, it might be useful to add a (supplementary) figure with the  network with household number/IDs as color or shape. In the network,  there seems to be a lot of relatedness within the villages and between  villages. Perhaps looking only at the distribution of the proportion of  highly related isolates is simplifying the data too much. Besides, there is no statistical difference between clustering at the household vs  within-village levels as indicated in Figure 3.

Unfortunately, there are too many households (71 in Figure 2) to make a figure with one color or shape per household readable. The statistical test of the difference between the within household and within village relatedness yielded a p value above the cutoff of 0.05 (p value of 0.084). However, it is possible that the lack of significance arises from the relatively low number of data points available in the “within household” group. This is even more plausible considering the statistical difference of both “within household” and “within village” groups with “between village” group. Overall, our results indicate a decreasing parasite relatedness with spatial distance, and that more investigation would be needed to quantify the difference between “within household” and “within village” groups. 

(19) Figure 4: Please add more description in the caption of this figure to help interpret what is displayed here. Figure 4A is hard to  interpret and does not seem to show more than is already shown in Figure 3A. What do the dots represent in Figure 4B? It is not clear what is  presented here.

Compared to Figure 3A, Figure 4A enables the visualization of the relatedness between each individual pair of time points, which are later used in the comparison of relatedness between seasonal groups in Figure 4B. For this reason, we believe that Figure 4A should remain in the manuscript. However, we agree that the relationship between Figure 4A and Figure 4B is not intuitive in the way we presented it initially. For this reason, we added more details in the legend and modified Figure 4A to highlight the seasonal groups used in Figure 4B. 

(20) Line 360-361: what did you do when haplotypes were not identical?

We explained it in the methods section (Lines 144-146): in this case, only WGS haplotypes were kept.

(21) Section chronic infections: it is important to mention that the  majority of chronic infections are individuals from the monthly  dry-season cohort.

We added a statement about the 21 chronically infected individuals that were also part of the December 2016 – May 2017 monthly follow-up (Lines 423-426).

(22) Lines 381-386: Did you investigate COI in these individuals? Could  it be co-circulating strains that you do not pick up at all times due to the consensus barcodes and discarding of mixed genotypes (and does not  necessarily show intra-host competition. That is speculation and should  perhaps not be in the results)?

This is exactly what we think is happening. Due to the very nature of genotyping, only one strain may be observed at a time in the case of a co-infection, where distinct but related strains are simultaneously present in the host. The picked-up strain is typically the one with the highest relative abundance at the time of sampling. As the reviewer stated, fluctuation of strain abundance might not only be due to intra-host competition but also asynchronous development stages of the two strains. We added this observation to the manuscript (Lines 432-435).

(22) Figure 6: highlight the samples where the barcode was not available in a different color to be able to see the difference between a  non-matching barcode and missing data.

We thank the reviewer for this great suggestion. We have now added to Figure 6 barcodes available along with their level of relatedness with the dominant genotypes for each continuous infections.

(24) Improve the discussion by adding a clear summary of the main  findings and their implications, as well as study-specific limitations.

The Discussion has been updated with a paragraph summarizing the primary results (Lines 451-457).

(25) Line 445: "implying that the whole population had been replaced in just one year "

a. What do you mean by replaced? Did other populations replace the  existing populations? I am not sure the lack of IBD is enough to show  that the population changed/was replaced. Perhaps it is more accurate to say that the same population evolved. Nevertheless, other measures such as genetic diversity and genetic differentiation or population  structure.would be more suitable to strengthen these conclusions.

We agree that “replaced” was the wrong term in this case. We rather intended to describe how the numerous recombinations between malaria parasites completely reshaped the same initial population which gradually displayed lower levels of relatedness over time. We updated the manuscript accordingly (Lines 507-512).

Reviewer #2 (Recommendations for the authors):

(1) Line 260: Remove Collins 22.

Fixed.

(2) Lines 270-274: 73 + 213 = 286 not 284; sum of percentages is equal to 101%.

The numbers are correct: the 73 barcodes identical (IBD >= 0.9) to another barcode are a subset of the 213 related (IBD >= 0.5) to another barcode. However we agree that this might be confusing and will considering barcodes to be related if they have an IBD between 0.5 and 0.9, while excluding those with an IBD >= 0.9. The text has been updated (Lines 299-301).

(3) Section: "Independence of seasonality and drug resistance markers prevalence".

The text has been revised and the supplementary figure is now a main figure.

(4) For readers unaware of malaria control policy in the Gambia it would be helpful to have more details on the specifics of anti-malarial drug  administration.

We added the drugs used in SMC (sulfadoxine-pyrimethamine and amodiaquine) and the first line antimalarial treatment in use in The Gambia during our study (Coartem) (Lines 383-388).

Reviewer #3 (Recommendations for the authors):

(1) The abstract is not as clear as the authors' summary. For example, I found the sentence starting with "with 425 P. falciparum..." hard to  follow.

The abstract has been updated.

(2) It is better to consistently use "barcode genotyping "or "genotyping by barcode". Sometimes "molecular genotyping" is used instead of  "barcode genotyping"

We have now replaced all occurrences of “barcode genotyping” with “molecular genotyping” or “molecular barcode genotyping”. We prefer to stick with “molecular genotyping” as this let us distinguish between the molecular and the genomic barcode.

(3) The introduction is quite disjoined and does not provide a clear  build-up to the gap in knowledge that the study is attempting to fill.  please revise.

Introduction is now thoroughly revised.

(4) Line 31 "with notable increase of parasite differentiation" is an interpretation and not an observation.

We have modified that sentence (Lines 31-33).

(5) Overall, the introduction requires substantial revision.

Introduction is now thoroughly revised.

(6) Line 70 "parasite population adapts..." I thought this required phenotypic analysis and not genetics?

The idea is that population of parasites may adapt to environmental conditions (such as seasonality) by selecting the most fitted genotypes. For instance, antimalarial exposure has an effect of selecting parasites with specific mutations in drug resistance related genes, and this even appears to be transient (for example with chloroquine). As such, there is good reason to think that seasonality might have a similar effect on parasite genetics.

(7) Line 129-130: the #442 is not reflected in the schematic Figure 1.

This is an intentional choice to make the figure more synthetic. For this reason, we included the Figure S1, which provides more details on the data collection and analysis pipeline.

(8) Line 242-243: "Made with natural earth". What is this?

This is a statement acknowledging the use of Natural Earth data to produce the map presented in Figure 1A.

(9) Line 260: "collins22", is this a reference?

Fixed.

(10) Line 269-70. Very hard to follow. Please revise.

We changed the text (Lines 293-297).

(11) Line 324: similarly... I think there is a typo here.

We did not find any typo in this specific sentence. However, “Similarly to Figure 3” sounds maybe a bit off, so we changed it to “As in Figure 3” (Line 351).

(12) Line 332-334: very hard to follow. please revise. Again, the lower  parasite relatedness during the transition from low to high was linked  to recombination occurring in the mosquito but what about infection  burden shifting to naive young children? Is there a role for host  immunity in the observed reduction in parasite-relatedness during the  transition period?

This text has been rewritten (Lines 356-361).

About the hypothesis of infection burden shifting to naïve young children, this question is difficult to address in The Gambia because children under 5 years old received Seasonal Malaria Chemoprophylaxis during the high transmission season. In older children (6-15 years old), the prevalence was similar to adults (Fogang et al., 2024).

About the role of host immunity on parasite relatedness across time and space, our dataset is too small to divide it in different age groups. Further studies should address this very interesting question.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

This paper examines changes in relaxation time (T1 and T2) and magnetization transfer parameters that occur in a model system and in vivo when cells or tissue are depolarized using an equimolar extracellular solution with different concentrations of the depolarizing ion K⁺. The motivation is to explain T2 changes that have previously been observed by the authors in an in vivo model with neural stimulation (DIANA) and to try to provide a mechanism to explain those changes.

Strengths:

The authors argue that the use of various concentrations of KCL in the extracellular fluid depolarize or hyperpolarize the cell pellets used and that this change in membrane potential is the driving force for the T2 (and T1-supplementary material) changes observed. In particular, they report an increase in T2 with increasing KCL concentration in the extracellular fluid (ECF) of pellets of SH-SY5Y cells. To offset the increasing osmolarity of the ECF due to the increase in KCL, the NaCL molarity of the ECF is proportionally reduced. The authors measure the intracellular voltage using patch clamp recordings, which is a gold standard. With 80 mM of KCL in the ECF, a change in T2 of the cell pellets of ~10 ms is observed with the intracellular potential recorded as about -6 mv. A very large T1 increase of ~90 ms is reported under the same conditions. The PSR (ratio of hydrogen protons on macromolecules to free water) decreases by about 10% at this 80 mM KCL concentration. Similar results are seen in a Jurkat cell line and similar, but far smaller changes are observed in vivo, for a variety of reasons discussed. As a final control, T1 and T2 values are measured in the various equimolar KCL solutions. As expected, no significant changes in T1 and T2 of the ECF were observed for these concentrations.

Weaknesses:

[Reviewer 1, Comment 1] While the concepts presented are interesting, and the actual experimental methods seem to be nicely executed, the conclusions are not supported by the data for a number of reasons. This is not to say that the data isn't consistent with the conclusions, but there are other controls not included that would be necessary to draw the conclusion that it is membrane potential that is driving these T1 and T2 changes. Unfortunately for these authors, similar experiments conducted in 2008 (Stroman et al. Magn. Reson. in Med. 59:700-706) found similar results (increased T2 with KCL) but with a different mechanism, that they provide definite proof for. This study was not referenced in the current work.

It is well established that cells swell/shrink upon depolarization/hyperpolarization. Cell swelling is accompanied by increased light transmittance in vivo, and this should be true in the pellet system as well. In a beautiful series of experiments, Stroman et al. (2008) showed in perfused brain slices that the cells swell upon equimolar KCL depolarization and the light transmittance increases. The time course of these changes is quite slow, of the order of many minutes, both for the T2-weighted MRI signal and for the light transmittance. Stroman et al. also show that hypoosmotic changes produce the exact same time course as the KCL depolarization changes (and vice versa for the hyperosmotic changes - which cause cell shrinkage). Their conclusion, therefore, was that cell swelling (not membrane potential) was the cause of the T2-weighted changes observed, and that these were relatively slow (on the scale of many minutes).

What are the implications for the current study? Well, for one, the authors cannot exclude cell swelling as the mechanism for T2 changes, as they have not measured that. It is however well established that cell swelling occurs during depolarization, so this is not in question. Water in the pelletized cells is in slow/intermediate exchange with the ECF, and the solutions for the two compartment relaxation model for this are well established (see Menon and Allen, Magn. Reson. in Med. 20:214-227 (1991). The T2 relaxation times should be multiexponential (see point (3) further below). The current work cannot exclude cell swelling as the mechanism for T2 changes (it is mentioned in the paper, but not dealt with). Water entering cells dilutes the protein structures, changes rotational correlation times of the proteins in the cell and is known to increase T2. The PSR confirms that this is indeed happening, so the data in this work is completely consistent with the Stroman work and completely consistent with cell swelling associated with depolarization. The authors should have performed light scattering studies to demonstrate the presence or absence of cell swelling. Measuring intracellular potential is not enough to clarify the mechanism.

[Reviewer 1, Response 1] We appreciate the reviewer’s comments. We agree that changes in cell volume due to depolarization and hyperpolarization significantly contribute to the observed changes in T2, PSR, and T1, especially in pelletized cells. For this reason, we already noted in the Discussion section of the original manuscript that cell volume changes influence the observed MR parameter changes, though this study did not present the magnitude of the cell volume changes. In this regard, we thank the reviewer for introducing the work by Stroman et al. (Magn Reson Med 59:700-706, 2008). When discussing the contribution of the cell volume changes to the observed MR parameter changes, we additionally discussed the work of Stroman et al. in the revised manuscript.

In addition, we acknowledge that the title and main conclusion of the original manuscript may be misleading, as we did not separately consider the effect of cell volume changes on MR parameters. To more accurately reflect the scope and results of this study and also take into account the reviewer 2’s suggestion, we adjusted the title to “Responses to membrane potential-modulating ionic solutions measured by magnetic resonance imaging of cultured cells and in vivo rat cortex” and also revised the relevant phrases in the main text.

Finally, when [K⁺]-induced membrane potential changes are involved, there seems to be factors other than cell volume changes that appear to influence T² changes. Our follow-up study shows that there are differences in volume changes for the same T² change in the following two different situations: pure osmotic volume changes versus [K⁺]-induced volume changes. For example, for the same T² change, the volume change for depolarization is greater than the volume change for hypoosmotic conditions. We will present these results in this coming ISMRM 2025 and are also preparing a manuscript to report shortly.

[Reviewer 1, Comment 2] So why does it matter whether the mechanism is cell swelling or membrane potential? The reason is response time. Cell swelling due to depolarization is a slow process, slower than hemodynamic responses that characterize BOLD. In fact, cell swelling under normal homeostatic conditions in vivo is virtually non-existent. Only sustained depolarization events typically associated with non-naturalistic stimuli or brain dysfunction produce cell swelling. Membrane potential changes associated with neural activity, on the other hand, are very fast. In this manuscript, the authors have convincingly shown a signal change that is virtually the same as what was seen in the Stroman publication, but they have not shown that there is a response that can be detected with anything approaching the timescale of an action potential. So one cannot definitely say that the changes observed are due to membrane potential. One can only say they are consistent with cell swelling, regardless of what causes the cell swelling.

For this mechanism to be relevant to explaining DIANA, one needs to show that the cell swelling changes occur within a millisecond, which has never been reported. If one knows the populations of ECF and pellet, the T2s of the ECF and pellet and the volume change of the cells in the pellet, one can model any expected T2 changes due to neuronal activity. I think one would find that these are minuscule within the context of an action potential, or even bulk action potential.

[Reviewer 1, Response 2] In the context of cell swelling occurring at rapid response times, if we define cell swelling simply as an “increase in cell volume,” there are several studies reporting transient structural (or volumetric) changes (e.g., ~nm diameter change over ~ms duration) in neuron cells during action potential propagation (Akkin et al., Biophys J 93:1347-1353, 2007; Kim et al., Biophys J 92:3122-3129, 2007; Lee et al., IEEE Trans Biomed Eng 58:3000-3003, 2011; Wnek et al., J Polym Sci Part B: Polym Phys 54:7-14, 2015; Yang et al., ACS Nano 12:4186-4193, 2018). These studies show a good correlation between membrane potential changes and cell volume changes (even if very small) at the cellular level within milliseconds.

As mentioned in the Response 1 above, this study does not address rapid dynamic membrane potential changes on the millisecond scale, which we explicitly mentioned as one of the limitations in the Discussion section of the original manuscript. For this reason, we do not claim in this study that we provide the reader with definitive answers about the mechanisms involved in DIANA. Rather, as a first step toward addressing the mechanism of DIANA, this study confirms that there is a good correlation between changes in membrane potential and measurable MR parameters (e.g., T² and PSR) when using ionic solutions that modulate membrane potential. Identifying MR parameter changes that occur during millisecond-scale membrane potential changes due to rapid neural activation will be addressed in the follow-up study mentioned in the Response 1 above.

There are a few smaller issues that should be addressed.

[Reviewer 1, Comment 3] (1) Why were complicated imaging sequences used to measure T1 and T2? On a Bruker system it should be possible to do very simple acquisitions with hard pulses (which will not need dictionaries and such to get quantitative numbers). Of course, this can only be done sample by sample and would take longer, but it avoids a lot of complication to correct the RF pulses used for imaging, which leads me to the 2nd point.

[Reviewer 1, Response 3] We appreciate the reviewer’s suggestion regarding imaging sequences. In fact, we used dictionaries for fitting in vivo T² decay data, not in vitro data. Sample-by-sample nonlocalized acquisition with hard pulses may be applicable for in vitro measurements. However, for in vivo measurements, a slice-selective multi-echo spin-echo sequence was necessary to acquire T² maps within a reasonable scan time. Our choice of imaging sequence was guided by the need to spatially resolve MR signals from specific regions of interest while balancing scan time constraints.

[Reviewer 1, Comment 4] (2) Figure S1 (H) is unlike any exponential T2 decay I have seen in almost 40 years of making T2 measurements. The strange plateau at the beginning and the bump around TE = 25 ms are odd. These could just be noise, but the fitted curve exactly reproduces these features. A monoexponential T2 decay cannot, by definition, produce a fit shaped like this.

[Reviewer 1, Response 4] The T² decay curves in Figure S1(H) indeed display features that deviate from a simple monoexponential decay. In our in vivo experiments, we used a multi-echo spin-echo sequence with slice-selective excitation and refocusing pulses. In such sequences, the echo train is influenced by stimulated echoes and imperfect slice profiles. This phenomenon is inherent to the pulse sequence rather than being artifacts or fitting errors (Hennig, Concepts Magn Reson 3:125-143, 1991; Lebel and Wilman, Magn Reson Med 64:1005-1014, 2010; McPhee and Wilman, Magn Reson Med 77:2057-2065, 2017). Therefore, we fitted the T₂ decay curve using the technique developed by McPhee and Wilman (2017).

[Reviewer 1, Comment 5] (3) As noted earlier, layered samples produce biexponential T2 decays and monoexponential T1 decays. I don't quite see how this was accounted for in the fitting of the data from the pellet preparations. I realize that these are spatially resolved measurements, but the imaging slice shown seems to be at the boundary of the pellet and the extracellular media and there definitely should be a biexponential water proton decay curve. Only 5 echo times were used, so this is part of the problem, but it does mean that the T2 reported is a population fraction weighted average of the T2 in the two compartments.

[Reviewer 1, Response 5] We understand the reviewer’s concern regarding potential biexponential decay due to the presence of different compartments. In our experiments, we carefully positioned the imaging slice sufficiently remote from the pellet-media interface. This approach ensures that the signal predominantly arises from the cells (and interstitial fluid), excluding the influence of extracellular media above the cell pellet. We described the imaging slice more clearly in the revised manuscript. As mentioned in our Methods section, for in vitro experiments, we repeated a single-echo spin-echo sequence with 50 difference echo times. While Figure 1C illustrates data from five echo times for visual clarity, the full dataset with all 50 echo times was used for fitting. We clarified this point in the revised manuscript to avoid any misunderstanding.

[Reviewer 1, Comment 6] (4) Delta T1 and T2 values are presented for the pellets in wells, but no absolute values are presented for either the pellets or the KCL solutions that I could find.

[Reviewer 1, Response 6] As requested by the reviewer, we included the absolute values in the supplementary information.

Reviewer #2 (Public review):

Summary:

Min et al. attempt to demonstrate that magnetic resonance imaging (MRI) can detect changes in neuronal membrane potentials. They approach this goal by studying how MRI contrast and cellular potentials together respond to treatment of cultured cells with ionic solutions. The authors specifically study two MRI-based measurements: (A) the transverse (T2) relaxation rate, which reflects microscopic magnetic fields caused by solutes and biological structures; and (B) the fraction or "pool size ratio" (PSR) of water molecules estimated to be bound to macromolecules, using an MRI technique called magnetization transfer (MT) imaging. They see that depolarizing K⁺ and Ba2+ concentrations lead to T2 increases and PSR decreases that vary approximately linearly with voltage in a neuroblastoma cell line and that change similarly in a second cell type. They also show that depolarizing potassium concentrations evoke reversible T2 increases in rat brains and that these changes are reversed when potassium is renormalized. Min et al. argue that this implies that membrane potential changes cause the MRI effects, providing a potential basis for detecting cellular voltages by noninvasive imaging. If this were true, it would help validate a recent paper published by some of the authors (Toi et al., Science 378:160-8, 2022), in which they claimed to be able to detect millisecond-scale neuronal responses by MRI.

Strengths:

The discovery of a mechanism for relating cellular membrane potential to MRI contrast could yield an important means for studying functions of the nervous system. Achieving this has been a longstanding goal in the MRI community, but previous strategies have proven too weak or insufficiently reproducible for neuroscientific or clinical applications. The current paper suggests remarkably that one of the simplest and most widely used MRI contrast mechanisms-T2 weighted imaging-may indicate membrane potentials if measured in the absence of the hemodynamic signals that most functional MRI (fMRI) experiments rely on. The authors make their case using a diverse set of quantitative tests that include controls for ion and cell type-specificity of their in vitro results and reversibility of MRI changes observed in vivo.

Weaknesses:

[Reviewer 2, Comment 1] The major weakness of the paper is that it uses correlational data to conclude that there is a causational relationship between membrane potential and MRI contrast. Alternative explanations that could explain the authors' findings are not adequately considered. Most notably, depolarizing ionic solutions can also induce changes in cellular volume and tissue structure that in turn alter MRI contrast properties similarly to the results shown here. For example, a study by Stroman et al. (Magn Reson Med 59:700-6, 2008) reported reversible potassium-dependent T2 increases in neural tissue that correlate closely with light scattering-based indications of cell swelling. Phi Van et al. (Sci Adv 10:eadl2034, 2024) showed that potassium addition to one of the cell lines used here likewise leads to cell size increases and T2 increases. Such effects could in principle account for Min et al.'s results, and indeed it is difficult to see how they would not contribute, but they occur on a time scale far too slow to yield useful indications of membrane potential. The authors' observation that PSR correlates negatively with T2 in their experiments is also consistent with this explanation, given the inverse relationship usually observed (and mechanistically expected) between these two parameters. If the authors could show a tight correspondence between millisecond-scale membrane potential changes and MRI contrast, their argument for a causal connection or a useful correlational relationship between membrane potential and image contrast would be much stronger. As it is, however, the article does not succeed in demonstrating that membrane potential changes can be detected by MRI.

[Reviewer 2, Response 1] We appreciate the reviewer’s comments. We agree that changes in cell volume due to depolarization and hyperpolarization significantly contribute to the observed MR parameter changes. For this reason, we have already noted in the Discussion section of the original manuscript that cell volume changes influence the observed MR parameter changes. In this regard, we thank the reviewer for introducing the work by Stroman et al. (Magn Reson Med 59:700-706, 2008) and Phi Van et al. (Sci Adv 10:eadl2034, 2024). When discussing the contribution of the cell volume changes to the observed MR parameter changes, we additionally discussed both work of Stroman et al. and Phi Van et al. in the revised manuscript.

In addition, this study does not address rapid dynamic membrane potential changes on the millisecond scale, which we explicitly discussed as one of the limitations of this study in the Discussion section of the original manuscript. For this reason, we do not claim in this study that we provide the reader with definitive answers about the mechanisms involved in DIANA. Rather, as a first step toward addressing the mechanism of DIANA, this study confirms that there is a good correlation between changes in membrane potential and measurable MR parameters (although on a slow time scale) when using ionic solutions that modulate membrane potential. Identifying MR parameter changes that occur during millisecond-scale membrane potential changes due to rapid neural activation will be addressed in the follow-up study mentioned in the Response 1 to Reviewer 1’s Comment 1 above.

Together, we acknowledge that the title and main conclusion of the original manuscript may be misleading. To more accurately reflect the scope and results of this study and also consider the reviewer’s suggestion, we adjusted the title to “Responses to membrane potential-modulating ionic solutions measured by magnetic resonance imaging of cultured cells and in vivo rat cortex” and also revised the relevant phrases in the main text.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

[Reviewer 1, Comment 7] The manuscript is well written. One thing to emphasize early on is that the KCL depolarization is done in an equimolar (or isotonic) manner. I was not clear on this point until I got to the very end of the methods. This is a strength of the paper and should be presented earlier.

[Reviewer 1, Response 7] In response to the reviewer’s suggestion, we have revised the manuscript to present the equimolar characteristic of our experiment earlier.

[Reviewer 1, Comment 8] In terms of experiments, the relaxation time measurements are not well constructed. They should be done with a CPMG sequence with hundreds of echos and properly curve fit. This is entirely possible on a Bruker spectrometer.

[Reviewer 1, Response 8] As noted in our Response to Reviewer 1’s Comment 3, while a CPMG sequence with numerous echoes and straightforward curve fitting can be effective, it is less feasible for in vivo experiments. Our multi-echo spin-echo sequence was a balanced approach between spatial resolution, reasonable scan duration, and the need to localize signals within specific regions of interest.

[Reviewer 1, Comment 9] Measurements of cell swelling should be done to determine the time course of the cell swelling. This could be with NMR (CPMG) or with light scattering. For this mechanism to be relevant to explaining DIANA, one needs to show that the cell swelling changes occur within a millisecond, which has never been reported. If one knows the populations of ECF and pellet, the T2s of the ECF and pellet and the volume change of the cells in the pellet, one can model any expected T2 changes due to neuronal activity.

[Reviewer 1, Response 9] We acknowledge the importance of further research to further strengthened the claims of this study through additional experiments such as cell volume recording. We will do it in future studies.

As noted in our Response 2 to Reviewer 1’s Comment 2, this study does not address rapid membrane potential changes on the millisecond scale, and we acknowledge that establishing the precise timing of cell swelling is crucial for fully understanding the mechanisms of DIANA. Our current work demonstrates that MR parameters (e.g., T² and PSR) correlate strongly with membrane potential-modulating ionic environments, but it does not extend to millisecond-scale neural activation. We recognize the importance of further experiments, such as direct cell volume measurements and plan to incorporate it in future studies to build on the insights gained from the present work.

Reviewer #2 (Recommendations for the authors):

Here are a few comments, questions, and suggestions for improvement:

[Reviewer 2, Comment 2] I could not find much information about the various incubation times and delays used for the authors' in vitro experiments. For each of the in vitro experiments in particular, how long were cells exposed to the stated ionic condition prior to imaging, and how long did the imaging take? Could this and any other relevant information about the experimental timing please be provided and added to the methods section?

[Reviewer 2, Response 2] We have included the information about the preparation/incubation times in the revised manuscript. For the scan time, it was already stated in the original manuscript: 23 minutes for the single-echo spin-echo sequence and 23 minutes for the inversion-recovery multi-echo spin-echo, for a total of 46 minutes.

[Reviewer 2, Comment 3] In what format were the cells used for patch clamping, and were any controls done to ensure that characteristics of these cells were the same as those pelleted and imaged in the MRI studies? How long were the incubation times with ionic solutions in the patch clamp experiment? This information should likewise be added to the paper.

[Reviewer 2, Response 3] We have clarified in the revised manuscript that SH-SY5Y cells were patch clamp-measured in their adherent state. On the other hand, the cells were dissociated from the culture plate and pelleted, so the experimental environments were not entirely identical. The patch clamp experiments involved a 20–30 minutes incubation period with the ionic solutions. We have included this information in the revised manuscript.

[Reviewer 2, Comment 4] Can the authors provide information about the mean cell size observed under each condition in their in vitro experiments?

[Reviewer 2, Response 4] We did not directly quantify the mean cell size for each in vitro condition in this study, so we do not have corresponding data. However, we acknowledge that this information could provide valuable insights into potential mechanisms underlying the observed MR parameter changes. In future experiments, we plan to include direct cell-size measurements to further elucidate how changes in cell volume or hydration contribute to our MR findings.

[Reviewer 2, Comment 5] The ionic challenges used both in vitro and in vivo could also have affected cell permeability, with corresponding effects that would be detectable in diffusion weighted imaging. Did the authors examine this or obtain any results that could reflect on contributions of permeability properties to the contrast effects they report?

[Reviewer 2, Response 5] We did not perform diffusion-weighted imaging and therefore do not have direct data regarding changes in cell permeability. We agree that incorporating diffusion-weighted measurements could help distinguish whether the MR parameters changes are driven primarily by membrane potential shifts, cell volume changes, or variations in permeability properties. We will consider these approaches in our future studies.

[Reviewer 2, Comment 6] Clearly, a faster stimulation method such as optogenetics, in combination with time-locked MRI readouts of the pelleted cells, would be more effective at demonstrating a useful relationship between cellular neurophysiology and MRI contrast in vitro. Can the authors present data from such an experiment? Is there any information they can present that documents the time course of observed responses in their experiments?

[Reviewer 2, Response 6] In the current study, our methodology did not include time-resolved or dynamic measurements. While it may be possible to obtain indirect information about the temporal dynamics using T²-weighted or MT-weighted imaging, such an experiment was beyond the scope of this work. However, we agree that an optogenetic approach with time-locked MRI acquisitions could help directly link cell physiology to MRI contrast, and we will explore this in future studies.

[Reviewer 2, Comment 7] The authors used a drug cocktail to suppress hemodynamic effects in the experiments of Figs. 5-6. What evidence is there that this cocktail successfully suppresses hemodynamic responses and that it also preserves physiological responses to the ionic challenges used in their experiments? Were analogous in vivo results also obtained in the absence of the cocktail?

[Reviewer 2, Response 7] We appreciate the reviewer’s concern regarding pharmacological suppression of hemodynamic effects. Although each component is known to inhibit nitric oxide synthesis, we did not directly measure the degree of hemodynamic suppression in this study. In addition, we cannot definitively confirm that these agents preserved the physiological responses to the ionic challenges. We have clarified these points in the revised manuscript and identified them as limitations of the study.

[Reviewer 2, Comment 8] Why weren't PSR results reported as part of the in vivo experimental results in Fig. 5? Does PSR continue to vary inversely to T2 in these experiments?

[Reviewer 2, Response 8] In our current experimental setup, acquiring the T² map four times required 48 minutes, and extending the scan to include additional quantitative MT measurements for PSR would have significantly prolonged the scanning session. Given that these experiments were conducted on acutely craniotomized rats, maintaining stable physiological conditions for such a long period of time was challenging. Therefore, due to time constraints, we did not perform MT measurements and focused on T₂ mapping.

[Reviewer 2, Comment 9] The authors have established in vivo optogenetic stimulation paradigms in their laboratory and used them in the Toi et al. DIANA study. Were T2 or PSR changes observed in vivo using standard T2 measurement or T2-weighted imaging methods that do not rely on the DIANA pulse sequence they originally applied?

[Reviewer 2, Response 9] Our current T₂ mapping experiments utilized a standard multi-echo spin-echo sequence, rather than the DIANA pulse sequence employed in our previous work. In this respect, the T₂ changes we observed in vivo do not rely on the specialized DIANA methodology.

[Reviewer 2, Comment 10] In the discussion section, the authors state that to their knowledge, theirs "is the first report that changes in membrane potential can be detected through MRI." This cannot be true, as their own Toi et al. Science paper previously claimed this, and a number of the studies cited on p.2 also claimed to detect close correlates of neuroelectric activity. This statement should be amended or revised.

[Reviewer 2, Response 10] We appreciate the reviewer’s comment. We have revised the discussion section of the manuscript to reflect the points raised by the reviewer.

[Reviewer 2, Comment 11] Because the current study does not actually demonstrate that changes in membrane potential can be detected by MRI, the authors should alter the title, abstract, and a number of relevant statements throughout the text to avoid implying that this has been shown. The title, for instance, could be changed to "Responses to depolarizing and hyperpolarizing ionic solutions measured by magnetic resonance imaging of excitable cells and rat brains," or something along these lines.

[Reviewer 2, Response 11] We appreciate the reviewer’s suggestions. We have revised the title, abstract, and relevant statements of the manuscript to clarify that our findings show MR-detectable responses to ionic solutions that are expected to modulate membrane potential, rather than demonstrating direct detection of membrane potential changes by MRI.

[Reviewer 2, Comment 12] The axes in Fig. 3 seem to be mislabeled. I think the horizontal axes are supposed to be membrane potential measured in mV.

[Reviewer 2, Response 12] Thank the reviewer for finding an error. We have corrected the axis labels in Figure 3 to indicate membrane potential (in mV) on the horizontal axis.

[Reviewer 2, Comment 13] Since neither the experiments in Jurkat cells (Fig. 4) nor the in vivo MRI tests (Fig. 5-6) appear to have made in conjunction with membrane potential measurements, it seems like a stretch to refer to these experiments as involving manipulation of membrane potentials per se. Instead, the authors should refer to them as involving administration of stimuli expected to be depolarizing or hyperpolarizing. The "hyperpolarization" and "depolarization" labels of Fig. 4 similarly imply a result that has not actually been shown, and should ideally be changed.

[Reviewer 2, Response 13] To prevent any misleading that membrane potential changes were directly measured in Jurkat cells or in vivo, we have revised the relevant text and figure labels.

[Reviewer 2, Comment 14] The changes in T2 and PSR documented with various K⁺ challenges to Jurkat cells in Fig. 4 seem to follow a step-function-like profile that differs from the results reported in SH-SY5Y cells. Can the authors explain what might have caused this difference?

[Reviewer 2, Response 14] We currently do not have a definitive explanation for why Jurkat cells exhibit a step-function-like response to varying K⁺ levels, whereas SH-SY5Y cells show a linear response to log [K⁺]. Experiments that include direct membrane potential measurements in Jurkat cells would help clarify whether this difference arises from genuinely different patterns of depolarization/hyperpolarization or from other factors. We have revised the revised manuscript to address this point.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review): 

Summary: 

This fascinating manuscript studies the effect of education on brain structure through a natural experiment. Leveraging the UK BioBank, these authors study the causal effect of education using causal inference methodology that focuses on legislation for an additional mandatory year of education in a regression discontinuity design. 

Strengths: 

The methodological novelty and study design were viewed as strong, as was the import of the question under study. The evidence presented is solid. The work will be of broad interest to neuroscientists 

Weaknesses: 

There were several areas which might be strengthed from additional consideration from a methodological perspective. 

We sincerely thank the reviewer for the useful input, in particular, their recommendation to clarify RD and for catching some minor errors in the methods (such as taking the log of the Bayes factors). 

Reviewer #1 (Recommendations for the authors): 

(1) The fuzzy local-linear regression discontinuity analysis would benefit from further description. 

(2) In the description of the model, the terms "smoothness" and "continuity" appear to be used interchangeably. This should be adjusted to conform to mathematical definitions. 

We have now added to our explanations of continuity regression discontinuity. In particular, we now explain “fuzzy”, and add emphasis on the two separate empirical approaches (continuity and local-randomization), along with fixing our use of “smoothness” and “continuity”.

results:

“Compliance with ROSLA was very high (near 100%; Sup. Figure 2). However, given the cultural and historical trends leading to an increase in school attendance before ROSLA, most adolescents were continuing with education past 15 years of age before the policy change (Sup Plot. 7b). Prior work has estimated 25 percent of children would have left school a year earlier if not for ROSLA 41. Using the UK Biobank, we estimate this proportion to be around 10%, as the sample is healthier and of higher SES than the general population (Sup. Figure 2; Sup. Table 2) 46–48.”

methods:

“RD designs, like ours, can be ‘fuzzy’ indicating when assignment only increases the probability of receiving it, in turn, treatment assigned and treatment received do not correspond for some units 33,53. For instance, due to cultural and historical trends, there was an increase in school attendance before ROSLA; most adolescents were continuing with education past 15 years of age (Sup Plot. 7b). Prior work has estimated that 25 percent of children would have left school a year earlier if not for ROSLA 41. Using the UK Biobank, we estimate this proportion to be around 10%, as the sample is healthier and of higher SES than the general population (Sup. Figure 2; Sup. Table 2) 46–48.”

(3) The optimization of the smoother based on MSE would benefit from more explanation and consideration. How was the flexibility of the model taken into account in testing? Were there any concerns about post-selection inference? A sensitivity analysis across bandwidths is also necessary. Based on the model fit in Figure 1, results from a linear model should also be compared. 

It is common in the RD literature to illustrate plots with higher-order polynomial fits while inference is based on linear (or at most quadratic) models (Cattaneo, Idrobo & Titiunik, 2019). We agree that this field-specific practice can be confusing to readers. Therefore, we have redone Figure 1 using local-linear fits better aligning with our analysis pipeline. Yet, it is still not a one-to-one alignment as point estimation and confidence are handled robustly while our plotting tools are simple linear fits. In addition, we updated Sup. Fig 3 and moved 3rd-order polynomial RD plots to Sup. Fig 4.

Empirical RD has many branching analytical decisions (bandwidth, polynomial order, kernel) which can have large effects on the outcome. Fortunately, RD methodology is starting to become more standardized (Catteneo & Titiunik, 2022, Ann. Econ Rev) as there have been indications of publication bias using these methods (Stommes, Aronow & Sävje, 2023, Research and Politics (This paper suggest it is not researcher degrees of freedom, rather inappropriate inferential methods)). While not necessarily ill-intended, researcher degrees of freedom and analytic flexibility are major contributors to publication bias. We (self) limited our analytic flexibility by using pre-registration (https://osf.io/rv38z).

One of the most consequential analytic decisions in RD is the bandwidth size as there is no established practice, they are context-specific and can be highly influential on the results. The choice of bandwidths can be framed as a ‘bias vs. variance trade-off’. As bandwidths increase, variance decreases since more subjects are added yet bias (misspecification error/smoothing bias) also increases (as these subjects are further away and less similar). In our case, our assignment (running/forcing) variable is ‘date of birth in months’; therefore our smallest comparison would be individuals born in August 1957 (unaffected/no treatment) vs September 1957 (affected/treated). This comparison has the least bias (subjects are the most similar to each other), yet it comes at the expense of very few subjects (high variance in our estimate). 

MSE-derived bandwidths attempt to solve this issue by offering an automatic method to choose an analysis bandwidth in RD. Specifically, this aims to minimize the MSE of the local polynomial RD point estimator – effectively choosing a bandwidth by balancing the ‘bias vs. variance trade-off’ (explained in detail 4.4.2 Cattaneo et al., 2019 p 45 - 51 “A practical introduction to regression discontinuity designs: foundations”). Yet, you are very correct in highlighting potential overfitting issues as they are “by construction invalid for inference” (Calonico, Cattaneo & Farrell, 2020, p. 192). Quoting from Cattaneo and Titiunik’s Annual Review of Economics from 2022: 

“Ignoring the misspecification bias can lead to substantial overrejection of the null hypothesis of no treatment effect. For example, back-of-the-envelop calculations show that a nominal 95% confidence interval would have an empirical coverage of about 80%.”

Fortunately, modern RD analysis packages (such as rdrohust or RDHonest) calculate robust confidence intervals - for more details see Armstrong and Kolesar (2020). For a summary on MSE-bandwidths see the section “Why is it hard to estimate RD effects?” in Stommes and colleagues 2023 (https://arxiv.org/abs/2109.14526). For more in-depth handling see the Catteneo, Idrobo, and Titiunik primer (https://arxiv.org/abs/1911.09511).

Lastly, with MSE-derived bandwidths sensitivity tests only make sense within a narrow window of the MSE-optimized bandwidth (5.5 Cattaneo et al., 2019 p 106 - 107). When a significant effect occurs, placebo cutoffs (artificially moving the cutoff) and donut-hole analysis are great sensitivity tests. Instead of testing our bandwidths, we decided to use an alternate RD framework (local randomization) in which we compare 1-month and 5-month windows. Across all analysis strategies, MRI modalities, and brain regions, we do not find any effects of the education policy change ROSLA on long-term neural outcomes.

(4) In the Bayesian analysis, the authors deviated from their preregistered analytic plan. This whole section is a bit confusing in its current form - for example, point masses are not wide but rather narrow. Bayes factors are usually estimated; it is unclear how or why a prior was specified. What exactly is being modeled using a prior? Also, throughout - If the log was taken, as the methods seem to indicate for the Bayes factor, this should be mentioned in figures and reported estimates. 

First, we would like to thank you for spotting that we incorrectly kept the log in the methods. We have fixed this and added the following sentence to the methods: 

“Bayes factors are reported as BF₁₀ in support of the alternative hypothesis, we report Bayes factors under 1 as the multiplicative inverse (BF₀₁ = 1/BF)”

All Bayesian analyses need to have a prior. In practice, this becomes an issue when you’re uncertain about 1) the location of the effect (directionality & center mass, defined by a location parameter), yet more importantly, the 2) confidence/certainty of the range-spread of possible effects (determined by a scale parameter). In normally distributed priors these two ‘beliefs’ are represented with a mean and a standard deviation (the latter impacts your confidence/certainty on the range of plausible parameter space). 

Supplementary figure 6 illustrates several distributions (location = 0 for all) with varying scale parameters; when used as Bayesian priors this indicates differing levels of confidence in our certainty of the plausible parameter space. We illustrate our three reported, normally distributed priors centered at zero in blue with their differing scale parameters (sd = .5, 1 & 1.5).

All of these five prior distributions have the same location parameter (i.e., 0) yet varying differences in the scale parameter – our confidence in the certainty of the plausible parameter space. At first glance it might seem like a flat/uniform prior (not represented) is a good idea – yet, this would put equal weight on the possibility of every estimate thereby giving the same probability mass to implausible values as plausible ones. A uniform prior would, for instance, encode the hypothesis that education causing a 1% increase in brain volume is just as plausible as it causing either a doubling or halving in brain volume. In human research, we roughly know a range of reasonable effect sizes and it is rare to see massive effects.

A benefit of ‘weakly-informative’ priors is that they limit the range of plausible parameter values. The default prior in STAN (a popular Bayesian estimation program; https://mc-stan.org) is a normally distributed prior with a mean of zero and an SD of 2.5 (seen in orange in the figure; our initial preregistered prior). This large standard deviation easily permits positive and negative estimates putting minimal emphasis on zero. Contrast this to BayesFactor package’s (Morey R, Rouder J, 2023) default “wide” prior which is the Cauchy distribution (0, .7) illustrated in magenta (for more on the Cauchy see: https://distribution-explorer.github.io/continuous/cauchy.html). 

These different defaults reflect differing Bayesian philosophical schools (‘estimate parameters’ vs ‘quantify evidence’ camps); if your goal is to accurately estimate a parameter it would be odd to have a strong null prior, yet (in our opinion) when estimating point-null BF’s a wide default prior gives far too much evidence in support of the null. In point-null BF testing the Savage-Dickey density ratio is the ratio between the height of the prior at 0 and the height of the posterior at zero (see Figure under section “testing against point null 0”). This means BFs can be very prior sensitive (seen in SI tables 5 & 6). For this reason, we thought it made sense to do prior sensitivity testing, to ensure our conclusions in favor of the null were not caused solely by an overly wide prior (preregistered orange distribution) we decided to report the 3 narrower priors (blue ones).

Alternative Bayesian null hypotheses testing methods such as using Bayes Factors to test against a null region and ‘region of practical equivalence testing’ are less prior sensitive, yet both methods demand the researcher (e.g. ‘us’) to decide on a minimal effect size of practical interest. Once a minimal effect size of interest is determined any effect within this boundary is taken as evidence in support of the null hypothesis.

(5) It is unclear why a different method was employed for the August / September data analysis compared to the full-time series. 

We used a local-randomization RD framework, an entirely different empirical framework than continuity methods (resulting in a different estimate). For an overview see the primer by Cattaneo, Idrobo & Titiunik 2023 (“A Practical Introduction to Regression Discontinuity Designs: Extensions”; https://arxiv.org/abs/2301.08958).

A local randomization framework is optimal when the running variable is discrete (as in our case with DOB in months) (Cattaneo, Idrobo & Titiunik 2023). It makes stronger assumptions on exchangeability therefore a very narrow window around the cutoff needs to be used. See Figure 2.1 and 2.2 (in the Cattaneo, Idrobo & Titiunik 2023) for graphical illustrations of 1) a randomized experiment, 2) a continuity RD design, and 3) local-randomization RD. Using the full-time series in a local randomization analysis is not recommended as there is no control for differences between individuals as we move further away from the cutoff – making the estimated parameter highly endogenous.

We understand how it is confusing to have both a new framework and Bayesian methods (we could have chosen a fully frequentist approach) but using a different framework allows us to weigh up the aforementioned ‘bias vs variance tradeoff’ while Bayesian methods allow us to say something about the weight of evidence (for or against) our hypothesis.

(6) Figure 1 - why not use model fits from those employed for hypothesis testing? 

This is a great suggestion (ties into #3), we have now redone Figure 1.

(7) The section on "correlational effect" might also benefit from additional analyses and clarifications. Indeed, the data come from the same randomized experiment for which minimum education requirements were adjusted. Was the only difference that the number of years of education was studied as opposed to the cohort? If so, would the results of this analysis be similar in another subsample of the UK Biobank for which there was no change in policy?

We have clarified the methods section for the correlational/associational effect. This was the same subset of individuals for the local randomization analysis; all we did was change the independent variable from an exogenous dummy-coded ROSLA term (where half of the sample had the natural experiment) to a continuous (endogenous) educational attainment IV. 

In principle, the results from the associational analysis should be exactly the same if we use other UK Biobank cohorts. To see if the association of education attainment with the global neuroimaging cohorts was similar across sub-cohorts of new individuals, we conducted post hoc Bayesian analysis on eight more subcohort of 10-month intervals, spaced 2 years apart from each other (Sup. Figure 7; each indicated by a different color). Four of these sub-cohorts predate ROSLA, while the other four are after ROSLA. Educational attainment is slowly increasing across the cohorts of individuals born from 1949 until 1965; intriguingly the effect of ROSLA is visually evident in the distributions of educational attainment (Sup. Figure 7). Also, as seen in the cohorts predating ROSLA more and more individuals were (already) choosing to stay in education past 15 years of age (see cohort 1949 vs 1955 in Sup. Figure 7).

Sup. Figure 8 illustrates boxplots of the educational attainment posterior of the eight sub-cohorts in addition to our original analysis (s1957) using a normal distributed prior with a mean of 0 and a sd of 1. Total surface area shows a remarkably replicable association with education attainment. Yet, it is evident the “extremely strong” association we found for CSF was a statistical fluke – as the posterior of other cohorts (bar our initial test) crosses zero. The conclusions for the other global neuroimaging covariates where we concluded ‘no associational effect’ seems to hold across cohorts.

We have now added methods, deviation from preregistration, and the following excerpt to the results:

“A post hoc replication of this associational analysis in eight additional 10-month cohorts spaced two years apart (Sup. Figure 7) indicates our preregistered report on the associational effect of educational attainment on CSF to be most likely a false-positive (Sup. Figure 8). Yet, the positive association between surface area and educational attainment is robust across the additional eight replication cohorts.”

Reviewer #2 (Public review): 

Summary: 

The authors conduct a causal analysis of years of secondary education on brain structure in late life. They use a regression discontinuity analysis to measure the impact of a UK law change in 1972 that increased the years of mandatory education by 1 year. Using brain imaging data from the UK Biobank, they find essentially no evidence for 1 additional year of education altering brain structure in adulthood. 

Strengths: 

The authors pre-registered the study and the regression discontinuity was very carefully described and conducted. They completed a large number of diagnostic and alternate analyses to allow for different possible features in the data. (Unlike a positive finding, a negative finding is only bolstered by additional alternative analyses). 

Weaknesses: 

While the work is of high quality for the precise question asked, ultimately the exposure (1 additional year of education) is a very modest manipulation and the outcome is measured long after the intervention. Thus a null finding here is completely consistent educational attainment (EA) in fact having an impact on brain structure, where EA may reflect elements of training after a second education (e.g. university, post-graduate qualifications, etc) and not just stopping education at 16 yrs yes/no. 

The work also does not address the impact of the UK Biobank's well-known healthy volunteer bias (Fry et al., 2017) which is yet further magnified in the imaging extension study (Littlejohns et al., 2020). Under-representation of people with low EA will dilute the effects of EA and impact the interpretation of these results. 

References: 

Fry, A., Littlejohns, T. J., Sudlow, C., Doherty, N., Adamska, L., Sprosen, T., Collins, R., & Allen, N. E. (2017). Comparison of Sociodemographic and Health-Related Characteristics of UK Biobank Participants With Those of the General Population. American Journal of Epidemiology, 186(9), 1026-1034. https://doi.org/10.1093/aje/kwx246 

Littlejohns, T. J., Holliday, J., Gibson, L. M., Garratt, S., Oesingmann, N., Alfaro-Almagro, F., Bell, J. D., Boultwood, C., Collins, R., Conroy, M. C., Crabtree, N., Doherty, N., Frangi, A. F., Harvey, N. C., Leeson, P., Miller, K. L., Neubauer, S., Petersen, S. E., Sellors, J., ... Allen, N. E. (2020). The UK Biobank imaging enhancement of 100,000 participants: rationale, data collection, management and future directions. Nature Communications, 11(1), 2624. https://doi.org/10.1038/s41467-020-15948-9 

We thank the reviewer for the positive comments and constructive feedback, in particular, their emphasis on volunteer bias in UKB (similar points were mentioned by Reviewer 3). We have now addressed these limitations with the following passage in the discussion:

“The UK Biobank is known to have ‘healthy volunteer bias’, as respondents tend to be healthier, more educated, and are more likely to own assets [71,72]. Various types of selection bias can occur in non-representative samples, impacting either internal (type 1) or external (type 2) validity. One benefit of a natural experimental design is that it protects against threats to internal validity from selection bias [43], design-based internal validity threats still exist, such as if volunteer bias differentially impacts individuals based on the cutoff for assignment. A more pressing limitation – in particular, for an education policy change – is our power to detect effects using a sample of higher-educated individuals. This is evident in our first stage analysis examining the percentage of 15-year-olds impacted by ROSLA, which we estimate to be 10% in neuro-UKB (Sup. Figure 2 & Sup. Table 2), yet has been reported to be 25% in the UK general population [41]. Our results should be interpreted for this subpopulation  (UK, 1973, from 15 to 16 years of age, compliers) as we estimate a ‘local’ average treatment effect [73]. Natural experimental designs such as ours offer the potential for high internal validity at the expense of external validity.”

We also highlighted it both in the results and methods.

We appreciate that one year of education may seem modest compared to the entire educational trajectory, but as an intervention, we disagree that one year of education is ‘a very modest manipulation’. It is arguably one of the largest positive manipulations in childhood development we can administer. If we were to translate a year of education into the language of a (cognitive) intervention, it is clear that the manipulation, at least in terms of hours, days, and weeks, is substantial. Prior work on structural plasticity (e.g., motor, spatial & cognitive training) has involved substantially more limited manipulations in time, intensity, and extent. There is even (limited) evidence of localized persistent long-term structural changes (Wollett & Maguire, 2011, Cur. Bio.).

We have now also highlighted the limited generalizability of our findings since we estimate a ‘local’ average treatment effect. It is possible higher education (college, university, vocational schools, etc.) could impact brain structure, yet we see no theoretical reason why it would while secondary wouldn’t. Moreover, higher education education is even trickier to research empirically due to heightened self and administrative selection pressures. While we cannot discount this possibility, the impacts of endogenous factors such as genetics and socioeconomic status are most likely heightened. That being said, higher education offers exciting possibilities to compare more domain-specific processes (e.g., by comparing a philosophy student to a mathematics student). Causality could be tested in European systems with point entry into field-specific programs – allowing comparison of students who just missed entry criteria into one topic and settled for another.

Regarding the amount of time following the manipulation, as we highlight in our discussion this is both a weakness and a strength. Viewed from a developmental neuroplasticity lens it would have been nice to have imaging immediately following the manipulation. Yet, from an aging perspective, our design has increased power to detect an effect.  

Reviewer #2 (Recommendations for the authors): 

(1) The authors assert there is no strong causal evidence for EA on brain structure. This overlooks work from Mendielian Randomisation, e.g. this careful work: https://pubmed.ncbi.nlm.nih.gov/36310536/ ... evidence from (good quality) MR studies should be considered. 

We thank the reviewer for highlighting this well-done mendelian randomization study. We have now added this citation and removed previous claims on the “lack of causal evidence existing”. We refrain from discussing Mendelian randomization, as it it would need to be accompanied by a nuanced discussion on the strong limitations regarding EduYears-PGS in Mendelian randomization designs.

(2) Tukey/Boxplot is a good name for your identification of outliers but your treatment of outliers has a well-recognized name that is missing: Windsorisation. Please add this term to your description to help the reader more quickly understand what was done. 

Thanks, we have now added the term winsorized.

(3) Nowhere is it plainly stated that "fuzzy" means that you allow for imperfect compliance with the exposure, i.e. some children born before the cut-off stayed in school until 16, and some born after the cut-off left school before 16. For those unfamiliar with RD it would be very helpful to explain this at or near the first reference of the term "fuzzy". 

We have now clarified the term ‘fuzzy’ to the results and methods:

methods:

“RD designs, like ours, can be ‘fuzzy’ indicating when assignment only increases the probability of receiving it, in turn, treatment assigned and treatment received do not correspond for some units 33,53. For instance, due to cultural and historical trends, there was an increase in school attendance before ROSLA; most adolescents were continuing with education past 15 years of age (Sup Plot. 7b). Prior work has estimated that 25 percent of children would have left school a year earlier if not for ROSLA 41. Using the UK Biobank, we estimate this proportion to be around 10%, as the sample is healthier and of higher SES than the general population (Sup. Figure 2; Sup. Table 2) 46–48.”

(4) Supplementary Figure 2 never states what the percentage actually measures. What exactly does each dot represent? Is it based on UK Biobank subjects with a given birth month? If so clarify. 

Fixed!

Reviewer #3 (Public review): 

Summary: 

This study investigates evidence for a hypothesized, causal relationship between education, specifically the number of years spent in school, and brain structure as measured by common brain phenotypes such as surface area, cortical thickness, total volume, and diffusivity. 

To test their hypothesis, the authors rely on a "natural" intervention, that is, the 1972 ROSLA act that mandated an extra year of education for all 15-year-olds. The study's aim is to determine potential discontinuities in the outcomes of interest at the time of the policy change, which would indicate a causal dependence. Naturalistic experiments of this kind are akin to randomised controlled trials, the gold standard for answering questions of causality. 

Using two complementary, regression-based approaches, the authors find no discernible effect of spending an extra year in primary education on brain structure. The authors further demonstrate that observational studies showing an effect between education and brain structure may be confounded and thus unreliable when assessing causal relationships. 

Strengths: 

(1) A clear strength of this study is the large sample size totalling up to 30k participants from the UK Biobank. Although sample sizes for individual analyses are an order of magnitude smaller, most neuroimaging studies usually have to rely on much smaller samples. 

(2) This study has been preregistered in advance, detailing the authors' scientific question, planned method of inquiry, and intended analyses, with only minor, justifiable changes in the final analysis. 

(3) The analyses look at both global and local brain measures used as outcomes, thereby assessing a diverse range of brain phenotypes that could be implicated in a causal relationship with a person's level of education. 

(4) The authors use multiple methodological approaches, including validation and sensitivity analyses, to investigate the robustness of their findings and, in the case of correlational analysis, highlight differences with related work by others. 

(5) The extensive discussion of findings and how they relate to the existing, somewhat contradictory literature gives a comprehensive overview of the current state of research in this area. 

Weaknesses: 

(1) This study investigates a well-posed but necessarily narrow question in a specific setting: 15-year-old British students born around 1957 who also participated in the UKB imaging study roughly 60 years later. Thus conclusions about the existence or absence of any general effect of the number of years of education on the brain's structure are limited to this specific scenario. 

(2) The authors address potential concerns about the validity of modelling assumptions and the sensitivity of the regression discontinuity design approach. However, the possibility of selection and cohort bias remains and is not discussed clearly in the paper. Other studies (e.g. Davies et al 2018, https://www.nature.com/articles/s41562-017-0279-y) have used the same policy intervention to study other health-related outcomes and have established ROSLA as a valid naturalistic experiment. Still, quoting Davies et al. (2018), "This assumes that the participants who reported leaving school at 15 years of age are a representative sample of the sub-population who left at 15 years of age. If this assumption does not hold, for example, if the sampled participants who left school at 15 years of age were healthier than those in the population, then the estimates could underestimate the differences between the groups.". Recent studies (Tyrrell 2021, Pirastu 2021) have shown that UK Biobank participants are on average healthier than the general population. Moreover, the imaging sub-group has an even stronger "healthy" bias (Lyall 2022). 

(3) The modelling approach used in this study requires that all covariates of no interest are equal before and after the cut-off, something that is impossible to test. Mentioned only briefly, the inclusion and exclusion of covariates in the model are not discussed in detail. Standard imaging confounds such as head motion and scanning site have been included but other factors (e.g. physical exercise, smoking, socioeconomic status, genetics, alcohol consumption, etc.) may also play a role. 

We thank the reviewer for their numerous positive comments and have now attempted to address the first two limitations (generalizability and UKB bias) with the following passage in the discussion:

“The UK Biobank is known to have ‘healthy volunteer bias’, as respondents tend to be healthier, more educated, and are more likely to own assets [71,72]. Various types of selection bias can occur in non-representative samples, impacting either internal (type 1) or external (type 2) validity. One benefit of a natural experimental design is that it protects against threats to internal validity from selection bias [43], design-based internal validity threats still exist, such as if volunteer bias differentially impacts individuals based on the cutoff for assignment. A more pressing limitation – in particular, for an education policy change – is our power to detect effects using a sample of higher-educated individuals. This is evident in our first stage analysis examining the percentage of 15-year-olds impacted by ROSLA, which we estimate to be 10% in neuro-UKB (Sup. Figure 2 & Sup. Table 2), yet has been reported to be 25% in the UK general population [41]. Our results should be interpreted for this subpopulation  (UK, 1973, from 15 to 16 years of age, compliers) as we estimate a ‘local’ average treatment effect [73]. Natural experimental designs such as ours offer the potential for high internal validity at the expense of external validity.”

We further highlight this in the results section:

“Compliance with ROSLA was very high (near 100%; Sup. Figure 2). However, given the cultural and historical trends leading to an increase in school attendance before ROSLA, most adolescents were continuing with education past 15 years of age before the policy change (Sup Plot. 7b). Prior work has estimated 25 percent of children would have left school a year earlier if not for ROSLA 41. Using the UK Biobank, we estimate this proportion to be around 10%, as the sample is healthier and of higher SES than the general population (Sup. Figure 2; Sup. Table 2) 46–48.”

Healthy volunteer bias can create two types of selection bias; crucially participation itself can serve as a collider threatening internal validity (outlined in van Alten et al., 2024; https://academic.oup.com/ije/article/53/3/dyae054/7666749). Natural experimental designs are partially sheltered from this major limitation, as ‘volunteer bias’ would have to differentially impact individuals on one side of the cutoff and not the other – thereby breaking a primary design assumption of regression discontinuity. Substantial prior work (including this article) has not found any threats to the validity of the 1973 ROSLA (Clark & Royer 2010, 2013; Barcellos et al., 2018, 2023; Davies et al., 2018, 2023). While the Davies 2028 article did IP-weight with the UK Biobank sample, Barcellos and colleagues 2023 (and 2018) do not, highlighting the following “Although the sample is not nationally representative,  our estimates have internal validity because there is no differential selection on the two sides of the September 1, 1957 cutoff – see  Appendix A.”.

The second (more acknowledged & arguably less problematic) type of selection bias results in threats to external validity (aka generalizability). As highlighted in your first point; this is a large limitation with every natural experimental design, yet in our case, this is further amplified by the UK Biobank’s healthy volunteer bias. We have now attempted to highlight this limitation in the discussion passage above.

Point 3 – the inability to fully confirm design validity – is again, another inherent limitation of a natural experimental approach. That being said, extensive prior work has tested different predetermined covariates in the 1973 ROSLA (cited within), and to our knowledge, no issues have been found. The 1973 ROSLA seems to be one of the better natural experiments around (there was also a concerted effort to have an ‘effective’ additional year; see Clark & Royer 2010). For these reasons, we stuck with only testing the variables we wanted to use to increase precision (also offering new neuroimaging covariates that didn’t exist in the literature base). One additional benefit of ROSLA was that the cutoff was decided years later on a variable that happened (date of birth) in the past – making it particularly hard for adolescents to alter their assignments.

Reviewer #3 (Recommendations for the authors): 

(1) FMRIB's preprocessing pipeline is mentioned. Does this include deconfounding of brain measures? Particularly, were measures deconfounded for age before the main analysis? 

This is such a crucial point that we triple-checked, brain imaging phenotypes were not corrected for age (https://biobank.ctsu.ox.ac.uk/crystal/crystal/docs/brain_mri.pdf) – large effects of age can be seen in the global metrics; older individuals have less surface area, thinner cortices, less brain volume (corrected for head size), more CSF volume (corrected for head size), more white matter hyperintensities, and worse FA values. Figure 1 shows these large age effects, which are controlled for in our continuity-based RD analysis.

One’s date of birth (DOB) of course does not match perfectly to their age, this is why we included the covariate ‘visit date’; this interplay can now be seen in our updated SI Figure 1 (recommended in #3) which shows the distributions of visit date, DOB, and age of scan. 

In a valid RD design covariates should not be necessary (as they should be balanced on either side of the cutoff), yet the inclusion of covariates does increase precision to detect effects. We tested this assumption, finding the effect of ‘visit date’ and its quadratic term to be not related to ROSLA (Sup. Table 1). This adds further evidence (specific to the UK Biobank sample) to the existing body of work showing the 1973 ROSLA policy change to not violate any design assumptions. Threats to internal validity would more than likely increase endogeneity and result in ‘false causal positive causal effects’ (which is not what we find).  

(2) Despite the large overall sample size, I am wondering whether the effective number of samples is sufficient to detect a potentially subtle effect that is further attenuated by the long time interval before scanning. As stated, for the optimised bandwidth window (DoB 20 to 35 months around cut-off), N is about 5000. Does this mean that effectively about 250 (10%) out of about 2500 participants born after the cut-off were leaving school at 16 rather than 15 because of ROSLA? For the local randomisation analysis, this becomes about N=10 (10% out of 100). Could a power analysis show that these cohort sizes are large enough to detect a reasonably large effect? 

This is a very valid point, one which we were grappling with while the paper was out for review. We now draw attention to this in the results and highlight this as a limitation in the discussion. While UKB’s non-representativeness limits our power (10% affected rather than 25% in the general population), it is still a very large sample. Our sample size is more in line with standard neuroimaging studies than with large cohort studies. 

The novelty of our study is its causal design, while we could very precisely measure an effect of some phenotype (variable X) in 40,000 individuals. This effect is probably not what we think we are measuring. Without IP-weighting it could even have a different sign. But more importantly, it is not variable X – it is the thousands of things (unmeasured confounders) that lead an individual to have more or less of variable X. The larger the sample the easier it is for small unmeasured confounders to reach significance (Big data paradox) – this in no way invalidates large samples, it is just our thinking and how we handle large samples will hopefully change to a more casual lens.

(3) Supplementary Figure 1: A similar raincloud plot of date of birth would be instructive to visualise the distribution of subjects born before and after the 1957 cut-off. 

Great idea! We have done this in Sup Fig. 1 for both visit date and DOB.

(4) p.9: Not sure about "extreme evidence", very strong would probably be sufficient. 

As preregistered, we interpreted Bayes Factors using Jeffrey’s criteria. ‘Extreme evidence’ is only used once and it is about finding an associational effect of educational attainment on CSF (BF10 > 100). Upon Reviewer 1’s recommendation 7, we conducted eight replication samples (Sup. Figure 7 & 8) and have now added the following passage to the results:

“A post hoc replication of this associational analysis in eight additional 10-month cohorts spaced two years apart (Sup. Figure 7) indicates our preregistered report on the associational effect of educational attainment on CSF to be most likely a false-positive (Sup. Figure 8). Yet, the positive association between surface area and educational attainment is robust across the additional eight replication cohorts.”

(5) The code would benefit from a bit of clean-up and additional documentation. In its current state, it is not easy to use, e.g. in a replication study. 

We have now further added documentation to our code; including a readme describing what each script does. The analysis pipeline used is not ideal for replications as the package used for continuity-based RD (RDHonest) initially could not handle covariates – therefore we manually corrected our variables after a discussion with Prof Kolesár (https://github.com/kolesarm/RDHonest/issues/7). 

Prof Kolesár added this functionality recently and future work should use the latest version of the package as it can correct for covariates. We have a new preprint examining the effect of 1972 ROLSA on telomere length in the UK Biobank using the latest package version of RDHonest (https://www.biorxiv.org/content/10.1101/2025.01.17.633604v1). To ensure maximum availability of such innovations, we will ensure the most up-to-date version of this script becomes available on this GitHub link (https://github.com/njudd/EduTelomere).

I like how this part of the reading brings awareness to the negative reputation that code switching has but also shows how it can be very useful. I think it's similar to when people say there is a place and a time to do something, usually in the context that you shouldn't be misbehaving in important setting. I have personally code switched in different scenarios such as my friends and my professor will see very different versions of me since I talk more formally to a professor than I would with my friends.

Reviewer #1 (Public review):

Summary:

The manuscript by Egawa and colleagues investigates differences in nodal spacing in an avian auditory brain stem circuit. The results are clearly presented and data are of very high quality. The authors make two main conclusions:

(1) Node spacing, i.e. internodal length, is intrinsically specified by the oligodendrocytes in the region they are found in, rather than axonal properties (branching or diameter).

(2) Activity is necessary (we don't know what kind of signaling) for normal numbers of oligodendrocytes and therefore the extent of myelination.

These are interesting observations, albeit phenomenon. I have only a few criticisms that should be addressed:

(1) The use of the term 'distribution' when describing the location of nodes is confusing. I think the authors mean rather than the patterns of nodal distribution, the pattern of nodal spacing. They have investigated spacing along the axon. I encourage the authors to substitute node spacing or internodal length for node distribution.

(2) In Seidl et al. (J Neurosci 2010) it was reported that axon diameter and internodal length (nodal spacing) were different for regions of the circuit. Can the authors help me better understand the difference between the Seidl results and those presented here?

(3) The authors looked only in very young animals - are the results reported here applicable only to development, or does additional refinement take place with aging?

(4) The fact that internodal length is specified by the oligodendrocyte suggests that activity may not modify the location of nodes of Ranvier - although again, the authors have only looked during early development. This is quite different than this reviewer's original thoughts - that activity altered internodal length and axon diameter. Thus, the results here argue against node plasticity. The authors may choose to highlight this point or argue for or against it based on results in adult birds?:

Significance:

This paper may argue against node plasticity as a mechanism for tuning of neural circuits. Myelin plasticity is a very hot topic right now and node plasticity reflects myelin plasticity. this seems to be a circuit where perhaps plasticity is NOT occurring. That would be interesting to test directly. One limitation is that this is limited to development.

Reviewer #2 (Public Review):

Summary:

This paper describes a new approach to detecting directed causal interactions between two genes without directly perturbing either gene. To check whether gene X influences gene Z, a reporter gene (Y) is engineered into the cell in such a way that (1) Y is under the same transcriptional control as X, and (2) Y does not influence Z. Then, under the null hypothesis that X does not affect Z, the authors derive an equation that describes the relationship between the covariance of X and Z and the covariance of Y and Z. Violation of this relationship can then be used to detect causality.

The authors benchmark their approach experimentally in several synthetic circuits. In 4 positive control circuits, X is a TetR-YFP fusion protein that represses Z, which is an RFP reporter. The proposed approach detected the repression interaction in 2 of the 4 positive control circuits. The authors constructed 16 negative control circuit designs in which X was again TetR-YFP, but where Z was either a constitutively expressed reporter, or simply the cellular growth rate. The proposed method detected a causal effect in two of the 16 negative controls, which the authors argue is perhaps not a false positive, but due to an unexpected causal effect. Overall, the data support the potential value of the proposed approach.

Strengths:

The idea of a "no-causality control" in the context of detected directed gene interactions is a valuable conceptual advance that could potentially see play in a variety of settings where perturbation-based causality detection experiments are made difficult by practical considerations.

By proving their mathematical result in the context of a continuous-time Markov chain, the authors use a more realistic model of the cell than, for instance, a set of deterministic ordinary differential equations.

The authors have improved the clarity and completeness of their proof compared to a previous version of the manuscript.

Limitations:

The authors themselves clearly outline the primary limitations of the study: The experimental benchmark is a proof of principle, and limited to synthetic circuits involving a handful of genes expressed on plasmids in E. coli. As acknowledged in the Discussion, negative controls were chosen based on the absence of known interactions, rather than perturbation experiments. Further work is needed to establish that this technique applies to other organisms and to biological networks involving a wider variety of genes and cellular functions. It seems to me that this paper's objective is not to delineate the technique's practical domain of validity, but rather to motivate this future work, and I think it succeeds in that.

Might your new "Proposed additional tests" subsection be better housed under Discussion rather than Results?

I may have missed this, but it doesn't look like you ran simulation benchmarks of your bootstrap-based test for checking whether the normalized covariances are equal. It would be useful to see in simulations how the true and false positive rates of that test vary with the usual suspects like sample size and noise strengths.

It looks like you estimated the uncertainty for eta_xz and eta_yz separately. Can you get the joint distribution? If you can do that, my intuition is you might be able to improve the power of the test (and maybe detect positive control #3?). For instance, if you can get your bootstraps for eta_xz and eta_yz together, could you just use a paired t-test to check for equality of means?

The proof is a lot better, and it's great that you nailed down the requirement on the decay of beta, but the proof is still confusing in some places:

- On pg 29, it says "That is, dividing the right equation in Eq. 5.8 with alpha, we write the ..." but the next equation doesn't obviously have anything to do with Eq. 5.8, and instead (I think) it comes from Eq 5.5. This could be clarified.

- Later on page 29, you write "We now evoke the requirement that the averages xt and yt are stationary", but then you just repeat Eq. 5.11 and set it to zero. Clearly you needed the limit condition to set Eq. 5.11 to zero, but it's not clear what you're using stationarity for. I mean, if you needed stationarity for 5.11 presumably you would have referenced it at that step.

It could be helpful for readers if you could spell out the practical implications of the theorem's assumptions (other than the no-causality requirement) by discussing examples of setups where it would or wouldn't hold.

I thought there was something particularly interesting about lonelygirl15's story in that it illustrates how much responsibility there is to being authentic online. The fact that "humans don't like being fooled" really resonated with me—I have certainly felt that way when I discovered something I had considered to be true later turned out to have been staged or manufactured. And, I have to admit, I also think that something is sort of interesting in that despite the revelation of truth, the channel just kept growing. People may have been upset initially, but they also realized that the narrative being told really was good, and they still wanted to know what occurred. It makes me wonder if, even though we appreciate authenticity, we just sort of love a good story even if it isn't "real."

Author response:

The following is the authors’ response to the original reviews

Response to the Editors’ Comments

Thankyou for this summary of the reviews and recommendations for corrections. We respond to each in turn, and have documented each correction with specific examples contained within our response to reviewers below.

‘They all recommend to clarify the link between hypotheses and analyses, ground them more clearly in, and conduct critical comparisons with existing literature, and address a potential multiple comparison problem.’

We have restructured our introduction to include the relevant literature outlined by the reviewers, and to be more clearly ground the goals of our model and broader analysis. We have additionally corrected for multiple comparisons within our exploratory associative analyses. We have additionaly sign posted exploratory tests more clearly.

‘Furthermore, R1 also recommends to include a formal external validation of how the model parameters relate to participant behaviour, to correct an unjustified claim of causality between childhood adversity and separation of self, and to clarify role of therapy received by patients.’

We have now tempered our language in the abstract which unintentionally implied causality in the associative analysis between childhood trauma and other-to-self generalisation. To note, in the sense that our models provide causal explanations for behaviour across all three phases of the task, we argue that our model comparison provides some causal evidence for algorithmic biases within the BPD phenotype. We have included further details of the exclusion and inclusion criteria of the BPD participants within the methods.

R2 specifically recommends to clarify, in the introduction, the specific aim of the paper, what is known already, and the approach to addressing it.’

We have more thoroughly outlined the current state of the art concerning behavioural and computational approaches to self insertion and social contagion, in health and within BPD. We have linked these more clearly to the aims of the work.

‘R2 also makes various additional recommendations regarding clarification of missing information about model comparison, fit statistics and group comparison of parameters from different models.’

Our model comparison approach and algorithm are outlined within the original paper for Hierarchical Bayesian Model comparison (Piray et al., 2019). We have outlined the concepts of this approach in the methods. We have now additionally improved clarity by placing descriptions of this approach more obviously in the results, and added points of greater detail in the methods, such as which statistics for comparison we extracted on the group and individual level.

In addition, in response to the need for greater comparison of parameters from different models, we have also hierarchically force-fitted the full suite of models (M1-M4) to all participants. We report all group differences from each model individually – assuming their explanation of the data - in Table S2. We have also demonstrated strong associations between parameters of equivalent meaning from different models to support our claims in Fig S11. Finally, we show minimal distortion to parameter estimates in between-group analysis when models are either fitted hierarchically to the entire population, or group wise (Figure S10).

‘R3 additionally recommends to clarify the clinical and cognitive process relevance of the experiment, and to consider the importance of the Phase 2 findings.’

We have now included greater reference to the assumptions in the social value orientation paradigm we use in the introduction. We have also responded to the specific point about the shift in central tendencies in phase 2 from the BPD group, noting that, while BPD participants do indeed get more relatively competitive vs. CON participants, they remain strikingly neutral with respect to the overall statespace. Importantly, model M4 does not preclude more competitive distributions existing.

‘Critically, they also share a concern about analyzing parameter estimates fit separately to two groups, when the best-fitting model is not shared. They propose to resolve this by considering a model that can encompass the full dynamics of the entire sample.’

We have hierarchically force-fitted the full suite of models (M1-M4) to all participants to allow for comparison between parameters within each model assumption. We report all group differences from each model individually – assuming their explanation of the data - in Table S2 and Table S3. We have also demonstrated strong associations between parameters of equivalent meaning from different models to support our claims in Fig S11. We also show minimal distortion to parameter estimates in between-group analysis when models are either fitted hierarchically to the entire population, or group wise (Figure S10).

Within model M1 and M2, the parameters quantify the degree to which participants believe their partner to be different from themselves. Under M1 and M2 model assumptions, BPD participants have meaningfully larger versus CON (Fig S10), which supports the notion that a new central tendency may be more parsimonious in phase 2 (as in the case of the optimal model for BPD, M4). We also show strong correlations across models between under M1 and M2, and the shift in central tendenices of beliefs between phase 1 and 2 under M3 and M4. This supports our primary comparison, and shows that even under non-dominant model assumptions, parameters demonstrate that BPD participants expect their partner’s relative reward preferences to be vastly different from themselves versus CON.

‘A final important point concerns the psychometric individual difference analyses which seem to be conducted on the full sample without considering the group structure.’

We have now more clearly focused our psychometric analysis. We control for multiple comparisons, and compare parameters across the same model (M3) when assessing the relationship between paranoia, trauma, trait mentalising, and social contagion. We have relegated all other exploratory analyses to the supplementary material and noted where p values survive correction using False Discovery Rate.

Reviewer 1:

‘The manuscript's primary weakness relates to the number of comparisons conducted and a lack of clarity in how those comparisons relate to the authors' hypotheses. The authors specify a primary prediction about disruption to information generalization in social decision making & learning processes, and it is clear from the text how their 4 main models are supposed to test this hypothesis. With regards to any further analyses however (such as the correlations between multiple clinical scales and eight different model parameters, but also individual parameter comparisons between groups), this is less clear. I recommend the authors clearly link each test to a hypothesis by specifying, for each analysis, what their specific expectations for conducted comparisons are, so a reader can assess whether the results are/aren't in line with predictions. The number of conducted tests relating to a specific hypothesis also determines whether multiple comparison corrections are warranted or not. If comparisons are exploratory in nature, this should be explicitly stated.’

We have now corrected for multiple comparisons when examining the relationship between psychometric findings and parameters, using partial correlations and bootstrapping for robustness. These latter analyses were indeed not preregistered, and so we have more clearly signposted that these tests were exploratory. We chose to focus on the influence of psychometrics of interest on social contagion under model M3 given that this model explained a reasonable minority of behaviour in each group. We have now fully edited this section in the main text in response, and relegated all other correlations to the supplementary materials.

‘Furthermore, the authors present some measures for external validation of the models, including comparison between reaction times and belief shifts, and correlations between model predicted accuracy and behavioural accuracy/total scores. However it would be great to see some more formal external validation of how the model parameters relate to participant behaviour, e.g., the correlation between the number of pro-social choices and ß-values, or the correlation between the change in absolute number of pro-social choices and the change in ß. From comparing the behavioural and computational results it looks like they would correlate highly, but it would be nice to see this formally confirmed.’

We have included this further examination within the Generative Accuracy and Recovery section:

‘We also assessed the relationship (Pearson rs) between modelled participant preference parameters in phase 1 and actual choice behaviour: was negatively correlated with prosocial versus competitive choices (r=-0.77, p<0.001) and individualistic versus competitive choices (r=-0.59, p<0.001); was positively correlated with individualistic versus competitive choices (r=0.53, p<0.001) and negatively correlated with prosocial versus individualistic choices (r=-0.69, p<0.001).’

‘The statement in the abstract that 'Overall, the findings provide a clear explanation of how self-other generalisation constrains and assists learning, how childhood adversity disrupts this through separation of internalised beliefs' makes an unjustified claim of causality between childhood adversity and separation of self - and other beliefs, although the authors only present correlations. I recommend this should be rephrased to reflect the correlational nature of the results.’

Sorry – this was unfortunate wording: we did not intend to imply causation with our second clause in the sentence mentioned. We have amended the language to make it clear this relationship is associative:

‘Overall, the findings provide a clear explanation of how self-other generalisation constrains and assists learning, how childhood adversity is associated with separation of internalised beliefs, and makes clear causal predictions about the mechanisms of social information generalisation under uncertainty.’

‘Currently, from the discussion the findings seem relevant in explaining certain aberrant social learning and -decision making processes in BPD. However, I would like to see a more thorough discussion about the practical relevance of their findings in light of their observation of comparable prediction accuracy between the two groups.’

We have included a new paragraph in the discussion to address this:

‘Notably, despite differing strategies, those with BPD achieved similar accuracy to CON participants in predicting their partners. All participants were more concerned with relative versus absolute reward; only those with BPD changed their strategy based on this focus. Practically this difference in BPD is captured either through disintegrated priors with a new median (M4) or very noisy, but integrated priors over partners (M1) if we assume M1 can account for the full population. In either case, the algorithm underlying the computational goal for BPD participants is far higher in entropy and emphasises a less stable or reliable process of inference. In future work, it would be important to assess this mechanism alongside momentary assessments of mood to understand whether more entropic learning processes contribute to distressing mood fluctuation.’

‘Relatedly, the authors mention that a primary focus of mentalization based therapy for BPD is 'restoring a stable sense of self' and 'differentiating the self from the other'. These goals are very reminiscent of the findings of the current study that individuals with BPD show lower uncertainty over their own and relative reward preferences, and that they are less susceptible to social contagion. Could the observed group differences therefore be a result of therapy rather than adverse early life experiences?’

This is something that we wish to explore in further work. While verbal and model descriptions appear parsimonious, this is not straight forward. As we see, clinical observation and phenomenological dynamics may not necessarily match in an intuitive way to parameters of interest. It may be that compartmentalisation of self and other – as we see in BPD participants within our data – may counter-intuitively express as a less stable self. The evolutionary mechanisms that make social insertion and contagion enduring may also be the same that foster trust and learning.

‘Regarding partner similarity: It was unclear to me why the authors chose partners that were 50% similar when it would be at least equally interesting to investigate self-insertion and social contagion with those that are more than 50% different to ourselves? Do the authors have any assumptions or even data that shows the results still hold for situations with lower than 50% similarity?’

While our task algorithm had a high probability to match individuals who were approximately 50% different with respect to their observed behaviour, there was variation either side of this value. The value of 50% median difference was chosen for two reasons: 1. We wanted to ensure participants had to learn about their partner to some degree relative to their own preferences and 2. we did not want to induce extreme over or under familiarity given the (now replicated) relationship between participant-partner similarity and intentional attributions (see below). Nevertheless, we did have some variation around the 50% median. Figure 3A in the top left panel demonstrates this fluctuation in participant-partner similarity and the figure legend further described this distribution (mean = 49%, sd = 12%). In future work we want to more closely manipulate the median similarity between participants and partners to understand how this facilitates or inhibits learning and generalisation.

There is some analysis of the relationship between degrees of similiarity and behaviour. In the third paragraph of page 15 we report the influence of participant-partner similarity on reaction times. In prior work (Barnby et al., 2022; Cognition) we had shown that similarity was associated with reduced attributions of harm about a partner, irrespective of their true parameters (e.g. whether they were prosocial/competitive). We replicate this previous finding with a double dissociation illustrated in Figure 4, showing that greater discrepancies in participant-partner prosociality increases explicit harmful intent attributions (but not self-interest), and discrepancies in participant-partner individualism reduces explicit self-interest attributions (but not harmful intent). We have made these clearer in our results structure, and included FDR correction values for multiple comparisons.

The methods section is rather dense and at least I found it difficult to keep track of the many different findings. I recommend the authors reduce the density by moving some of the secondary analyses in the supplementary materials, or alternatively, to provide an overall summary of all presented findings at the end of the Results section.

We have now moved several of our exploratory findings into the supplementary materials, noteably the analysis of participant-partner similarity on reaction times (Fig S9), as well as the uncorrected correlation between parameters (Fig S7).

Fig 2C) and Discussion p. 21: What do the authors mean by 'more sensitive updates'? more sensitive to what?

We have now edited the wording to specify ‘more belief updating’ rather than ‘sensitive’ to be clearer in our language.

P14 bottom: please specify what is meant by axial differences.

We have changed this to ‘preference type’ rather than using the term ‘axial’.

It may be helpful to have Supplementary Figure 1 in the main text.

Thank you for this suggestion. Given the volume of information in the main text we hope that it is acceptable for Figure S1 to remain in the supplementary materials.

Figure 3D bottom panel: what is the difference between left and right plots? Should one of them be alpha not beta?

The left and right plots are of the change in standard deviation (left) and central tendency (right) of participant preference change between phase 1 and 3. This is currently noted in the figure legend, but we had added some text to be clearer that this is over prosocial-competitive beliefs specifically. We chose to use this belief as an example given the centrality of prosocial-comeptitive beliefs in the learning process in Figure 2. We also noticed a small labelling error in the bottom panels of 3D which should have noted that each plot was either with respect to the precision or mean-shift in beliefs during phase 3.

‘The relationship between uncertainty over the self and uncertainty over the other with respect to the change in the precision (left) and median-shift (right) in phase 3 prosocial-competitive beliefs .’

Supplementary Figure 4: The prior presented does not look neutral to me, but rather right-leaning, so competitive, and therefore does indeed look like it was influenced by the self-model? If I am mistaken please could the authors explain why.

This example distribution is taken from a single BPD participant. In this case, indeed, the prior is somewhat right-shifted. However, on a group level, priors over the partner were closely centred around 0 (see reported statistics in paragraph 2 under the heading ‘Phase 2 – BPD Participants Use Disintegrated and Neutral Priors). However, we understand how this may come across as misleading. For clarity we have expanded upon Figure S4 to include the phase 1 and prior phase 2 distributions for the entire BPD population for both prosocial and individualistic beliefs. This further demonstrates that those with BPD held surprisingly neutral beliefs over the expectations about their partners’ prosociality, but had minor shifts between their own individualistic preferences and the expected individualistic preferences of their partners. This is also visible in Figure S2.

Reviewer 2:

‘There are two major weaknesses. First, the paper lacks focus and clarity. The introduction is rather vague and, after reading it, I remained confused about the paper's aims. Rather than relying on specific predictions, the analysis is exploratory. This implies that it is hard to keep track, and to understand the significance, of the many findings that are reported.’

Thank you for this opportunity to be clearer in our framing of the paper. While the model makes specific causal predictions with respect to behavioural dynamics conditional on algorithmic differences, our other analyses were indeed exploratory. We did not preregister this work but now given the intriguing findings we intent to preregister our future analyses.

We have made our introduction clearer with respect to the aims of the paper:

‘Our present work sought to achieve two primary goals: 1. Extend prior causal computational theories to formalise the interrelation between self-insertion and social contagion within an economic paradigm, the Intentions Game and 2., Test how a diagnosis of BPD may relate to deficits in these forms of generalisation. We propose a computational theory with testable predictions to begin addressing this question. To foreshadow our results, we found that healthy participants employ a mixed process of self-insertion and contagion to predict and align with the beliefs of their partners. In contrast, individuals with BPD exhibit distinct, disintegrated representations of self and other, despite showing similar average accuracy in their learning about partners. Our model and data suggest that the previously observed computational characteristics in BPD, such as reduced self-anchoring during ambiguous learning and a relative impermeability of the self, arise from the failure of information about others to transfer to and inform the self. By integrating separate computational findings, we provide a foundational model and a concise, dynamic paradigm to investigate uncertainty, generalization, and regulation in social interactions.’

‘Second, although the computational approach employed is clever and sophisticated, there is important information missing about model comparison which ultimately makes some of the results hard to assess from the perspective of the reader.’

Our model comparison employed what is state of the art random-effects Bayesian model comparison (Piray et al., 2019; PLOS Comp. Biol.). It initially fits each individual to each model using Laplace approximation, and subsequently ‘races’ each model against each other on the group level and individual level through hierarchical constraints and random-effect considerations. We included this in the methods but have now expanded on the descrpition we used to compare models:

In the results -

‘All computational models were fitted using a Hierarchical Bayesian Inference (HBI) algorithm which allows hierarchical parameter estimation while assuming random effects for group and individual model responsibility (Piray et al., 2019; see Methods for more information). We report individual and group-level model responsibility, in addition to protected exceedance probabilities between-groups to assess model dominance.’

We added to our existing description in the methods –

‘All computational models were fitted using a Hierarchical Bayesian Inference (HBI) algorithm which allows hierarchical parameter estimation while assuming random effects for group and individual model responsibility (Piray et al., 2019). During fitting we added a small noise floor to distributions (2.22e^-16) before normalisation for numerical stability. Parameters were estimated using the HBI in untransformed space drawing from broad priors (μM\=0, σ²_M = 6.5; where M\={M1, M2, M3, M4}). This process was run independently for each group. Parameters were transformed into model-relevant space for analysis. All models and hierarchical fitting was implemented in Matlab (Version R2022B). All other analyses were conducted in R (version 4.3.3; arm64 build) running on Mac OS (Ventura 13.0). We extracted individual and group level responsibilities, as well as the protected exceedance probability to assess model dominance per group.’

(1) P3, third paragraph: please define self-insertion

We have now more clearly defined this in the prior paragraph when introducing concepts.

‘To reduce uncertainty about others, theories of the relational self (Anderson & Chen, 2002) suggest that people have availble to them an extensive and well-grounded representation of themselves, leading to a readily accessible initial belief (Allport, 1924; Kreuger & Clement, 1994) that can be projected or integrated when learning about others (self-insertion).’

(2) Introduction: the specific aim of the paper should be clarified - at the moment, it is rather vague. The authors write: "However, critical questions remain: How do humans adjudicate between self-insertion and contagion during interaction to manage interpersonal generalization? Does the uncertainty in self-other beliefs affect their generalizability? How can disruptions in interpersonal exchange during sensitive developmental periods (e.g., childhood maltreatment) inform models of psychiatric disorders?". Which of these questions is the focus of the paper? And how does the paper aim at addressing it?

(3) Relatedly, from the introduction it is not clear whether the goal is to develop a theory of self-insertion and social contagion and test it empirically, or whether it is to study these processes in BPD, or both (or something else). Clarifying which specific question(s) is addressed is important (also clarifying what we already know about that specific question, and how the paper aims at elucidating that specific question).

We have now included our specific aims of the paper. We note this in the above response to the reviwers general comments.

(4) "Computational models have probed social processes in BPD, linking the BPD phenotype to a potential over-reliance on social versus internal cues (Henco et al., 2020), 'splitting' of social latent states that encode beliefs about others (Story et al., 2023), negative appraisal of interpersonal experiences with heightened self-blame (Mancinelli et al., 2024), inaccurate inferences about others' irritability (Hula et al., 2018), and reduced belief adaptation in social learning contexts (Siegel et al., 2020). Previous studies have typically overlooked how self and other are represented in tandem, prompting further investigation into why any of these BPD phenotypes manifest." Not clear what the link between the first and second sentence is. Does it mean that previous computational models have focused exclusively on how other people are represented in BPD, and not on how the self is represented? Please spell this out.

Thank you for the opportunity to be clearer in our language. We have now spelled out our point more precisely, and included some extra relevant literature helpfully pointed out by another reviewer.

‘Computational models have probed social processes in BPD, although almost exclusively during observational learning. The BPD phenotype has been associated with a potential over-reliance on social versus internal cues (Henco et al., 2020), ‘splitting’ of social latent states that encode beliefs about others (Story et al., 2023), negative appraisal of interpersonal experiences with heightened self-blame (Mancinelli et al., 2024), inaccurate inferences about others’ irritability (Hula et al., 2018), and reduced belief adaptation in social learning contexts (Siegel et al., 2020). Associative models have also been adapted to characterize  ‘leaky’ self-other reinforcement learning (Ereira et al., 2018), finding that those with BPD overgeneralize (leak updates) about themselves to others (Story et al., 2024). Altogether, there is currently a gap in the direct causal link between insertion, contagion, and learning (in)stability.’

(5) P5, first paragraph. The description of the task used in phase 1 should be more detailed. The essential information for understanding the task is missing.

We have updated this section to point toward Figure 1 and the Methods where the details of the task are more clearly outlined. We hope that it is acceptable not to explain the full task at this point for brevity and to not interrupt the flow of the results.

“Detailed descriptions of the task can be found in the methods section and Figure 1.’

(6) P5, second paragraph: briefly state how the Psychometric data were acquired (e.g., self-report).

We have now clarified this in the text.

‘All participants also self-reported their trait paranoia, childhood trauma, trust beliefs, and trait mentalizing (see methods).’

(7) "For example, a participant could make prosocial (self=5; other=5) versus individualistic (self=10; other=5) choices, or prosocial (self=10; other=10) versus competitive (self=10; other=5) choices". Not sure what criteria are used for distinguishing between individualistic and competitive - they look the same?

Sorry. This paragraph was not clear that the issue is that the interpretation of the choice depends on both members of the pair of options. Here, in one pair {(self=5,other=5) vs (self=10,other=5)}, it is highly pro-social for the self to choose (5,5), sacrificing 5 points for the sake of equality. In the second pair {(self=10,other=10) vs (self=10,other=5)}, it is highly competitive to choose (10,5), denying the other 5 points at no benefit to the self. We have clarified this:

‘We analyzed the ‘types’ of choices participants made in each phase (Supplementary Table 1). The interpretation of a participant’s choice depends on both values in a choice. For example, a participant could make prosocial (self=5; other=5) versus individualistic (self=10; other=5) choices, or prosocial (self=10; other=10) versus competitive (self=10; other=5) choices. There were 12 of each pair in phases 1 and 3 (individualistic vs. prosocial; prosocial vs. competitive; individualistic vs. competitive).’  

(8) "In phase 1, both CON and BPD participants made prosocial choices over competitive choices with similar frequency (CON=9.67[3.62]; BPD=9.60[3.57])" please report t-test - the same applies also various times below.

We have now included the t test statistics with each instance.

‘In phase 3, both CON and BPD participants continued to make equally frequent prosocial versus competitive choices (CON=9.15[3.91]; BPD=9.38[3.31]; t=-0.54, p=0.59); CON participants continued to make significantly less prosocial versus individualistic choices (CON=2.03[3.45]; BPD=3.78 [4.16]; t=2.31, p=0.02). Both groups chose equally frequent individualistic versus competitive choices (CON=10.91[2.40]; BPD=10.18[2.72]; t=-0.49, p=0.62).’

(9) P 9: "Models M2 and M3 allow for either self-insertion or social contagion to occur independently" what's the difference between M2 and M3?

Model M2 hypothesises that participants use their own self representation as priors when learning about the other in phase 2, but are not influenced by their partner. M3 hypothesises that participants form an uncoupled prior (no self-insertion) about their partner in phase 2, and their choices in phase 3 are influenced by observing their partner in phase 2 (social contagion). In Figure 1 we illustrate the difference between M2 and M3. In Table 1 we specifically report the parameterisation differences between M2 and M3. We have also now included a correlational analysis of parameters between models to demonstrate the relationship between model parameters of equivalent value between models (Fig S11). We have also force fitted all models (M1-M4) to the data independently and reported group differences within each (see Table S2 and Table S3).

(10) P 9, last paragraph: I did not understand the description of the Beta model.

The beta model is outlined in detail in Table 1. We have also clarified the description of the beta model on page 9:

‘The ‘Beta model’ is equivalent to M1 in its causal architecture (both self-insertion and social contagion are hypothesized to occur) but differs in richness: it accommodates the possibility that participants might only consider a single dimension of relative reward allocation, which is typically emphasized in previous studies (e.g., Hula et al., 2018).’

(11) P 9: I wonder whether one could think about more intuitive labels for the models, rather than M1, M2 etc.. This is just a suggestion, as I am not sure a short label would be feasible here.

Thank you for this suggestion. We apologise that it is not very intitutive. The problem is that given the various terms we use to explain the different processes of generalisation that might occur between self and other, and given that each model is a different combination of each, we felt that numbering them was a lesser evil. We hope that the reader will be able to reference both Figure 1 and Table 1 to get a good feel for how the models and their causal implications differ.

(12) Model comparison: the information about what was done for model comparison is scant, and little about fit statistics is reported. At the moment, it is hard for a reader to assess the results of the model comparison analysis.

Model comparison and fitting was conducted using simultaneous hierarchical fitting and random-effects comparison. This is employed through the HBI package (Piray et al., 2019) where the assumptions and fitting proceedures are outlined in great detail. In short, our comparison allows for individual and group-level hierarchical fitting and comparison. This overcomes the issue of interdependence between and within model fitting within a population, which is often estimated separately.

We have outlined this in the methods, although appreciate we do not touch upon it until the reader reaches that point. We have added a clarification statement on page 9 to rectify this:

‘All computational models were fitted using a Hierarchical Bayesian Inference (HBI) algorithm which allows hierarchical parameter estimation while assuming random effects for group and individual model responsibility (Piray et al., 2019; see Methods for more information). We report individual and group-level model responsibility, in addition to protected exceedance probabilities between-groups to assess model dominance.’

(13) P 14, first paragraph: "BPD participants were also more certain about both types of preference" what are the two types of preferences?

The two types of preferences are relative (prosocial-competitive) and absolute (individualistic) reward utility. These are expressed as b and a respectively. We have expanded the sentence in question to make this clearer:

‘BPD participants were also more certain about both self-preferences for absolute and relative reward ( = -0.89, 95%HDI: -1.01, -0.75; = -0.32, 95%HDI: -0.60, -0.04) versus CON participants (Figure 2B).’

(14) "Parameter Associations with Reported Trauma, Paranoia, and Attributed Intent" the results reported here are intriguing, but not fully convincing as there is the problem of multiple comparisons. The combinations between parameters and scales are rather numerous. I suggest to correct for multiple comparisons and to flag only the findings that survive correction.

We have now corrected this and controlled for multiple comparisons through partial correlation analysis, bootstrapping assessment for robustness, permutation testing, and False Detection Rate correction. We only report those that survive bootstrapping and permutation testing, reporting both corrected (p[fdr]) and uncorrected (p) significance.

(15) Results page 14 and page 15. The authors compare the various parameters between groups. I would assume that these parameters come from M1 for controls and from M4 for BDP? Please clarify if this is indeed the case. If it is the case, I am not sure this is appropriate. To my knowledge, it is appropriate to compare parameters between groups only if the same model is fit to both groups. If two different models are fit to each group, then the parameters are not comparable, as the parameter have, so to speak, different "meaning" in two models. Now, I want to stress that my knowledge on this matter may be limited, and that the authors' approach may be sound. However, to be reassured that the approach is indeed sound, I would appreciate a clarification on this point and a reference to relevant sources about this approach.

This is an important point. First, we confirmed all our main conclusions about parameter differences using the maximal model M1 to fit all the participants. We added Supplementary Table 2 to report the outcome of this analysis. Second, we did the same for parameters across all models M1-M4, fitting each to participants without comparison. This is particularly relevant for M3, since at least a minority of participants of both groups were best explained by this model. We report these analyses in Fig S11:

Since the M4 is nested within M1, we argue that this comparison is still meaningful, and note explanations in the text for why the effects noted between groups may occur given the differences in their causal meaning, for example in the results under phase 2 analyses:

‘Belief updating in phase 2 was less flexible in BPD participants. Median change in beliefs (from priors to posteriors) about a partner’s preferences was lower versus. CON ( = -5.53, 95%HDI: -7.20, -4.00; = -10.02, 95%HDI: -12.81, -7.30). Posterior beliefs about partner were more precise in BPD versus CON ( = -0.94, 95%HDI: -1.50, -0.45;  = -0.70, 95%HDI: -1.20, -0.25).  This is unsurprising given the disintegrated priors of the BPD group in M4, meaning they need to ‘travel less’ in state space. Nevertheless, even under assumptions of M1 and M2 for both groups, BPD showed smaller posteriors median changes versus CON in phase 2 (see Table T2). These results converge to suggest those with BPD form rigid posterior beliefs.’

(16) "We built and tested a theory of interpersonal generalization in a population of matched participants" this sentence seems to be unwarranted, as there is no theory in the paper (actually, as it is now, the paper looks rather exploratory)

We thank the reviewer for their perspective. Formal models can be used as a theoretical statement on the casual algorithmic process underlying decision making and choice behaviour; the development of formal models are an essential theoretical tool for precision and falsification (Haslbeck et al., 2022). In this sense, we have built several competing formal theories that test, using casual architectures, whether the latent distribution(s) that generate one’s choices generalise into one’s predictions about another person, and simultaneously whether one’s latent distribution(s) that represent beliefs about another person are used to inform future choices.

Reviewer 3:

‘My broad question about the experiment (in terms of its clinical and cognitive process relevance): Does the task encourage competition or give participants a reason to take advantage of others? I don't think it does, so it would be useful to clarify the normative account for prosociality in the introduction (e.g., some of Robin Dunbar's work).’

We agree that our paradigm does not encourage competition. We use a reward structure that makes it contingent on participants to overcome a particular threshold before earning rewards, but there is no competitive element to this, in that points earned or not earned by partners have no bearing on the outcomes for the participant. This is important given the consideration of recursive properties that arise through mixed-motive games; we wanted to focus purely on observational learning in phase 2, and repercussion-free choices made by participants in phase 1 and 3, meaning the choices participants, and decisions of a partner, are theoretically in line with self-preferences irrespective of the judgement of others. We have included a clearer statement of the structure of this type of task, and more clearly cited the origin for its structure (Murphy & Ackerman, 2011):

‘Our present work sought to achieve two primary goals. 1. Extend prior causal computational theories to formalise and test the interrelation between self-insertion and social contagion on learning and behaviour to better probe interpersonal generalisation in health, and 2., Test whether previous computational findings of social learning changes in BPD can be explained by infractions to self-other generalisation. We accomplish these goals by using a dynamic, sequential social value economic paradigm, the Intentions Game, building upon a Social Value Orientation Framework (Murphy & Ackerman, 2011) that assumes motivational variation in joint reward allocation.’

Given the introductions structure as it stands, we felt providing another paragraph on the normative assumptions of such a game was outside the scope of this article.

‘The finding that individuals with BPD do not engage in self-other generalization on this task of social intentions is novel and potentially clinically relevant. The authors find that BPD participants' tendency to be prosocial when splitting points with a partner does not transfer into their expectations of how a partner will treat them in a task where they are the passive recipient of points chosen by the partner. In the discussion, the authors reasonably focus on model differences between groups (Bayesian model comparison), yet I thought this finding -- BPD participants not assuming prosocial tendencies in phase 2 while CON participant did -- merited greater attention. Although the BPD group was close to 0 on the \beta prior in Phase 2, their difference from CON is still in the direction of being more mistrustful (or at least not assuming prosociality). This may line up with broader clinical literature on mistrustfulness and attributions of malevolence in the BPD literature (e.g., a 1992 paper by Nigg et al. in Journal of Abnormal Psychology). My broad point is to consider further the Phase 2 findings in terms of the clinical interpretation of the shift in \beta relative to controls.’

This is an important point, that we contextualize within the parameterisation of our utility model. While the shift toward 0 in the BPD participants is indeed more competitive, as the reviewer notes, it is surprisingly centred closely around 0, with only a slight bias to be prosocial (mean = -0.47;  = -6.10, 95%HDI: -7.60, -4.60). Charitably we might argue that BPD participants are expecting more competitive preferences from their partner. However even so, given their variance around their priors in phase 2, they are uncertain or unconfident about this. We take a more conservative approach in the paper and say that given the tight proximity to 0 and the variance of their group priors, they are likely to be ‘hedging their bets’ on whether their partner is going to be prosocial or competitive. While the movement from phase 1 to 2 is indeed in the competitive direction it still lands in neutral territory. Model M4 does not preclude central tendancies at the start of Phase 2 being more in the competitive direction.

‘First, the authors note that they have "proposed a theory with testable predictions" (p. 4 but also elsewhere) but they do not state any clear predictions in the introduction, nor do they consider what sort of patterns will be observed in the BPD group in view of extant clinical and computational literature. Rather, the paper seems to be somewhat exploratory, largely looking at group differences (BPD vs. CON) on all of the shared computational parameters and additional indices such as belief updating and reaction times. Given this, I would suggest that the authors make stronger connections between extant research on intention representation in BPD and their framework (model and paradigm). In particular, the authors do not address related findings from Ereira (2020) and Story (2024) finding that in a false belief task that BPD participants *overgeneralize* from self to other. A critical comparison of this work to the present study, including an examination of the two tasks differ in the processes they measure, is important.’

Thank you for this opportunity to include more of the important work that has preceded the present manuscript. Prior work has tended to focus on either descriptive explanations of self-other generalisation (e.g. through the use of RW type models) or has focused on observational learning instability in absence of a causal model from where initial self-other beliefs may arise. While the prior work cited by the reviewer [Ereira (2020; Nat. Comms.) and Story (2024; Trans. Psych.)] does examine the inter-trial updating between self-other, it does not integrate a self model into a self’s belief about an other prior to observation. Rather, it focuses almost exclusively on prediction error ‘leakage’ generated during learning about individual reward (i.e. one sided reward). These findings are important, but lie in a slightly different domain. They also do not cut against ours, and in fact, we argue in the discussion that the sort of learning instability described above and splitting (as we cite from Story ea. 2024; Psych. Rev.) may result from a lack of self anchoring typical of CON participants. Nevertheless we agree these works provide an important premise to contrast and set the groundwork for our present analysis and have included them in the framing of our introduction, as well as contrasting them to our data in the discussion.

In the introduction:

‘The BPD phenotype has been associated with a potential over-reliance on social versus internal cues (Henco et al., 2020), ‘splitting’ of social latent states that encode beliefs about others (Story et al., 2023), negative appraisal of interpersonal experiences with heightened self-blame (Mancinelli et al., 2024), inaccurate inferences about others’ irritability (Hula et al., 2018), and reduced belief adaptation in social learning contexts (Siegel et al., 2020). Associative models have also been adapted to characterize  ‘leaky’ self-other reinforcement learning (Ereira et al., 2018), finding that those with BPD overgeneralize (leak updates) about themselves to others (Story et al., 2024). Altogether, there is currently a gap in the direct causal link between insertion, contagion, and learning (in)stability.’

In the discussion:

‘Disruptions in self-to-other generalization provide an explanation for previous computational findings related to task-based mentalizing in BPD. Studies tracking observational mentalizing reveal that individuals with BPD, compared to those without, place greater emphasis on social over internal reward cues when learning (Henco et al., 2020; Fineberg et al., 2018). Those with BPD have been shown to exhibit reduced belief adaptation (Siegel et al., 2020) along with ‘splitting’ of latent social representations (Story et al., 2024a). BPD is also shown to be associated with overgeneralisation in self-to-other belief updates about individual outcomes when using a one-sided reward structure (where participant responses had no bearing on outcomes for the partner; Story et al., 2024b). Our analyses show that those with BPD are equal to controls in their generalisation of absolute reward (outcomes that only affect one player) but disintegrate beliefs about relative reward (outcomes that affect both players) through adoption of a new, neutral belief. We interpret this together in two ways: 1. There is a strong concern about social relativity when those with BPD form beliefs about others, 2. The absence of constrained self-insertion about relative outcomes may predispose to brittle or ‘split’ beliefs. In other words, those with BPD assume ambiguity about the social relativity preferences of another (i.e. how prosocial or punitive) and are quicker to settle on an explanation to resolve this. Although self-insertion may be counter-intuitive to rational belief formation, it has important implications for sustaining adaptive, trusting social bonds via information moderation.’

In addition, perhaps it is fairer to note more explicitly the exploratory nature of this work. Although the analyses are thorough, many of them are not argued for a priori (e.g., rate of belief updating in Figure 2C) and the reader amasses many individual findings that need to by synthesized.’

We have now noted the primary goals of our work in the introduction, and have included caveats about the exploratory nature of our analyses. We would note that our model is in effect a causal combination of prior work cited within the introduction (Barnby et al., 2022; Moutoussis et al., 2016). This renders our computational models in effect a causal theory to test, although we agree that our dissection of the results are exploratory. We have more clearly signposted this:

‘Our present work sought to achieve two primary goals. 1. Extend prior causal computational theories to formalise and test the interrelation between self-insertion and social contagion on learning and behaviour to better probe interpersonal generalisation in health, and 2., Test whether previous computational findings of social learning changes in BPD can be explained by infractions to self-other generalisation. We accomplish these goals by using a dynamic, sequential economic paradigm, the Intentions Game, building upon a Social Value Orientation Framework (Murphy & Ackerman, 2011) that assumes innate motivational variation in joint reward allocation.‘

‘Second, in the discussion, the authors are too quick to generalize to broad clinical phenomena in BPD that are not directly connected to the task at hand. For example, on p. 22: "Those with a diagnosis of BPD also show reduced permeability in generalising from other to self. While prior research has predominantly focused on how those with BPD use information to form impressions, it has not typically examined whether these impressions affect the self." Here, it's not self-representation per se (typically, identity or one's view of oneself), but instead cooperation and prosocial tendencies in an economic context. It is important to clarify what clinical phenomena may be closely related to the task and which are more distal and perhaps should not be approached here.’

Thank you for this important point. We agree that social value orientation, and particularly in this economically-assessed form, is but one aspect of the self, and we did not test any others. A version of the social contagion phenomena is also present in other aspects of the self in intertemporal (Moutoussis et al., 2016), economic (Suzuki et al., 2016) and moral preferences (Yu et al., 2021). It would be most interesting to attempt to correlate the degrees of insertion and contagion across the different tasks.

We take seriously the wider concern that behaviour in our tasks based on economic preferences may not have clinical validity. This issue is central in the whole field of computational psychiatry, much of which is based on generalizing from tasks like ours, and discussing correlations with psychometric measures. We hope that it is acceptable to leave such discussions to the many reviews on computational psychiatry (Montague et al., 2012; Hitchcock et al., 2022; Huys et al., 2016). Here, we have just put a caveat in the dicussion:

‘Finally, a limitation may be that behaviour in tasks based on economic preferences may not have clinical validity. This issue is central to the field of computational psychiatry, much of which is based on generalising from tasks like that within this paper and discussing correlations with psychometric measures. Extrapolating  economic tasks into the real world has been the topic of discussion for the many reviews on computational psychiatry (e.g. Montague et al., 2012; Hitchcock et al., 2022; Huys et al., 2016). We note a strength of this work is the use of model comparison to understand causal algorithmic differences between those with BPD and matched healthy controls. Nevertheless, we wish to further pursue how latent characteristics captured in our models may directly relate to real-world affective change.’

‘On a more technical level, I had two primary concerns. First, although the authors consider alternative models within a hierarchical Bayesian framework, some challenges arise when one analyzes parameter estimates fit separately to two groups, particularly when the best-fitting model is not shared. In particular, although the authors conduct a model confusion analysis, they do not as far I could tell (and apologies if I missed it) demonstrate that the dynamics of one model are nested within the other. Given that M4 has free parameters governing the expectations on the absolute and relative reward preferences in Phase 2, is it necessarily the case that the shared parameters between M1 and M4 can be interpreted on the same scale? Relatedly, group-specific model fitting has virtues when believes there to be two distinct populations, but there is also a risk of overfitting potentially irrelevant sample characteristics when parameters are fit group by group.

To resolve these issues, I saw one straightforward solution (though in modeling, my experience is that what seems straightforward on first glance may not be so upon further investigation). M1 assumes that participants' own preferences (posterior central tendency) in Phase 1 directly transfer to priors in Phase 2, but presumably the degree of transfer could vary somewhat without meriting an entirely new model (i.e., the authors currently place this question in terms of model selection, not within-model parameter variation). I would suggest that the authors consider a model parameterization fit to the full dataset (both groups) that contains free parameters capturing the *deviations* in the priors relative to the preceding phase's posterior. That is, the free parameters $\bar{\alpha}_{par}^m$ and $\bar{\beta}_{par}^m$ govern the central tendency of the Phase 2 prior parameter distributions directly, but could be reparametrized as deviations from Phase 1 $\theta^m_{ppt}$ parameters in an additive form. This allows for a single model to be fit all participants that encompasses the dynamics of interest such that between-group parameter comparisons are not biased by the strong assumptions imposed by M1 (that phase 1 preferences and phase 2 observations directly transfer to priors). In the case of controls, we would expect these deviation parameters to be centred on 0 insofar as the current M1 fit them best, whereas for BPD participants should have significant deviations from earlier-phase posteriors (e.g., the shift in \beta toward prior neutrality in phase 2 compared to one's own prosociality in phase 1). I think it's still valid for the authors to argue for stronger model constraints for Bayesian model comparison, as they do now, but inferences regarding parameter estimates should ideally be based on a model that can encompass the full dynamics of the entire sample, with simpler dynamics (like posterior -> prior transfer) being captured by near-zero parameter estimates.’

Thank you for the chance to be clearer in our modelling. In particular, the suggestion to include a model that can be fit to all participants with the equivalent of the likes of partial social insertion, to check if the results stand, can actually be accomplished through our existing models.  That is, the parameter that governs the flexibility over beliefs in phase 2 under models M1 (dominant for CON participant) and M2 parameterises the degree to which participants think their partner may be different from themselves. Thus, forcibly fitting M1 and M2 hierarchically to all participants, and then separately to BPD and CON participants, can quantify the issue raised: if BPD participants indeed distinguish partners as vastly different from themselves enough to warent a new central tendency, should be quantitively higher in BPD vs CON participants under M1 and M2.

We therefore tested this, reporting the distributional differences between for BPD and CON participants under M1, both when fitted together as a population and as separate groups. As is higher for BPD participants under both conditions for M1 and M2 it supports our claim and will add more context for the comparison - may be large enough in BPD that a new central tendency to anchor beliefs is a more parsimonious explanation.

We cross checked this result by assessing the discrepancy between the participant’s and assumed partner’s central tendencies for both prosocial and individualistic preferences via best-fitting model M4 for the BPD group. We thereby examined whether belief disintegration is uniform across preferences (relative vs abolsute reward) or whether one tendency was shifted dramatically more than another.  We found that beliefs over prosocial-competitive preferences were dramatically shifted, whereas those over individualistic preferences were not.

We have added the following to the main text results to explain this:

Model Comparison:

‘We found that CON participants were best fit at the group level by M1 (Frequency = 0.59, Protected Exceedance Probability = 0.98), whereas BPD participants were best fit by M4 (Frequency = 0.54, Protected Exceedance Probability = 0.86; Figure 2A). We first analyse the results of these separate fits. Later, in order to assuage concerns about drawing inferences from different models, we examined the relationships between the relevant parameters when we forced all participants to be fit to each of the models (in a hierarchical manner, separated by group). In sum, our model comparison is supported by convergence in parameter values when comparisons are meaningful. We refer to both types of analysis below.’

Phase 1:

‘These differences were replicated when considering parameters between groups when we fit all participants to the same models (M1-M4; see Table S2).’

Phase 2:

‘To check that these conclusions about self-insertion did not depend on the different models, we found that only under M1 and M2 were consistently larger in BPD versus CON. This supports the notion that new central tendencies for BPD participants in phase 2 were required, driven by expectations about a partner’s relative reward. (see Fig S10 & Table S2). and parameters under assumptions of M1 and M2 were strongly correlated with median change in belief between phase 1 and 2 under M3 and M4, suggesting convergence in outcome (Fig S11).’

‘Furthermore, even under assumptions of M1-M4 for both groups, BPD showed smaller posterior median changes versus CON in phase 2 (see Table T2). These results converge to suggest those with BPD form rigid posterior beliefs.’

‘Assessing this same relationship under M1- and M2-only assumptions reveals a replication of this group effect for absolute reward, but the effect is reversed for relative reward (see Table S3). This accords with the context of each model, where under M1 and M2, BPD participants had larger phase 2 prior flexibility over relative reward (leading to larger initial surprise), which was better accounted for by a new central tendency under M4 during model comparison. When comparing both groups under M1-M4 informational surprise over absolute reward was consistently restricted in BPD (Table S3), suggesting a diminished weight of this preference when forming beliefs about an other.’

Phase 3

‘In the dominant model for the BPD group—M4—participants are not influenced in their phase 3 choices following exposure to their partner in phase 2. To further confirm this we also analysed absolute change in median participant beliefs between phase 1 and 3 under the assumption that M1 and M3 was the dominant model for both groups (that allow for contagion to occur). This analysis aligns with our primary model comparison using M1 for CON and M4 for BPD  (Figure 2C). CON participants altered their median beliefs between phase 1 and 3 more than BPD participants (M1: linear estimate = 0.67, 95%CI: 0.16, 1.19; t = 2.57, p = 0.011; M3: linear estimate = 1.75, 95%CI: 0.73, 2.79; t = 3.36, p < 0.001). Relative reward was overall more susceptible to contagion versus absolute reward (M1: linear estimate = 1.40, 95%CI: 0.88, 1.92; t = 5.34, p<0.001; M3: linear estimate = 2.60, 95%CI: 1.57, 3.63; t = 4.98, p < 0.001). There was an interaction between group and belief type under M3 but not M1 (M3: linear estimate = 2.13, 95%CI: 0.09, 4.18, t = 2.06, p=0.041). There was only a main effect of belief type on precision under M3 (linear estimate = 0.47, 95%CI: 0.07, 0.87, t = 2.34, p = 0.02); relative reward preferences became more precise across the board. Derived model estimates of preference change between phase 1 and 3 strongly correlated between M1 and M3 along both belief types (see Table S2 and Fig S11).’

‘My second concern pertains to the psychometric individual difference analyses. These were not clearly justified in the introduction, though I agree that they could offer potentially meaningful insight into which scales may be most related to model parameters of interest. So, perhaps these should be earmarked as exploratory and/or more clearly argued for. Crucially, however, these analyses appear to have been conducted on the full sample without considering the group structure. Indeed, many of the scales on which there are sizable group differences are also those that show correlations with psychometric scales. So, in essence, it is unclear whether most of these analyses are simply recapitulating the between-group tests reported earlier in the paper or offer additional insights. I think it's hard to have one's cake and eat it, too, in this regard and would suggest the authors review Preacher et al. 2005, Psychological Methods for additional detail. One solution might be to always include group as a binary covariate in the symptom dimension-parameter analyses, essentially partialing the correlations for group status. I remain skeptical regarding whether there is additional signal in these analyses, but such controls could convince the reader. Nevertheless, without such adjustments, I would caution against any transdiagnostic interpretations such as this one in the Highlights: "Higher reported childhood trauma, paranoia, and poorer trait mentalizing all diminish other-to-self information transfer irrespective of diagnosis." Since many of these analyses relate to scales on which the groups differ, the transdiagnostic relevance remains to be demonstrated.’

We have restructured the psychometric section to ensure transparency and clarity in our analysis. Namely, in response to these comments and those of the other reviewers, we have opted to remove the parameter analyses that aimed to cross-correlate psychometric scores with latent parameters from different models: as the reviewer points out, we do not have parity between dominant models for each group to warrant this, and fitting the same model to both groups artificially makes the parameters qualitatively different. Instead we have opted to focus on social contagion, or rather restrictions on , between phases 1 and 3 explained by M3. This provides us with an opportunity to examine social contagion on the whole population level isolated from self-insertion biases. We performed bootstrapping (1000 reps) and permutation testing (1000 reps) to assess the stability and significance of each edge in the partial correlation network, and then applied FDR correction (p[fdr]), thus controlling for multiple comparisons. We note that while we focused on M3 to isolate the effect across the population, social contagion across both relative and absolute reward under M3 strongly correlated with social contagion under M1 (see Fig S11).

‘We explored whether social contagion may be restricted as a result of trauma, paranoia, and less effective trait mentalizing under the assumption of M3 for all participants (where everyone is able to be influenced by their partner). To note, social contagion under M3 was highly correlated with contagion under M1 (see Fig S11). We conducted partial correlation analysis to estimate relationships conditional on all other associations and retained all that survived bootstrapping (1000 reps), permutation testing (1000 reps), and subsequent FDR correction. Persecution and CTQ scores were both moderately associated with MZQ scores (RGPTSB r = 0.41, 95%CI: 0.23, 0.60, p = 0.004, p[fdr]=0.043; CTQ r = 0.354 95%CI: 0.13, 0.56, p=0.019, p[fdr]=0.02). MZQ scores were in turn moderately and negatively associated with shifts in prosocial-competitive preferences () between phase 1 and 3 (r = -0.26, 95%CI: -0.46, -0.06, p=0.026, p[fdr]=0.043). CTQ scores were also directly and negatively associated with shifts in individualistic preferences (; r = -0.24, 95%CI: -0.44, -0.13, p=0.052, p[fdr]=0.065). This provides some preliminary evidence that trauma impacts beliefs about individualism directly, whereas trauma and persecutory beliefs impact beliefs about prosociality through impaired mentalising (Figure 4A).’

(1) As far as I could tell, the authors didn't provide an explanation of this finding on page 5: "However, CON participants made significantly fewer prosocial choices when individualistic choices were available" While one shouldn't be forced to interpret every finding, the paper is already in that direction and I found this finding to be potentially relevant to the BPD-control comparison.

Thank you for this observation. This sentance reports the fact that CON participants were effectively more selfish than BPD participants. This is captured by the lower value of reported in Figure 2, and suggests that CON participants were more focused on absolute value – acting in a more ‘economically rational’ manner – versus BPD participants. This fits in with our fourth paragraph of the discussion where we discuss prior work that demonstrates a heightened social focus in those with BPD. Indeed, the finding the reviewer highlights further emphasises the point that those with BPD are much more sensitive, and motived to choose, options concerning relative reward than are CON participants. The text in the discussion reads:

‘We also observe this in self-generated participant choice behaviour, where CON participants were more concerned over absolute reward versus their BPD counterparts, suggesting a heighted focus on relative vs. absolute reward in those with BPD.’

(2) The adaptive algorithm for adjusting partner behavior in Phase 2 was clever and effective. Did the authors conduct a manipulation check to demonstrate that the matching resulted in approximately 50% difference between one's behavior in Phase 1 and the partner in Phase 2? Perhaps Supplementary Figure suffices, but I wondered about a simpler metric.

Thanks for this point. We highlight this in Figure 3B and within the same figure legend although appreciate the panel is quite small and may be missed.  We have now highlighted this manipulation check more clearly in behavioural analysis section of the main text:

‘Server matching between participant and partner in phase 2 was successful, with participants being approximately 50% different to their partners with respect to the choices each would have made on each trial in phase 2 (mean similarity=0.49, SD=0.12).’

(3) The resolution of point-range plots in Figure 4 was grainy. Perhaps it's not so in the separate figure file, but I'd suggest checking.

Apologies. We have now updated and reorganised the figure to improve clarity.

(4) p. 21: Suggest changing to "different" as opposed to "opposite" since the strategies are not truly opposing: "but employed opposite strategies."

We have amended this.

(5) p. 21: I found this sentence unclear, particularly the idea of "similar updating regime." I'd suggest clarifying: "In phase 2, CON participants exhibited greater belief sensitivity to new information during observational learning, eventually adopting a similar updating regime to those with BPD."

We have clarified this statement:

‘In observational learning in phase 2, CON participants initially updated their beliefs in response to new information more quickly than those with BPD, but eventually converged to a similar rate of updating.’

(6) p. 23: The content regarding psychosis seemed out of place, particularly as the concluding remark. I'd suggest keeping the focus on the clinical population under investigation. If you'd like to mention the paradigm's relevance to psychosis (which I think could be omitted), perhaps include this as a future direction when describing the paradigm's strengths above.

We agree the paragraph is somewhat speculative. We have omitted it in aid of keeping the messaging succinct and to the point.

(7) p. 24: Was BPD diagnosis assess using unstructured clinical interview? Although psychosis was exclusionary, what about recent manic or hypomanic episodes or Bipolar diagnosis? A bit more detail about BPD sample ascertainment would be useful, including any instruments used to make a diagnosis and information about whether you measured inter-rater agreement.

Participants diagnosed with BPD were recruited from specialist personality disorder services across various London NHS mental health trusts. The diagnosis of BPD was established by trained assessors at the clinical services and confirmed using the Structured Clinical Interview for DSM-IV (SCID-II) (First et al., 1997). Individuals with a history of psychotic episodes, severe learning disability or neurological illness/trauma were excluded. We have now included this extra detail within our methods in the paper:

‘The majority of BPD participants were recruited through referrals by psychiatrists, psychotherapists, and trainee clinical psychologists within personality disorder services across 9 NHS Foundation Trusts in the London, and 3 NHS Foundation Trusts across England (Devon, Merseyside, Cambridgeshire). Four BPD participants were also recruited by self-referral through the UCLH website, where the study was advertised. To be included in the study, all participants needed to have, or meet criteria for, a primary diagnosis of BPD (or emotionally-unstable personality disorder or complex emotional needs) based on a professional clinical assessment conducted by the referring NHS trust (for self-referrals, the presence of a recent diagnosis was ascertained through thorough discussion with the participant, whereby two of the four also provided clinical notes). The patient participants also had to be under the care of the referring trust or have a general practitioner whose details they were willing to provide. Individuals with psychotic or mood disorders, recent acute psychotic episodes, severe learning disability, or current or past neurological disorders were not eligible for participation and were therefore not referred by the clinical trusts.‘

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this paper Kawasaki et al describe a regulatory role for the PIWI/piRNA pathway in rRNA regulation in Zebrafish. This regulatory role was uncovered through a screen for gonadogenesis defective mutants, which identified a mutation in the meioc gene, a coiled-coil germ granule protein. Loss of this gene leads to redistribution of Piwil1 from germ granules to the nucleolus, resulting in silencing of rRNA transcription.

Strengths:

Most of the experimental data provided in this paper is compelling. It is clear that in the absence of meioc, PiwiL1 translocates in to the nucleolus and results in down regulation of rRNA transcription. the genetic compensation of meioc mutant phenotypes (both organismal and molecular) through reduction in PiwiL1 levels are evidence for a direct role for PiwiL1 in mediating the phenotypes of meioc mutant.

Weaknesses:

Questions remain on the mechanistic details by which PiwiL1 mediated rRNA down regulation, and whether this is a function of Piwi in an unperturbed/wildtype setting. There is certainly some evidence provided in support of the natural function for piwi in regulating rRNA transcription (figure 5A+5B). However, the de-enrichment of H3K9me3 in the heterozygous (Figure 6F) is very modest and in my opinion not convincingly different relative to the control provided. It is certainly possible that PiwiL1 is regulating levels through cleavage of nascent transcripts. Another aspect I found confounding here is the reduction in rRNA small RNAs in the meioc mutant; I would have assumed that the interaction of PiwiL1 with the rRNA is mediated through small RNAs but the reduction in numbers do not support this model. But perhaps it is simply a redistribution of small RNAs that is occurring. Finally, the ability to reduce PiwiL1 in the nucleolus through polI inhibition with actD and BMH-21 is surprising. What drives the accumulation of PiwiL1 in the nucleolus then if in the meioc mutant there is less transcription anyway?

Despite the weaknesses outlined, overall I find this paper to be solid and valuable, providing evidence for a consistent link between PIWI systems and ribosomal biogenesis. Their results are likely to be of interest to people in the community, and provide tools for further elucidating the reasons for this link.

The amount of cytoplasmic rRNA in piwi+/- was increased by 26% on average (figure 5A+5B), the amount of ChiP-qPCR of H3K9 was decreased by about 26% (Figure 6F), and ChiP-qPCR of Piwil1 was decreased by 35% (Figure 6G), so we don't think there is a big discrepancy. On the other hand, the amount of ChiP-qPCR of H3K9 in meioc^mo/mo was increased by about 130% (Figure 6F), while ChiP-qPCR of Piwil1 was increased by 50%, so there may be a mechanism for H3K9 regulation of Meioc that is not mediated by Piwil1. As for what drives the accumulation of Piwil1 in the nucleolus, although we have found that Piwil1 has affinity for rRNA (Fig. 6A), we do not know what recruits it. Significant increases in the 18-35nt small RNA of 18S, 28S rRNAs and R2 were not detected in meioc^mo/mo testes enriched for 1-8 cell spermatogonia, compared with meioc^+/mo testes. The nucleolar localization of Piwil1 has revealed in this study, which will be a new topic for future research.

Reviewer #2 (Public review):

Summary:

In this study, the authors report that Meioc is required to upregulate rRNA transcription and promote differentiation of spermatogonial stem cells in zebrafish. The authors show that upregulated protein synthesis is required to support spermatogonial stem cells' differentiation into multi-celled cysts of spermatogonia. Coiled coil protein Meioc is required for this upregulated protein synthesis and for increasing rRNA transcription, such that the Meioc knockout accumulates 1-2 cell spermatogonia and fails to produce cysts with more than 8 spermatogonia. The Meioc knockout exhibits continued transcriptional repression of rDNA. Meioc interacts with and sequesters Piwil1 to the cytoplasm. Loss of Meioc increases Piwil1 localization to the nucleolus, where Piwil1 interacts with transcriptional silencers that repress rRNA transcription.

Strengths:

This is a fundamental study that expands our understanding of how ribosome biogenesis contributes to differentiation and demonstrates that zebrafish Meioc plays a role in this process during spermatogenesis. This work also expands our evolutionary understanding of Meioc and Ythdc2's molecular roles in germline differentiation. In mouse, the Meioc knockout phenocopies the Ythdc2 knockout, and studies thus far have indicated that Meioc and Ythdc2 act together to regulate germline differentiation. Here, in zebrafish, Meioc has acquired a Ythdc2-independent function. This study also identifies a new role for Piwil1 in directing transcriptional silencing of rDNA.

Weaknesses:

There are limited details on the stem cell-enriched hyperplastic testes used as a tool for mass spec experiments, and additional information is needed to fully evaluate the mass spec results. What mutation do these testes carry? Does this protein interact with Meioc in the wildtype testes? How could this mutation affect the results from the Meioc immunoprecipitation?

Stem cell-enriched hyperplastic testes came from wild-type adult sox17::GFP transgenic zebrafish. Sperm were found in these hyperplastic testes, and when stem cells were transplanted, they self-renewed and differentiated into sperm. It is not known if the hyperplasias develop due to a genetic variant in the line. We added the following comment in L201-204.

“The SSC-enriched hyperplastic testes, which are occasionally found in adult wildtype zebrafish, contain cells at all stages of spermatogenesis. Hyperplasia-derived SSCs self-renewed and differentiated in transplants of aggregates mixed with normal testicular cells.”

Reviewer #3 (Public review):

Summary:

The paper describes the molecular pathway to regulate germ cell differentiation in zebrafish through ribosomal RNA biogenesis. Meioc sequesters Piwil1, a Piwi homolog, which suppresses the transcription of the 45S pre-rDNA by the formation of heterochromatin, to the perinuclear bodies. The key results are solid and useful to researchers in the field of germ cell/meiosis as well as RNA biosynthesis and chromatin.

Strengths:

The authors nicely provided the molecular evidence on the antagonism of Meioc to Piwil1 in the rRNA synthesis, which supported by the genetic evidence that the inability of the meioc mutant to enter meiosis is suppressed by the piwil1 heterozygosity.

Weaknesses:

(1) Although the paper provides very convincing evidence for the authors' claim, the scientific contents are poorly written and incorrectly described. As a result, it is hard to read the text. Checking by scientific experts would be highly recommended. For example, on line 38, "the global translation activity is generally [inhibited]", is incorrect and, rather, a sentence like "the activity is lowered relative to other cells" is more appropriate here. See minor points for more examples.

Thank you for pointing that out. I corrected the parts pointed out.

(2) In some figures, it is hard for readers outside of zebrafish meiosis to evaluate the results without more explanation and drawing.

We refined Figure 1A and added explanation about SSC, sox17::egfp positive cells, and the SSC-enriched hyperplastic testis in L155-158.

(3) Figure 1E, F, cycloheximide experiments: Please mention the toxicity of the concentration of the drug in cell proliferation and viability.

When testicular tissue culture was performed at 0.1, 1, 10, 100, 250, and 500mM, abnormal strong OP-puro signals including nuclei were found in cells at 10mM or more. We added the results in the Supplemental Figure S2G. In addition, at 1mM, growth was perturbed in fast-growing 32≤-cell cysts of spermatogonia, but not in 1-4-cell spermatogonia, as described in L127-130.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

I don't have any recommendations for improvement. While I have outlined some of the weaknesses of the paper above. I don't see addressing these questions as pertinent for publication of this paper.

Reviewer #2 (Recommendations for the authors):

(1) The manuscript uses the terms 1-2 cell spermatogonia, GSC, and SSC throughout the figures and text. For example, 1-2 cell spermatogonia is used in Figure 1C, GSC is used in Figure 1F, and SSC is used in Figure 1 legend. The use of all three terms without definitions as to how they each relate with one another is confusing, particularly to those outside the zebrafish spermatogenesis field. It would be best to only use one term if the three terms are used interchangeably or to define each term if they represent different populations.

GSC is a writing mistake. In this study, sox17-positive cells, which have been confirmed to self-renew and differentiate (Kawasaki et al., 2016), are considered SSCs. On the other hand, a comparison of meioc and ythdc2 mutants revealed differences in the composition of each cyst, so we describe the number of cysts confirmed. We added new data that 1-2 cell spermatogonia are sox17-positive in Supplemental Figure S3 (L157-158).

(2) Figure 1B: What does the "SC" label represent in these figure panels?

We added the explanation in the Figure legend.

(3) Fig 7B and S7B show incongruent results, and the text implies that Fig S7B data better reflects in vivo biology. It is not clear how the authors interpret the different results between 7B and S7B.

Thank you for pointing that out. Fig 7A and 7B were obtained by isolating sox17-positive cells. Because it was difficult to detect nucleoli in the isolated cells, probably due to the isolation procedure, we added S7B, which was analyzed in sectioned tissues. As this reviewer pointed out, S7B reflects the in vivo state better, so we changed S7B to 7B and 7B to S7B.

Reviewer #3 (Recommendations for the authors):

Minor points:

(1) For general readers, it is nice to add a scheme of zebrafish spermatogenesis (lines 77-78) together with Figure 1A.

As mentioned above, we refined Figure 1A.

(2) Line 28, silence: the word "silence" is too strong here since rDNA is transcribed in some levels to ensure the cell survival.

Thank you for your comment. We changed "silence" to "maintain low levels."

(3) Line 60, YTDHC2: Please explain more about what protein YTDHC2 is.

We added a description of Ythdc2 in the introduction.

(4) Line 69, Piwil1: Please explain more about what protein Piwil1 is.

We added a description of Piwil1 in the introduction.

(5) Figure 1B, sperm: Please show clearly which sperms are in this figure using arrows etc.

We represented sperm using arrowheads in Fig 1B.

(6) Figure 1C, SC: Please show what SC is in the legend.

We added the explanation in the Figure legend.

(7) Line 83, meiotic makers: should be "meiotic prophase I makers".

Thank you for pointing out the inaccurate expression description. We revised it.

(8) Line 84, phosphor-histone H3: Should be "histone H3 phospho-S10 "

We revised it.

(9) Figure S1A, PH3: Please add PH3 is "histone H3 phospho-S10 ".

We revised it.

(10) Figure S1A, moto+/-: this heterozygous mutant showed an increased apoptosis. If so, please mention this in the text. If not, please remove the data.

Thank you for pointing that out. The heterozygous mutant did not increase apoptosis, so we removed the data.

(11) Line 88, no females developed: This means all males in the mutant. If so, what Figure S1B shows? These cells are spermatocytes? No "oocytes" developed is correct here?

All meioc^mo/mo zebrafish were males, and the meioc^mo/mo cells in Fig. S1B are spermatogonia. No spermatocytes or oocytes were observed. To show this, we added "no oocytes" in L90.

(12) Line 89, initial stages: What do the initial stages mean here? Please explain.

The “initial stages” was changed to the pachytene stage.

(13) Figure S1C: mouse Meioc rectangle lacks a right portion of it. Please explain two mutations encode a truncated protein in the main text.

I apologize. It seems that the portion was missing during the preparation of the manuscript. We corrected it. In addition, we added a description of the protein truncation in L100-101.

(14) Line 99: What "GRCz11" is.

GRCz11 refers to the version of the zebrafish reference genome assembly. We added this.

(15) Figure S2A: Dotted lines are cysts. If so, please mention it in the legend.

We corrected the figure legend.

(16) Figure S2B and C:, B1-4, C1-7: Rather use spermatogonia etc as a caption here.

We corrected the figure and figure legend.

(17) Line 113, hereafter, wildtype: Should be "wild type" or "wild-type".

We corrected them.

(18) Figure 1C: Please indicate what dotted lines mean here.

We added “Dotted lines; 1-2 cell spermatogonia.”

(19) Line 113, de novo: Please italicize it.

We corrected it.

(20) Line 113-116: Figure 1D shows two populations in the protein synthesis (low and high) in the 1-2-cell stage. Please mention this in the text.

We added mention of two population.

(21) Line 121, in vitro: Please italicize it.

We corrected it.

(22) Line 138-139, Figure 2A: Please indicate two populations in the rRNA concentrations (low and high) in the 1-2-cell stage. How much % of each cell is?

We added mention of two population and % of each cell.

(23) Figure 2B, cytes: Please explain the rRNA expression in spermatocytes (cytes) in the text.

The decrease in rRNA signal intensity in spermatocytes was added.

(24) Figure 2A, lines 147, low signals: Figure 2A did not show big differences between wild type and the mutant. What did the authors mean here? Lower levels of rRNAs in the mutant than in wild type. If so, please write the text in that way.

We think that it is important to note that we were unable to find cells with upregulated rRNA signals, and therefore changed to “could not find cells with high signals of rRNAs and Rpl15 in meioc^mo/mo spermatogonia”.

(25) Figure 2E: Please add a schematic figure of a copy of rDNA locus such as Fig. S3A right.

We added a schema of rDNA locus and primer sites such as Figure S3A right (now Figure 2F) in Figure 2E.

(26) Figure S3A: This Figure should be in the main Figure. The quantification of Northern blots should be shown as a graph with statistical analysis.

We added the quantification and transfer to the main Figure (Figure 2F).

(27) Figure 4A: Please show single-color images (red or green) with merged ones.

We added single-color images in the Figure 4A.

(28) Line 198, Piwil1: Please explain what Piwil1 is briefly.

We are sorry, but we could not quite understand the meaning of this comment. To show that Piwil1 is located in the nucleolus, we indicated it as (Figure 4A, arrowhead) in L209.

(29) Line 198, Ddx4-positive: What is "Ddx4-positive"? Explain it for readers.

Ddx4 is a marker for germinal granules, and the description was changed to reflect this.

(30) Line 209, Fig. S4D-G: Please mention the method of the detection of piRNA briefly.

We have described that we have sequenced small RNAs of 18-35 nt. Accordingly, we changed the term piRNA to small RNA.

(31) Line 217: Please mention piwil1 homozygous mutant are inviable.

We added that piwil1-/- are viable in L231.

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Reply to the reviewers

Reviewer #1

__Evidence, reproducibility and clarity __

The manuscript explores mild physiological and metabolic disturbances in patient-derived fibroblasts lacking G6Pase expression, suggesting that these cells retain a "distinctive disease phenotype" of GSD1a. The manuscript is well written with well-designed experiments. However, it remains unclear whether these phenotypes genuinely reflect the pathology of GSD1a-relevant tissues. The authors did not validate these findings in a liver-specific G6pc knockout mouse model, raising concerns about the study's relevance to GSD1a. Additionally, the lack of sufficient in vivo evidence undermines the therapeutic potential of GHF201 for this disease. Overall, the study lacks a few key pieces of evidence to completely justify its conclusions at both fundamental and experimental levels.

__Reply:__We thank the reviewer for this general comment which gives us the opportunity to better explain the scope of our work. The purpose and focus of this work are not to test the pathological relevance of skin fibroblasts to GSD1a pathology. We do not claim that skin fibroblasts are involved in GSD1a pathogenesis. It is also not a developmental work claiming to uncover GSD1a pathogenic axis throughout embryonic development. As a matter of fact, since skin fibroblasts originate from the mesoderm embryonic germ layer and hepatocytes develop from the endoderm embryonic germ layer, it would even be unlikely that the pathological phenotype found in skin fibroblasts directly contributes to GSD1a pathology in model mice or in patients. Indeed, we are not aware of any dermatological contribution to GSD1a pathology in patients. However, our results suggest that in addition to the established and mutated organ (liver in the liver-specific G6pc knockout mouse model), other, relatively less studied, patho-mechanisms in distal tissues may also contribute to GSD1a pathology. Notably, this work is also not testing a therapeutic modality for GSD1a. Our work uses GSD1a disease models as a tool for demonstrating, or reviving, the concept of epigenomic landscape (Waddington, 1957): Different cell phenotypes, such as healthy and diseased, are established by innate metabolic differences between their respective cell environments, which impose epigenetic changes generating these different phenotypes. In this respect, our manuscript has a similar message to the one in the recently published paper Korenfeld et al (2024) Nucleic Acids Res 53:gkae1161. doi: 10.1093/nar/gkae1161: The Kornfeld et al paper shows that intermittent fasting generates an epigenetic footprint in PPARα-binding enhancers that is "remembered" by hepatocytes leading to stronger transcriptional response to imposed fasting by up-regulation of ketogenic pathways. In the same way, the diseased GSD1a status imposes metabolic changes, as detailed here, leading to permanent epigenetic changes, also described here, which are "remembered" by GSD1a fibroblasts and play a major role in the transcription of pathogenic genes in these patient's cells. This in turn is how the diseased state is preserved, even in cells not expressing the G6Pase mutant, which is the direct cause of the disease. We added this perspective to the Discussion to better highlight the key takeaway from our manuscript.Naturally, research such as ours with a claim on biological memory would involve ex vivo experiments where tissues are isolated from their in-situ environments and tested for preservation of the original in situ phenotype. The few in vivo experiments we performed (Fig. 5) are mainly aimed at demonstrating that not only the phenotype, but also therapy response is "remembered" ex vivo: In the same way that the G6PC-loss-of-function liver responded positively to GHF201 therapy in situ, ex vivo cells not expressing G6PC also responded positively to the same therapy. This observation only demonstrates further support for "memorization" of the disease phenotype by cell types not expressing the mutant: Both the diseased phenotype and response to therapy were preserved ex vivo.Lastly, while interesting, validation of our findings in vivo (as suggested by the reviewer) is not related to the scope of this manuscript. Such experiments, using the liver-targeted G6pc knockout mouse model, are the follow-up story, which is related to the origin of inductive signals that cause the curious and novel phenotype mechanism in GSD1a fibroblasts described in this manuscript. The scope and volume of such research constitute a novel manuscript.

Since dietary restriction is the only management strategy for GSD1a, the authors should clarify whether the patient fibroblast donors were on a dietary regimen and for how long. Given that fibroblasts do not express G6Pase, it is possible that the observed phenotype could be influenced by the patient's diet history.

__Reply:__We thank the reviewer for this important comment, we agree that it is important to note the dietary regimen assigned to the cohort of patients described in this study. We added an explanation to the manuscript on patient's diets as shown below.Briefly, all patients besides patient 6894 were treated with the recommended dietary regimen for GSD1a as explained in Genereviews (Bali et al (2021)). This dietary treatment (now added to the Methods section in the manuscript) allows to maintain normal blood glucose levels, prevent secondary metabolic derangements, and prevent long-term complications. Specifically, this dietary treatment includes- nocturnal nasogastric infusion of a high glucose formula in addition to usual frequent meals during. By constantly maintaining a nearly normal level of blood glucose, this treatment causes a remarkable decrease, although not normalization, of blood lactate, urate and triglyceride levels, as well as bleeding time values. A second layer in the treatment includes the use of uncooked starch in the dietary regimen to allow maintenance of a normal blood glucose levels for long periods of time. Patient 6894 did not tolerate well the uncooked cornstarch and therefore was treated with a tailored dietary treatment planned by metabolic disease specialists and dedicated certified dieticians highly experienced with the management of pediatric and adult patients with GSDs and other inborn errors of metabolism. The biopsies of patients were taken in the range of 3 month to several years from receiving the aforementioned dietary regimen.Importantly, the strict metabolic diet imposed on GSD1a patients might influence the observed phenotype described throughout the manuscript. This concept aligns with our claim that the GSD1a skin cells are affected by the dysregulated metabolism in patients in comparison to healthy individuals. Interestingly, while patient 0762 harbors a mutation in the SI gene in addition to the G6PC mutation and patient 6894 did not receive the same dietary regimen as other patients (as explained above), all patients do show similar disease related phenotypes, perhaps highlighting the role of an early programing process that affected these cells due to the severe metabolic aberrations presented in this disease from birth.One of the main pathological features of GSD1a is glycogen buildup. The authors should compare glycogen levels between healthy controls and GSD1a fibroblasts and provide a dot plot analysis.

One of the main pathological features of GSD1a is glycogen buildup. The authors should compare glycogen levels between healthy controls and GSD1a fibroblasts and provide a dot plot analysis.

__Reply:__We thank the reviewer for this important comment. We added glycogen levels of HC to Figure S2A and accordingly also edited the relevant text in the Results section.

Figure S2A - As mentioned above, the authors should present healthy control vs. patient fibroblast glycogen data. Without this, the rationale for using GHF201 is questionable.

__Reply:__We thank the reviewer for this important comment. We added glycogen levels of HC to Figure S2A as mentioned above.

Figure S2B-C - If the authors propose that GHF201 reduces glycogen and increases intracellular glucose in GSD1a fibroblasts, they need direct evidence. Either directly quantifying glycogen levels or even better would be a labeling experiment to confirm that the free intracellular glucose originates from glycogen. Additionally, the reduction in sample size from N=24 in glycogen analysis to N=3 in the glucose assay needs justification.

__Reply:__We thank the reviewer for this comment. To clarify, the results shown in Figure S2A left are based on PAS assay, directly quantifying glycogen in cells with and without GHF201 treatment. We have now added HC glycogen levels as requested above. Regarding N, this is explained in Methods: In imaging experiments N was determined based on wells from the experiments done in three independent plates following the rationale that each well is independent from the others and reflects a population of hundreds of cells as previously described in (Lazic SE, Clarke-Williams CJ, Munafò MR (2018) What exactly is 'N' in cell culture and animal experiments?. PLOS Biology 16(4):e2005282. https://doi.org/10.1371/journal.pbio.2005282, Gharaba S, Sprecher U, Baransi A, Muchtar N, Weil M. Characterization of fission and fusion mitochondrial dynamics in HD fibroblasts according to patient's severity status. Neurobiol Dis. 2024 Oct 15;201:106667. doi: 10.1016/j.nbd.2024.106667. Epub 2024 Sep 14. PMID: 39284371.). Figure S2A right shows the glucose quantification experiment that we think the reviewer is referring to. Glucose increase is normally concomitant with glycogen reduction and we therefore show these results in support of the glycogen reduction results. These glucose results are part of our metabolomics results done on the same cells (Figure 6), where glucose is one of the metabolites analyzed. This metabolomics analysis was repeated three times; therefore, N is 3. In summary, these results show that GHF201 directly contributes to glycogen reduction in GSD1a fibroblasts and concomitantly increases glucose levels.

Figure S2B-C- It is not shown how GHF201 increases intracellular glucose? If glycophagy is a possibility, the authors should do an experiment to confirm this.

__Reply:__Assuming the reviewer's comment is related to Figure S2A right, glucose levels are only shown to validate the glycogen reduction results (also see point 4): When glycogen levels are reduced, especially by inhibition of glycogen synthesis, glucose levels are supposed to concomitantly rise, being spared as an indirect substrate of glycogen synthesis. There is no proof, and as a matter of fact we also do not assume, that the GHF201-mediated reduction in glycogen levels is a result of increased glycophagy: Glycophagy has been described in cell types with high glycogen turnover, e.g., muscle and liver cells, not fibroblasts. Additionally, glycophagy is a glycogen-selective process implicating STBD1 whose expression in skin fibroblasts is negligible (https://www.proteinatlas.org/ENSG00000118804-STBD1/tissue).On the other hand, glycogen in GSD1a does not accumulate in lysosomes. It is built up in the cytoplasm (Hicks et al (2011) Ultrastr Pathol 35: 183-196; Hannah et al (2023) Nat Rev Dis Primers DOI: 10.1038/s41572-023-00456-z). Therefore, we do not believe that GHF201 reduced glycogen by enhancing glycophagy. As we show, GHF201 activated several key catabolic pathways. It is more likely that activation of one of these pathways, the AMPK pathway, inhibited glycogen synthesis via phosphorylation and ensuing inhibition of glycogen synthase. Alternatively, excessive cytoplasmic glycogen might enter lysosomes by bulk autophagy, or microautophagy (not by glycophagy) and GHF201 might induce lysosomal glycogenolysis by alpha glucosidase as an established lysosomal activator (Kakhlon et al (2021)). However, since, as explained, the mechanism of action of GHF201 is not the topic of this manuscript and therefore we did not dwell more into that.

Figure 2- How can GSD1a fibroblasts have significantly reduced OCR (Fig. 2B) but increased mitochondrial ATP production (Fig. 2H)?

__Reply:__We thank the reviewer for highlighting this important topic. OCR, measured in Fig. 2B, is an indirect measure of ATP production. Therefore, changes in OCR only measure the capacity of the mitochondria to produce ATP, and not the direct quantity of ATP. Other factors might influence ATP production, e.g., substrate availability and the activity of other metabolic pathways. On the other hand, the ATP Rate Assay (Figure 2h), provides a real-time direct measurement of ATP levels incorporating coupling efficiency and P/O ratio assumptions. Therefore, these two measurements do not necessarily match. We will add this information to the relevant segment in the text to clarify why OCR is reduced and mitochondrial ATP production increased in GSD1a cells.

Why do GSD1a fibroblasts show reduced glycolytic ATP (Figure 2h) despite increased glycolysis and glycolytic capacity (Fig 2J-K)?

__Reply:__We thank the reviewer for highlighting this important topic. ECAR measures medium acidification and thus reflects the production of lactic acid, which is a byproduct of glycolysis. However, medium acidification is also influenced by other factors that can acidify the extracellular environment, especially CO2 production which can originate from the intramitochondrial Krebs cycle which produces reductive substrates for mitochondrial respiration, or OCR. Moreover, the buffering capacity of the Seahorse mito stress assay medium might mask changes in lactic acid production, leading to an underestimation of glycolytic activity. On the other hand, glycolytic ATP production measured by the ATP rate assay directly quantifies the rate of ATP production from glycolysis. Notably, there is a major difference between ECAR and the ATP rate assay: The ATP rate assay is less sensitive to variations in buffering capacity than ECAR measurements. This is because the ATP rate assay relies on inhibitor-driven changes in OCR and ECAR, rather than absolute pH values.Teleologically, as indicated, the increased ECAR in GSD1a cells represents a known compensatory response to deficient ATP production which is stimulation of glycolysis (Figure 2i). To test the success of this known compensatory attempt, we applied the real-time ATP rate assay, but as explained they do not report the same entities. We will add this information to the relevant segment in the text to clarify how reduced glycolytic ATP can be co-observed with increased glycolytic capacity.

The authors should clarify how many healthy control and patient fibroblast lines were compared per experiment. Given the wide age range, the unexpectedly small error bars raise concerns about variability and statistical robustness.

Reply:__We thank the reviewer for raising this topic. Number of samples per experiment is reported in the Methods section. As for the age range, patients age was matched to healthy controls to account for age differences and experiments were performed under similar passages range. This procedure allowed us to control for technical differences between samples that might arise due to different passages and ages. Importantly, the cohort of samples used in this manuscript included GSD1a patients with different ages further implying the strength of the observed disease phenotype found in patients' cells which exists regardless of the different age and gender of patients. The HC samples were chosen to match age and gender and passages were used in the recommended range (L. Hayflick,The limited in vitro lifetime of human diploid cell strains,Experimental Cell Research,Volume 37, Issue 3,1965,Pages 614-636, änzelmann S, Beier F, Gusmao EG, Koch CM, Hummel S, Charapitsa I, Joussen S, Benes V, Brümmendorf TH, Reid G, Costa IG, Wagner W. Replicative senescence is associated with nuclear reorganization and with DNA methylation at specific transcription factor binding sites. Clin Epigenetics. 2015 Mar 4;7(1):19. doi: 10.1186/s13148-015-0057-5. PMID: 25763115; PMCID: PMC4356053., Magalhães, S.; Almeida, I.; Pereira, C.D.; Rebelo, S.; Goodfellow, B.J.; Nunes, A. The Long-Term Culture of Human Fibroblasts Reveals a Spectroscopic Signature of Senescence. Int. J. Mol. Sci. __2022, 23, 5830. https://doi.org/10.3390/ijms23105830). Finally, for the error bars, assuming the reviewer is addressing this for all experiments, this means that results are consistent across each compared group and reflects robustness of the results. Further, to ensure statistical robustness we used bootstrapping, 95% confidence intervals and other statistical methodologies that were designed to increase the validity of the conclusions drawn from different experiments.

Figure 5- The study should include Tamoxifen-untreated mice as a control to properly assess the efficacy of GHF201 in regulating glucose-6-P and glycogen levels.

__Reply:__GHF201 reduced liver glucose-6-phosphate (G6P) with p-/-* mice livers and their normalization by GHF201.

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

General comments: the authors propose a very intriguing concept, that metabolic abnormalities trigger epigenetic changes in tissues distal from the disease site, even in cells in which the affected gene is not expressed. This is demonstrated in primary fibroblasts from patients with Glycogen Storage Disease type 1a (GSD1a). The authors provide a large amount of data to support the compelling concept of "Disease-Associated Programming", a term that they have coined to describe this effect. The level of novelty is very high and so is the impact of the study, since the above may apply to many different pathological conditions. Although, the study is well performed and employs multiple approaches and analyses to address the raised hypothesis, there are some limitations and concerns that need to be addressed by the authors.

__Reply:__We thank the reviewer for this comment and will address each comment raised.

The different phenotypic characteristics are only demonstrated in skin fibroblasts which is not sufficient to support the conclusions made in the Discussion about the general applicability of the proposed disease-induced, metabolite-driven epigenetic programming to all cells and tissues. The authors should discuss this as a limitation of the study and general conclusions should be formulated with more caution.

__Reply:__We concur with this comment and accept that this is a general limitation of the study. We added a reservation clause at the beginning of the Discussion section.

The authors describe a range of alterations in patients' fibroblasts as compared to healthy control fibroblasts. However, they draw parallels to the liver which is the organ primarily affected by GSD1a, stating that tissues other than the liver such as skin fibroblasts phenocopy the liver pathology (Discussion). Extrapolation of the findings to the liver is also made in the section "ATAC-seq, RNA-seq and EPIC methylation data integration". Here, the authors comment on the finding that identified genes are associated with tumour formation and draw parallels to hepatocellular carcinoma which is an important co-morbidity of GSD1a. These correlations, although interesting, should be presented as indications and not as "strong links". A major difference between fibroblasts and liver cells in the case of GSD1a is the massive accumulation of glycogen in the liver. This is a major metabolic feature which largely defines the disease's pathology. In addition to the similarities in the pathological features between the liver and other tissues such as fibroblasts, the authors should highlight this major difference and discuss their findings within this context.

__Reply:__We thank the reviewer for this important comment. We have toned down the language correlating the regulation of gene expression between fibroblasts and liver in GSD1a. We have also alluded to the key metabolic difference between fibroblasts and liver - glycogen levels and turnover - in the second paragraph of the Discussion. We are aware that if our deep analyses were conducted on a different tissue with different basal metabolism the results might have been different. However, the GSD1a-pathogenic findings in fibroblasts suggest that they might also contribute to pathology in situ, perhaps by modulating the expression of functionally redundant genes.

For basically all experiments performed in the study the authors follow the approach of culturing cells for 48 hours under serum and glucose starvation, followed be 24-hour cultivation in complete medium. This was practiced in a previous study by the authors (PMID: 34486811) to enhance the levels of glycogen in skin fibroblasts of patients with Adult Polyglucosan Body Disease. For the current study the selection of this treatment protocol is not sufficiently justified. Although, differences are described between patients' fibroblasts and controls under these conditions, it would have been interesting to address the reported parameters also at standard culturing conditions. This might be too much to ask for the purposes of this revision, but the authors may provide a better justification for the selection of the above treatment protocol and discuss whether the described phenotypic features are constitutive abnormalities present at all times or are induced by the metabolic stress imposed to the cells through this treatment.

__Reply:__We thank the reviewer for pointing this important topic. Previously, we used the 72 h condition (48 h starvation followed by 24 h glucose supplementation) to attain two goals: generation of glycogen burden by excessive glucose re-uptake after glucose starvation and induction of basal autophagy by serum starvation so as to sensitize detection of the action of the autophagic activator GHF201 on a background of already induced autophagy. As stated, this 72 h condition was used previously in other GSD cell models (Kakhlon et al (2021) - GSDIV, Mishra et al (2024) - GSDIII, GSDII - in preparation), so we decided to use it in this work as well to enable cross-GSD comparison of GHF201 efficacy in GSD cell models. Moreover, as shown in Figure 1, the largest differences between HC and GSD1a fibroblasts, especially in lysosomal and mitochondrial features, were observed at the 72 h time condition. We therefore used this condition in all other fibroblasts experiments presented in this manuscript. Our ultimate aim was to test whether the metabolic reprograming induced in situ by the patients' diseased state before culturing generates stable epigenetic modifications withstanding seclusion from the original in situ environment. Thus, using the non-physiological 72 h condition, after the fibroblasts were cultured in full media remote from the in situ environment, can only confirm the stability and environment-independence of these metabolically-driven epigenetic modulations. We now provide this justification at the beginning of the Results section.

In the Figures, the authors provide comparisons between controls and patient fibroblasts (+/- GHF201). Although the authors provide the respective p values in all figures, it is not clear which differences are considered significant and which are not. Since some of the indicated p values are > 0.0. The authors should indicate which of these changes are significant or non-significant and these should be presented and discussed accordingly in the text.

__Reply:__We thank the reviewer for highlighting this important topic. We will add this information to the methods segment. Throughout the manuscript, p https://doi.org/10.1080/00031305.2018.1529624, Cumming, G. (2013). The New Statistics: Why and How. Psychological Science, 25(1), 7 29. https://doi.org/10.1177/0956797613504966 (Original work published 2014)). Along with the p values we presented all data points in each comparison and added bootstrap mediated 95 % confidence intervals as well. Since our sample size was small, we chose to focus on effect sizes, to use a higher p value threshold and to implement various advanced methodologies that allowed us to find important biological patterns.

In Figure S2A, the authors show a reduction of glycogen levels in GSD1a fibroblasts following treatment with GHF201. Glycogen accumulation is central to this study, since a) is considered by the authors "a disease marker which is reversed by GHF201" - this is demonstrated in the liver of L.G6pc-/- mice and, according to the authors, replicated in the fibroblasts, b) as suggested by the authors it is the biochemical aberration that drives epigenetic modifications generating "disease memory". It is therefore important to appreciate whether GSD1a cells display pathologically increased levels of glycogen. This is also pertinent to the lack of G6PC expression in fibroblasts. The authors should include in Fig. S2A glycogen measurements of HC control fibroblasts cultured under the same conditions to compare with the levels present in GSD1a cells.

__Reply:__We thank the reviewer for highlighting this issue. We added glycogen levels of HC to Figure 2SA as requested. Expectedly, glycogen levels are similar between HC and GSD1a fibroblasts because neither wild type G6PC1 in HC, or mutated G6PC1 in GSD1a fibroblasts is expressed. We have now corrected the manuscript text suggesting that glycogen is accumulated in GSD1a fibroblasts and rephrased the text to express the more versatile state where epigenetic modulation could be mediated by different metabolic perturbations according to the expression profile: G6PC1 mutant expressers (notably liver and kidney cells) could inhibit p-AMPK by glycogen accumulation, while non-expressers could inhibit p-AMPK by lowering NAD+. Text changes related to this new concept are found in the Results section "Exploring epigenetics as a phenotypic driver in GSD1a fibroblasts by ATAC-seq analysis" and in the Discussion section "Metabolic-driven, disease-associated programming of cell memory."

Comparisons between protein levels (AMPK/pAMPK, Sirt1, TFEB, p62 ane PGC1a) are made on the basis of fluorescence intensity in immunostained cells. These results need to be supported by relevant western blot images to exclude that binding of the antibodies to unspecific sites contributes to the measured fluorescence.

__Reply:__We thank the reviewer for this comment allowing us to clarify the reasoning behind the selected methods for the main markers identification. Throughout the manuscript we employed both Western blot and immunofluorescence experiments. We believe that immunofluorescence present as a more robust and efficient method for the following reasons: i. It allows to focus on proteins in their native state; ii. Immunofluorescence allows to observe proteins in relation to their location in the cells (for example TFs in nuclei area); iii. Immunofluorescence allows to focus on each cell and exclude cells which are dead, stressed or with a low viability characteristic; iv. Immunofluorescence allows to generate much more data. For the following reasons, the main proteins explored in this work we used immunofluorescence, in each immunofluorescence experiment we added a control for the secondary antibody alone, verifying the signal is related to the antibodies only. This information can be added if requested. Importantly, some of the antibodies used were recommended for immunofluorescence and not for Western blot. As the reviewer requested, we now provide western blot results for proteins that produced a signal with the antibodies in Western blots, all markers mentioned except TFEB were added to Figure S3 d.

The authors demonstrate that treatment of GSD1a fibroblasts with histone deacetylase inhibitors reverses some of the phenotypic alterations. Given that GHF201 also improves these phenotypic differences it would be interesting to address whether GHF201 has any effect on histone acetylation.

Reply: We strongly agree with this comment and have therfore tested for the effect of GHF201 on H3K27 acetylation levels as shown in Fiugre 3f and on the deacetylase -SIRT-1 as shown in Figure 3e, Figure S3d and representative images in Figure S2b.

The authors report reduced levels of the transcription factors PGC1α and TFEB in GSD1a fibroblasts. Does this correlate with lower levels of expression of PGC1α and TFEB target genes in the RNA-seq experiments?

Reply:

We thank the reviewer for raising this topic, since there were thousands of differentially expressed genes and we cannot mention all we focused on the most important ones that comprise key pathways we wanted to highlight as described in the Results section. We have now linked in the Results section examples of PGC1α and TFEB target genes that were reduced due to lower levels of these transcription factors in GSD1a, as compared to HC cells. Importantly, a full list of the genes from the RNA-seq experiment can be found in Table S3. Genes regulated by TFEB contain the CLEAR (Coordinated Lysosomal Expression and Regulation) motif. Two notable genes regulated by CLEAR binding TFs such as TFEB, which are very important biologically, are cathepsin L and S (Figure 6A right) both of which were reduced in GSD1a and are now elaborated in the Results section referring to Figure 6a right. Additionally, Table S3 shows differentially expressed genes in GSD1a cells where there are many other lysosomal related genes that are downmodulated in GSD1a, we now added another important example, ATP6V0D2 to the Discussion as the reviewer suggested. As for PGC1alpha, a notable gene whose expression is up-modulated by PGC1alpha, which is down-modulated in GSD1a, is ALDH1A1 (Figure 6a right). In addition, we have now added PPARG and its coactivators alpha and beta to the discussion as requested by the reviewer, these genes are shown in Table S3 and are downmodulated in GSD1a. Finally, the transcriptional effect of PGC1alpha and TFEB is also mentioned in the Discussion within the cell phenotyping section, where we describe the deep impact of dysregulation of NAD+/NADH-Sirt-1-TFEB regulatory axis on the cell phenotype at all the levels described in the manuscript.

Please revise the following sentences as the statements made are not adequately supported by the provided data a. "This NAD+/NADH increase correlated with reduced cytotoxicity and increased cell confluence (Figure 3d) suggesting that NAD+ availability prevails over ATP availability as an effector of cell thriving in GSD1a cells."

__Reply:__If one ranks treatments according to NAD+/NADH (Figure 3c) and according to cytotoxicity (Figure 3d left) and cell confluence (Figure 3d right), then the mentioned correlation can be supported. ATP availability is compromised by gramicidin, yet gramicidin, which also increased NAD+/NADH, reduced cytotoxicity and enhanced cell confluence.

b. "....in further support that respiration-dependent NAD+ availability mediate GHF201's corrective effect in GSD1a cells."

__Reply:__Our data (Figure 3c) show that GHF201 increased NAD+/NADH both alone and with gramicidin.

Please indicate on the densitometry graph of Fig. 10b the treatment (HDACi), for better visibility.

__Reply:__We agree and have corrected the Figure as requested.

The reference list (n=160) is probably too long for a research article.

__Reply:__The number of references reflect the length and depth of the manuscript and we believe that each reference merits its place. We agree that the number of references is large but we are not sure which criteria to use to exclude some references and to reduce them to a more acceptable number that we assume would be determined by the publishing journal.

The study is of high novelty and impact, as it proposes a so far undescribed biological mechanism contributing to disease pathology that could apply for general pathological conditions. Although this is a compelling concept, it is only demonstrated in skin fibroblasts which limits its applicability at an organismal level.

__Reply:__We thank the reviewer for this comment and for raising the important comments that allowed us to improve our manuscript, please see our reply to point 1.

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

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Reply to the reviewers

1. General Statements [optional]

We* thank all three Reviewers for appreciating our work and for sharing constructive feedback to further enhance the quality of our work. It is really gratifying to read that the Reviewers believe that this work will be of interest to broad audience and will be suitable for a high profile journal. Further, the experiments suggested by the reviewers will add value to the work and will substantiate our findings. It is important to highlight that we have already performed most of the suggested experiments except a couple of experiments that we have plan to carry out during full revision. Please find below the details of experiments performed and planned to address the reviewers comments. *

2. Description of the planned revisions

Reviewer #1

Comment 6. In Figure 6A, B, does the Orai3 western blot show any of the heavier bands seen in the ubiquitination IP if you show the whole blot? It should.

Reviewer #2

Comment 5. Fig. 6A and 6B. Show the full Orai3 and Ubiquitin WBs. As presented the figure current just shows that there are ubiquitin proteins in Orai3 pull down, not that Orai3 is ubiquitinated.

Reviewer #3

Comment 3. In the scheme in Fig. 10, the authors highlight that Orai3 is ubiquitinated. Do they have any idea where the site of action of ubiquitination in Orai3 is located?

Response: We thank the Reviewer 1, 2 and 3 regarding their query on the co-immunoprecipitation assays performed for studying Orai3 ubiquitination. The reviewers are asking for ubiquitination status of Orai3 and the potential sites for Orai3 ubiquitination. To address these comments, we are planning to perform co-immunoprecipitation assays with mutated Orai3 with mutations of potential ubiquitination sites. We have already performed bioinformatic analysis and it revealed presence of three potential ubiquitination sites on Orai3: K2 (present on N-terminal region), K274 and K279 (present on C-terminal region). We would mutate these lysine residues on Orai3 protein via site-directed mutagenesis and check the Orai3 ubiquitination status. These experiments will answer the question raised by Reviewers and strengthen the Orai3 ubiquitination data.

Please refer to below diagrammatic illustration showing potential ubiquitination sites on Orai3:

Reviewer #2

Comment 7. Also, all the imaging and pull down do not prove conclusively direct interaction between MARCH8 and Orai3, they rather show that the proteins are in the same complex. Although it is unlikely best for the text to be moderated accordingly.

Response: We understand the concern raised by Reviewer 2 regarding direct or indirect interaction of MARCH8 and Orai3. Hence, we are planning to perform co-immunoprecipitation assays in which we delete the MARCH8 interacting domain in Orai3 protein and check the for direct interaction of these proteins. Bioinformatic analysis and literature survey have highlighted two possible MARCH8 interacting domains in Orai3. The first domain is present in 2nd loop region, present between the 2nd and 3rd transmembrane domains at the LMVXXXL (AA113-120) motif and the second domain is present at the GXXXG (AA235-239) motif, present in the 3rd loop region of Orai3. We will remove these domains from Orai3 protein individually and check its effect on MARCH8 interaction. These experiments will provide conclusive evidence of direct interaction between Orai3 and MARCH8.

Please refer to below diagrammatic illustration displaying potential MARCH8 binding sites on Orai3:

3. Description of the revisions that have already been incorporated in the transferred manuscript

Reviewer #1

Comment 1. The observation that both transcriptional regulation and protein degradation of Orai3 is regulated downstream of one transcription factor is not, in and of itself, entirely surprising. All proteolytic components are transcriptionally regulated and this phenomenon is likely relatively common. However, what I do think is both impressive and important is that the authors have characterized both components of the pathway within a disease context. While I am not going to search the literature for how often transcription and proteolysis are co-regulated for other proteins, it is the case for many short-lived proteins and perhaps many others. As such, discussion throughout the abstract and introduction that co-regulation of these processes is unprecedented should be removed.

Response: We thank the Reviewer for thinking that our work is both impressive and important. Further, we understand the Reviewer’s point that transcription and proteolysis may be co-regulated for other proteins. However, our extensive literature search did not resulted in such scenarios. Therefore, to best of our knowledge, we are revealing for the first time that same transcription factor regulates both transcription and protein degradation of the same target in a context dependent manner in a single study. In case, Reviewer would still recommend to modify the text in abstract and introduction, we would do it.

Comment 2. In discussing figure 1, the authors switch from claiming to be studying NFATc binding to studying NFAT expression. This use of 2 different naming conventions is certain to confuse readers; the authors should use the approved current naming system in referring to NFAT isoforms. In which case NFAT2 is NFATc1.

Response: We would like to thank the Reviewer for highlighting this point. We have effectively addressed this comment by changing the nomenclature of NFAT2 to NFATc1 throughout the manuscript text and figures.

Comment 3. The ChIP analyses in figures 1H and 7D are important findings, however, there is missing information. Typically, ChIP is used to validate putative binding sites; as such, one would expect 3 separate qPCR reactions for Orai3, not one. It is also important to note that qPCR products should be uniform in size and under 100 bp; here, the product size is not stated. Finally, demonstrating that an antibody targeting ANY other NFAT isoform fails to pull down whatever product this is would increase confidence considerably.

Also, the gold standard for validating ChIP is to mutate the sites and eliminate binding. The "silver" standard would be to mutate them in your luciferase vector and demonstrate that NFATc1 no longer stimulates luciferase expression. Since neither of these was done, the ChIP data provided should not be considered formally validated.

Response: We thank the Reviewer for raising this highly relevant concern. In this revised manuscript, we have addressed this comment by performing several additional experiments. The new data provided in the revised manuscript corroborates our earlier results. Indeed, this data has notably strengthen our work.

In the revised manuscript, we performed ChIP assay where we increased the number of sonication cycles to 35 so as to make sheared chromatin of around 100 bp. Next, we designed primers to amplify individual NFATc1 binding sites on Orai3 promoter, but due to close proximity of the NFATc1 binding sites, we could design two primer sets. The primer first set to amplify the -1017 bp binding site and the second set to amplify the -990 and -920 bp. Further, as suggested by the Reviewer, we performed immunoprecipitation with the four isoforms of NFAT. Our results show that only NFATc1 pulldown shows significant enrichment of Orai3 promoter with both the primer sets as compared to the IP mock samples and other NFAT isoforms (Figure 1J). Hence, our data reveals that only NFATc1 binds to these predicted sites on the Orai3 promoter and it doesn’t show a preference among these binding sites.

Further, as suggested by the Reviewer, we mutated the Orai3 promoter in luciferase vector with deletions of the individual NFATc1 binding sites and also cloned a truncated Orai3 promoter with no NFATc1 binding sites into the luciferase vector. The luciferase assays with these mutant and truncated promoters show that upon co-expression of NFATc1, the luciferase activity of the mutant Orai3 promoter with deletion of individual NFATc1 binding site is significantly reduced in comparison to wild type Orai3 promoter. Furthermore, the maximum decrease in luciferase activity was seen with the truncated Orai3 promoter with no NFATc1 binding sites (Figure 1I). These results show that NFATc1 binds to the predicted binding sites on Orai3 promoter. Taken together, the additional ChIP assays with the four isoforms of NFAT and luciferase assays with mutated & truncated Orai3 promoters validates the transcriptional regulation of Orai3 by NFATc1.

Comment 4. In figures 2 and 3, only one cell line is used to represent each of 3 conditions of pancreatic cancer. That is insufficient to make generalized conclusions; some aspects of this figure (expression and stability, not function) should be extended to 2 to 3 cell lines/condition. TCGA data validating this point would also be helpful.

Response: We really appreciate the feedback given by Reviewer 1. To strengthen our manuscript, we have addressed this comment by performing experiments in 2 cell lines/condition of pancreatic cancer. This new data in the revised manuscript provides substantial evidence for the dichotomous regulation of Orai3 by NFATc1.

In the revised manuscript, we carried out NFATc1 overexpression and NFAT inhibition via VIVIT studies in three additional cell lines: BXPC-3 (non-metastatic), ASPC-1 (invasive) and SW1990 (metastatic). The results in these cell-lines support our earlier findings as both overexpression of NFATc1 and VIVIT mediated NFAT inhibition leads to transcriptional upregulation of Orai3 in BXPC-3 (non-metastatic) (Figure S3A, D), ASPC-1 (invasive) (Figure S3G, J) and SW1990 (metastatic) (Figure S3M, P). These results are similar to our earlier data from MiaPaCa-2 (non-metastatic), PANC-1 (invasive) and CFPAC-1 (metastatic) cells. Further, NFATc1 overexpression leads to an increase in Orai3 protein levels in BXPC-3 (non-metastatic) (Figure S3B, C) and a decrease in Orai3 protein levels in ASPC-1 (invasive) (Figure S3H, I) and SW1990 (metastatic) (Figure S3N, O). Moreover, VIVIT transfection leads to a decrease in Orai3 protein levels in BXPC-3 (non-metastatic) (Figure S3E, F) and an increase in Orai3 protein levels in ASPC-1 (invasive) (Figure S3K, L) and SW1990 (metastatic) (Figure S3Q, R). The findings in these cell lines recapitulates the data obtained earlier from MiaPaCa-2 (non-metastatic), PANC-1 (invasive) and CFPAC-1 (metastatic) cell lines. Therefore, this new data supports our conclusion regarding the dichotomous regulation of Orai3 by NFATc1 across the three conditions of pancreatic cancer.

Comment 5. Upon finding that NFAT inhibition stimulates Orai3 transcription (same as O/E), the authors essentially conclude that this confirms regulation of Orai3 by NFAT and that there must be compensation. This is not supported by any data; the use of siRNA validates that Orai3 has some dependence on NFATc1 for transcription, but the nature of this relationship is not adequately explained.

Response: We thank the Reviewer for asking this question. In our manuscript, we performed NFATc1 inhibition studies using VIVIT and siRNA-mediated NFATc1 knockdown. Both of these assays show increase in Orai3 mRNA levels in all non-metastatic, invasive and metastatic pancreatic cancer cell lines. To understand if the increase in Orai3 mRNA levels is via transcriptional regulation, we performed luciferase assay which showed that VIVIT mediated NFAT inhibition leads to increase in luciferase activity suggesting the binding of other transcription factors on the Orai3 promoter. To corroborate this hypothesis, in our revised manuscript, we performed luciferase assay in wild type Orai3 promoter and truncated Orai3 promoter with no NFATc1 binding sites. NFAT inhibition via VIVIT transfection led to an increase in luciferase activity in both wild type and truncated Orai3 promoter (Figure S2A). Hence, removal of NFATc1 binding sites had no significant effect on luciferase activity suggesting that apart from NFATc1, other endogenous transcription factors are involved in regulating Orai3 transcription. We have not identified all the transcription factors that can modulate Orai3 upon NFAT inhibition as it is beyond the scope of this study. We sincerely hope the Reviewer 1 would be satisfied with this additional data.

Reviewer #2

Comment 1. Figure 1 all overexpression no evidence of endogenous NFAT2 regulating Orai3. I realize there may be limitations on available NFAT isoform specific antibodies so it is not essential to directly show this but a comment to that effect in the paper would be useful.

Response: We apologize to the Reviewer for not highlighting the NFAT2 (NFATc1) loss of function data effectively. Actually, in the __Figure 3 __and __Supplementary Figure 2 __of the original manuscript, we showed VIVIT mediated NFAT inhibition and siRNA induced NFATc1 silencing data to provide the evidence that endogenous NFATc1 regulates Orai3.

Comment 2. Figure 1F. Show RNA levels of Orai3 following overexpression of the other NFAT isoforms.

Response: As suggested by the Reviewer, in the revised manuscript, we overexpressed the four NFAT isoforms: NFATc2, NFATc1, NFATc4 & NFATc3 and checked Orai3 mRNA levels. qRT-PCR analysis shows that overexpression of NFATc1 results in the highest and significant increase in Orai3 mRNA levels compared to the empty vector and other NFAT isoforms (Figure 1F). This data corroborates the western blot data of NFAT isoforms overexpression highlighting the transcriptional regulation of Orai3 by NFATc1.

Comment 3. Fig. S3D, E. For both MARCH3 and 8 higher expression levels correlate with better survival whereas in the text it is stated that this is the case only for MARCH8. Please correct.

Response: The survival analysis of pancreatic cancer patients with low MARCH3 and MARCH8 levels shows that around 30% of patients with low MARCH3 levels survived for 5.5 years, whereas in case of MARCH8 30% of patients with high MARCH8 levels survived for >7.5 years. Hence high MARCH8 expression in pancreatic cancer patients provided significant survival advantage compared to high MARCH3 levels. Therefore, in the text, we meant that compared to MARCH3, higher MARCH8 levels correlate with better survival. As suggested by the Reviewer, we have modified the text to make this point clearer.

Comment 4. For the 2APB stimulation experiments there is a large variation in the level of the response between experiments even for the same cell type. For example, compare the level of the 2APB-stimulated Orai3 influx between Fig. 4H and 5C on the MiaPaCa-2 cells. Also there doesn't seem to be a correlation between the levels of Orai3 protein from WB and the 2APB stimulated entry among the different cell lines. This needs to be addressed and differences explained.

Response: We understand the concern raised by Reviewer 2 regarding calcium imaging experiments in MiaPaCa-2 cell line. Therefore, in the revised manuscript, we repeated calcium imaging experiments in MiaPaCa-2 and updated the representative traces as well as quantitative analysis (Figure 2D, E, 3D, E, 4H, I, S2L, M). Further, we have discussed this point in the text of the manuscript.

Comment 6. Fig. 6C and 6D. Show the line in 6C from which the intensity profile in 6D was generated. Also give the details of the imaging setup in methods: size of the pinhole, imaging mode, etc. The colocalization is not very convincing.

Response: As recommended by the Reviewer, in the revised manuscript, we have indicated the region used for intensity profile generation by drawing a line in the representative image (Figure 6D). Further, we have updated the methodology of colocalization microscopy with details of the size of the pinhole and imaging mode.

Comment 8. May be worth showing that overexpression of MARCH8 in the metastatic cell lines decreases their migration and metastasis as the argument is that these cells need high Orai3 but not too high. So, it would be predicted that overexpression of MARCH8 should lower Orai3 levels enough to prevent their metastasis.

Response: We would like to thank the Reviewer for this highly relevant suggestion. In our revised manuscript, we carried out transwell migration assays with MARCH8 overexpression as well as MARCH8 knockdown in CFPAC-1 (metastatic) cells. Our data shows that stable lentiviral knockdown of MARCH8 increased the number of migrated CFPAC-1 cells compared to shNT CFPAC-1 cells while MARCH8 overexpression decreased the number of migrated CFPAC-1 cells compared to empty vector control cells (Figure 9F, G). Therefore, as pointed out by the Reviewer, MARCH8 overexpression lowers Orai3 levels in metastatic pancreatic cancer cells and hinders their metastatic potential.

Comment 9. Fig. 10. Show higher levels of Orai3 protein in the metastatic side.

Response: As suggested, we have updated the summary figure (Figure 10) showing higher Orai3 protein levels in the metastatic side.

Comment 10. Please show all full WBs in the supplementary data.

Response: As recommended by the Reviewer, we have provided all full western blots in a supplementary file (Supplementary File 1).

Reviewer #3

Comment 1. The authors show that MARCH8 physically associates with Orai3 using Co-IP and Co-localization studies. For the co-localization studies the authors should still provide a quantitative analysis. Furthermore, can the authors detect FRET between March and Orai3? Can you please state the labels used in the co-localization experiments also in the figure legend.

Response: As suggested by Reviewer 3, in the revised manuscript, we have provided quantitative analysis of Orai3 and MARCH8 co-localization. Further, we have stated the labels used in the co-localization experiment in the figure legend of the revised manuscript. Unfortunately, we could not perform FRET assay between Orai3 and MARCH8 due to limited resources. Instead, as discussed in the planned revisions section, we are planning to perform co-immunoprecipitation assay with mutated Orai3 protein in which the MARCH8 interacting domains are deleted to investigate direct interaction of Orai3 and MARCH8. We believe that Reviewer 3 will be satisfied with this experiment.

Comment 2. In the abstract it is only getting clear at the end that pancreatic cancer cells are used. It would be great if the authors could introduce this fact already more at the beginning of the abstract.

Response: As recommended by the Reviewer, in the revised manuscript, we have introduced the use of pancreatic cancer cells at the beginning of the abstract.

Comment 4. In other cancer types recent reports suggest a co-expression of Orai1 and Orai3 and even the formation of heteromers. Does only Orai3 or also Orai1 play a role in pancreatic cancer cells? Could there we difference in degradation when Orai3 forms homomers or heteromers with Orai1.

Response: We thank the reviewer for asking this interesting question. There is only one report on Orai1’s role in pancreatic cancer. It was suggested that Orai1 can contribute to apoptotic resistance of pancreatic cancer cells (Kondratska et al. BBA-Molecular Cell Research, 2014). However, only one cell line i.e. PANC-1 was used in this study. While our earlier work and other studies have demonstrated that Orai3 drives pancreatic cancer metastasis (Arora et al. Cancers, 2021) and proliferation (Dubois et al. BBA-Molecular Cell Research, 2021) respectively. Therefore, emerging literature suggests that both Orai1 and Orai3 can contribute to different aspects of pancreatic cancer progression. But whether Orai1 and Orai3 form heteromers in pancreatic cancer cells remains unexplored. Further, we believe that the degradation machinery and the underlying molecular mechanisms would be analogous for both Orai3 homomers and heteromers. Nonetheless, the rate of degradation may differ for Orai3 homomers and heteromers as literature suggests that usually proteins are more stable in large heteromeric protein complexes.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

This manuscript describes a series of experiments documenting trophic egg production in a species of harvester ant, Pogonomyrmex rugosus. In brief, queens are the primary trophic egg producers, there is seasonality and periodicity to trophic egg production, trophic eggs differ in many basic dimensions and contents relative to reproductive eggs, and diets supplemented with trophic eggs had an effect on the queen/worker ratio produced (increasing worker production).

The manuscript is very well prepared and the methods are sufficient. The outcomes are interesting and help fill gaps in knowledge, both on ants as well as insects, more generally. More context could enrich the study and flow could be improved.

We thank the reviewer for these comments. We agree that the paper would benefit from more context. We have therefore greatly extended the introduction.

Reviewer #2 (Public Review):

The manuscript by Genzoni et al. provides evidence that trophic eggs laid by the queen in the ant Pogonomyrmex rugosis have an inhibitory effect on queen development. The authors also compare a number of features of trophic eggs, including protein, DNA, RNA, and miRNA content, to reproductive eggs. To support their argument that trophic eggs have an inhibitory effect on queen development, the authors show that trophic eggs have a lower content of protein, triglycerides, glycogen, and glucose than reproductive eggs, and that their miRNA distributions are different relative to reproductive eggs. Although the finding of an inhibitory influence of trophic eggs on queen development is indeed arresting, the egg cross-fostering experiment that supports this finding can be effectively boiled down to a single figure (Figure 6). The rest of the data are supplementary and correlative in nature (and can be combined), especially the miRNA differences shown between trophic and reproductive eggs. This means that the authors have not yet identified the mechanism through which the inhibitory effect on queen development is occurring. To this reviewer, this finding is more appropriate as a short report and not a research article. A full research article would be warranted if the authors had identified the mechanism underlying the inhibitory effect on queen development. Furthermore, the article is written poorly and lacks much background information necessary for the general reader to properly evaluate the robustness of the conclusions and to appreciate the significance of the findings.

We thank the reviewer for these comments. We agree that the paper would benefit by having more background information and more discussion. We have followed this advice in the revision.

Reviewer #3 (Public Review):

In "Trophic eggs affect caste determination in the ant Pogonomyrmex rugosus" Genzoni et al. probe a fundamental question in sociobiology, what are the molecular and developmental processes governing caste determination? In many social insect lineages, caste determination is a major ontogenetic milestone that establishes the discrete queen and worker life histories that make up the fundamental units of their colonies. Over the last century, mechanisms of caste determination, particularly regulators of caste during development, have remained relatively elusive. Here, Genzoni et al. discovered an unexpected role for trophic eggs in suppressing queen development - where bi-potential larvae fed trophic eggs become significantly more likely to develop into workers instead of gynes (new queens). These results are unexpected, and potentially paradigm-shifting, given that previously trophic eggs have been hypothesized to evolve to act as an additional intracolony resource for colonies in potentially competitive environments or during specific times in colony ontogeny (colony foundation), where additional food sources independent of foraging would be beneficial. While the evidence and methods used are compelling (e.g., the sequence of reproductive vs. trophic egg deposition by single queens, which highlights that the production of trophic eggs is tightly regulated), the connective tissue linking many experiments is missing and the downstream mechanism is speculative (e.g., whether miRNA, proteins, triglycerides, glycogen levels in trophic eggs is what suppresses queen development). Overall, this research elevates the importance of trophic eggs in regulating queen and worker development but how this is achieved remains unknown.

We thank the reviewer for these comments and agree that future work should focus on identifying the substances in trophic eggs that are responsible for caste determination.  

Reviewer #1 (Recommendations For The Authors):

Introduction:

The context for this study is insufficiently developed in the introduction - it would be nice to have a more detailed survey of what is known about trophic eggs in insects, especially social insects. The end of the introduction nicely sets up the hypothesis through the prior work described by Helms Cahan et al. (2011) where they found JH supplementation increased trophic egg production and also increased worker size. I think that the introduction could give more context about egg production in Pogonomyrmex and other ants, including what is known about worker reproduction. For example, Suni et al. 2007 and Smith et al. 2007 both describe the absence of male production by workers in two different harvester ants. Workers tend to have underdeveloped ovaries when in the presence of the queen. Other species of ants are known to have worker reproduction seemingly for the purpose of nutrition (see Heinze and Hölldober 1995 and subsequent studies on Crematogaster smithi). Because some ants, including Pogonomyrmex, lack trophallaxis, it has been hypothesized that they distribute nutrients throughout the nest via trophic eggs as is seen in at least one other ant (Gobin and Ito 2000). Interestingly, Smith and Suarez (2009) speculated that the difference in nutrition of developing sexual versus worker larvae (as seen in their pupal stable isotope values) was due to trophic egg provisioning - they predicted the opposite as was found in this study, but their prediction was in line with that of Helms Cahan et al. (2011). This is all to say that there is a lot of context that could go into developing the ideas tested in this paper that is completely overlooked. The inclusion of more of what is known already would greatly enrich the introduction.

We agree that it would be useful to provide a larger context to the study. We now provide more information on the life-history of ants and explained under what situations queens and workers may produce trophic eggs. We also mentioned that some ants such as Crematogaster smithi have a special caste of “large workers” which are morphologically intermediate between winged queens and small workers and appear to be specialized in the production of unfertilized eggs. We now also mention the study of Goby and Ito (200) where the authors show that trophic eggs may play an important role in food distribution withing the colony, in particular in species where trophallaxis is rare or absent.

Methods:

L49: What lineage is represented in the colonies used? The collection location is near where both dependent-lineage (genetic caste determining) P. rugosus and "H" lineage exist. This is important to know. Further, depending on what these are, the authors should note whether this has relevance to the study. Not mentioning genetic caste determination in a paper that examines caste determination is problematic.

This is a good point. We have now provided information at the very beginning of the material and method section that the queens had been collected in populations known not to have dependentlineage (genetic caste determining) mechanisms of caste determination.

L63 and throughout: It would be more efficient to have a paragraph that cites R (must be done) and RStudio once as the tool for all analyses. It also seems that most model construction and testing was done using lme4 - so just lay this out once instead of over and over.

We agree and have updated the manuscript accordingly.

L95: 'lenght' needs to be 'length' in the formula.

Thanks, corrected.

L151: A PCA was used but not described in the methods. This should be covered here. And while a Mantel test is used, I might consider a permANOVA as this more intuitively (for me, at least) goes along with the PCA.

We added the PCA description in the Material and Method section.

Results:

I love Fig. 3! Super cool.

Thanks for this positive comment.

Discussion:

It would be good to have more on egg cannibalism. This is reasonably well-studied and could be good extra context.

We have added a paragraph in the discussion to mention that egg cannibalism is ubiquitous in ants.

Supp Table 1: P. badius is missing and citations are incorrectly attributed to P. barbatus.

P. badius was present in the Table but not with the other Pogonomyrmex species. For some genera the species were also not listed in alphabetic order. This has been corrected.

Reviewer #2 (Recommendations For The Authors):

COMMENTS ON INTRODUCTION:

The introduction is missing information about caste determination in ants generally and Pogonomyrmex rugosis specifically. This is important because some colonies of Pogonomyrmex rugosis have been shown to undergo genetic caste determination, in which case the main result would be rendered insignificant. What is the evidence that caste determination in the lineages/colonies used is largely environmentally influenced and in what contexts/environmental factors? All of this should be made clear.

This is a good point. We have expanded the introduction to discuss previous work on caste determination in Pogonomyrmex species with environmental caste determination and now also provide evidence at the beginning of the Material and Method section that the two populations studied do not have a system of genetic caste determination.

Line 32 and throughout the paper: What is meant exactly by 'reproductive eggs'? Are these eggs that develop specifically into reproductives (i.e., queens/males) or all eggs that are non-trophic? If the latter, then it is best to refer to these eggs as 'viable' in order to prevent confusion.

We agree and have updated the manuscript accordingly.

Figure 1/Supp Table 1: It is surprising how few species are known to lay trophic eggs. Do the authors think this is an informative representation of the distribution of trophic egg production across subfamilies, or due to lack of study? Furthermore, the branches show ant subfamilies, not families. What does the question mark indicate? Also, the information in the table next to the phylogeny is not easy to understand. Having in the branches that information, in categories, shown in color for example, could be better and more informative. Finally, having the 'none' column with only one entry is confusing - discuss that only one species has been shown to definitely not lay trophic eggs in the text, but it does not add much to the figure.

Trophic eggs are probably very common in ants, but this has not been very well studied. We added a sentence in the manuscript to make this clear.

Thanks for noticing the error family/subfamily error. This has been corrected in Figure 1 and Supplementary Table 1.

The question mark indicates uncertainty about whether queens also contribute to the production of trophic eggs in one species (Lasius niger). We have now added information on that in the Figure legend.

We agree with the reviewer that it would be easier to have the information on whether queens and workers produce trophic on the branches of the Tree. However, having the information on the branches would suggest that the “trait” evolved on this part of the tree. As we do not know when worker or queen production of trophic eggs exactly evolved, we prefer to keep the figure as it is.

Finally, we have also removed the none in the figure as suggested by the reviewer and discussed in the manuscript the fact that the absence of trophic eggs has been reported in only one ant species (Amblyopone silvestrii: Masuko 2003).

COMMENTS ON MATERIALS AND METHODS:

Why did they settle on three trophic eggs per larva for their experimental setup?

We used three trophic eggs because under natural conditions 50-65% of the eggs are trophic. The ratio of trophic eggs to viable eggs (larvae) was thus similar natural condition.

Line 50: In what kind of setup were the ants kept? Plaster nests? Plastic boxes? Tubes? Was the setup dry or moist? I think this information is important to know in the context of trophic eggs.

We now explain that colonies were maintained in plastic boxes with water tubes.

Line 60: Were all the 43 queens isolated only once, or multiple times?

Each of the 43 queens were isolated for 8 hours every day for 2 weeks, once before and once after hibernation (so they were isolated multiple times). We have changed the text to make clear that this was done for each of the 43 queens.

Could isolating the queen away from workers/brood have had an effect on the type of eggs laid?

This cannot be completely ruled out. However, it is possible to reliably determine the proportion of viable and trophic eggs only by isolating queens. And importantly the main aim of these experiments was not to precisely determine the proportion viable and trophic eggs, but to show that this proportion changes before and after hibernation and that queens do not lay viable and trophic eggs in a random sequence.

Since it was established that only queens lay trophic eggs why was the isolation necessary?

Yes this was necessary because eggs are fragile and very difficult to collect in colonies with workers (as soon as eggs are laid they are piled up and as soon as we disturb the nest, a worker takes them all and runs away with them). Moreover, it is possible that workers preferentially eat one type of eggs thus requiring to remove eggs as soon as queens would have laid them. This would have been a huge disturbance for the colonies.

Line 61: Is this hibernation natural or lab induced? What is the purpose of it? How long was the hibernation and at what temperature? Where are the references for the requirement of a diapause and its length?

The hibernation was lab induced. We hibernated the queens because we previously showed that hibernation is important to trigger the production of gynes in P. rugosus colonies in the laboratory (Schwander et al 2008; Libbrecht et al 2013). Hibernation conditions were as described in Libbrecht et al (2013).  

Line 73: If the queen is disturbed several times for three weeks, which effect does it have on its egg-laying rate and on the eggs laid? Were the eggs equally distributed in time in the recipient colonies with and without trophic eggs to avoid possible effects?

It is difficult to respond what was the effect of disturbance on the number and type of eggs laid. But again our aim was not to precisely determine these values but determine whether there was an effect of hibernation on the proportion of trophic eggs. The recipient colonies with and without trophic eggs were formed in exactly the same way. No viable eggs were introduced in these colonies, but all first instar larvae have been introduced in the same way, at the same time, and with random assignment. We have clarified this in the Material and Method section.

Line 77: Before placing the freshly hatched larvae in recipient colonies, how long were the recipient colonies kept without eggs and how long were they fed before giving the eggs? Were they kept long enough without the queen to avoid possible effects of trophic eggs, or too long so that their behavior changed?

The recipient colonies were created 7 to 10 days before receiving the first larvae and were fed ad libitum with grass seeds, flies and honey water from the beginning. Trophic eggs that would have been left over from the source colony should have been eaten within the first few days after creating the recipient colonies. However, even if some trophic eggs would have remained, this would not influence our conclusion that trophic eggs influence caste fate, given the fully randomized nature of our treatments and the considerable number of independent replicates. The same applies to potential changes in worker behavior following their isolation from the queen.

Line 77: Is it known at what stage caste determination occurs in this species? Here first instar larvae were given trophic eggs or not. Does caste-determination occur at the first instar stage? If not, what effect could providing trophic eggs at other stages have on caste-determination?

A previous study showed that there is a maternal effect on caste determination in the focal species (Schwander et al 2008). The mechanism underlying this maternal effect was hypothesized to be differential maternal provisioning of viable eggs. However, as we detail in the discussion, the new data presented in our study suggests that the mechanism is in fact a different abundance of trophic eggs laid by queens. There is currently no information when exactly caste determination occurs during development

COMMENTS ON RESULTS:

Line 65: How does investigating the order of eggs laid help to "inform on the mechanisms of oogenesis"?

We agree that the aim was not to study the mechanism of oogenesis. We have changed this sentence accordingly: “To assess whether viable and trophic eggs were laid in a random order, or whether eggs of a given type were laid in clusters, we isolated 11 queens for 10 hours, eight times over three weeks, and collected every hour the eggs laid”

Figure 2: There is no description/discussion of data shown in panels B, C, E, and F in the main text.

We have added information in the main text that while viable eggs showed embryonic development at 25 and 65 hours (Fig 12 B, C) there was no such development for trophic eggs (Fig. 2 E,F).

Line 172: Please explain hibernation details and its significance on colony development/life cycle.

We have added this information in the Material and Method section.

Figure 6: How is B plotted? How could 0% of gynes have 100% survival?

The survival is given for the larvae without considering caste. We have changed the de X axis of panel B and reworded the Figure legend to clarify this.

Is reduced DNA content just an outcome of reduced cell number within trophic eggs, i.e., was this a difference in cell type or cell number? Or is it some other adaptive reason?

It is likely to be due to a reduction in cell number (trophic eggs have maternal DNA in the chorion, while viable eggs have in addition the cells from the developing zygote) but we do not have data to make this point.

Is there a logical sequence to the sequence of egg production? The authors showed that the sequence is non-random, but can they identify in what way? What would the biological significance be?

We could not identify a logical sequence. Plausibly, the production of the two types of eggs implies some changes in the metabolic processes during egg production resulting in queens producing batches of either viable or trophic eggs. This would be an interesting question to study, but this is beyond the scope of this paper.

Figure 6b is difficult to follow, and more generally, legends for all figures can be made clearer and more easy to follow.

We agree. We have now improved the legends of Fig 6B and the other figures.

Lines 172-174: "The percentage of eggs that were trophic was higher before hibernation...than after. This higher percentage was due to a reduced number of reproductive eggs, the number of trophic eggs laid remained stable" - are these data shown? It would be nice to see how the total egglaying rate changes after hibernation. Also, is the proportion of trophic eggs laid similar between individual queens?

No the data were not shown and we do not have excellent data to make this point. We have therefore removed the sentence “This higher percentage was due to a reduced number of reproductive eggs, the number of trophic eggs laid remained stable” from the manuscript.

Figure 6B: Do several colonies produce 100% gynes despite receiving trophic eggs? It would be interesting if the authors discussed why this might occur (e.g., the larvae are already fully determined to be queens and not responsive to whatever signal is in the trophic eggs).

The reviewer is correct that 4 colonies produced 100% gynes despite receiving trophic eggs. However, the number of individuals produced in these four colonies was small (2,1,2,1, see supplementary Table 2). So, it is likely that it is just by chance that these colonies produced only gynes.

Figure 5: Why a separation by "size distribution variation of miRNA"? What is the relevance of looking at size distributions as opposed to levels?

We did that because there many different miRNA species, reflected by the fact that there is not just one size peak but multiple one. This is why we looked at size distribution

Figure 2: The image of the viable embryo is not clear. If possible, redo the viable to show better quality images.

Unfortunately, we do not anymore have colonies in the laboratory so this is not possible.

COMMENTS ON DISCUSSION:

Lines 236-247: Can an explanation be provided as to why the effect of trophic eggs in P. rugosus is the opposite of those observed by studies referenced in this section? Could P. rugosus have any life history traits that might explain this observation?

In the two mentioned studies there were other factors that co-varied with variation in the quantity of trophic eggs. We mentioned that and suggested that it would be useful to conduct experimental manipulation of the quantity of trophic eggs in the Argentine ant and P. barbatus (the two species where an effect of trophic eggs had been suggested).

The discussion should include implications and future research of the discovery.

We made some suggestions of experiments that should be performed in the future

The conclusion paragraph is too short and does not represent what was discussed.

We added two sentences at the end of the paragraph to make suggestions of future studies that could be performed.

Lines 231 to 247: Drastically reduce and move this whole part to the introduction to substantiate the assumption that trophic eggs play a nutritional role.

We moved most of this paragraph to the introduction, as suggested by the reviewer.

Reviewer #3 (Recommendations For The Authors):

I would like to commend the authors on their study. The main findings of the paper are individually solid and provide novel insight into caste determination and the nature of trophic eggs. However, the inferences made from much of the data and connections between independent lines of evidence often extend too far and are unsubstantiated.

We thank the reviewer for the positive comment. We made many changes in the manuscript to improve the discussion of our results.

This point is eye-opening because I hadn’t thought about design as something that could exclude people. It makes me realize that designers have a lot of responsibility to think about who might be left out. I want to learn more about how to avoid these mistakes and make my designs more fair and accessible for everyone.

Author response:

The following is the authors’ response to the previous reviews

eLife Assessment

This work presents a valuable self-supervised method for the segmentation of 3D cells in microscopy images, alongside an implementation as a Napari plugin and an annotated dataset. While the Napari plugin is readily applicable and promises to eliminate time consuming data labeling to speed up quantitative analysis, there is incomplete evidence to support the claim that the segmentation method generalizes to other light-sheet microscopy image datasets beyond the two specific ones used here.

Technical Note: We showed the utility of CellSeg3D in the first submission and in our revision on 5 distinct datasets; 4 of which we showed F1-Score performance on. We do not know which “two datasets” are referenced. We also already showed this is not limited to LSM, but was used on confocal images; we already limited our scope and changed the title in the last rebuttal, but just so it’s clear, we also benchmark on two non-LSM datasets.

In this revision, we have now additionally extended our benchmarking of Cellpose and StarDrist on all 4 benchmark datasets, where our Wet3D (our novel contribution of a self-supervised model) outperforms or matches these supervised baselines. Moreover, we perform rigorous testing of our model’s generalization by training on one dataset and testing generalization to the other 3; we believe this is on par (or beyond) what most cell segmentation papers do, thus we hope that “incomplete” can now be updated.

Public Reviews:

Reviewer #1 (Public review):

This work presents a self-supervised method for the segmentation of 3D cells in microscopy images, an annotated dataset, as well as a napari plugin. While the napari plugin is potentially useful, there is insufficient evidence in the manuscript to support the claim that the proposed method is able to segment cells in other light-sheet microscopy image datasets than the two specific ones used here.

Thank you again for your time. We benchmarked already on four datasets the performance of WNet3Dd (our 3D SSL contribution) - thus, we do not know which two you refer to. Moreover, we now additionally benchmarked Cellpose and StarDist on all four so readers can see that on all datasets, WNet3D outperforms or matches these supervised methods.

I acknowledge that the revision is now more upfront about the scope of this work. However, my main point still stands: even with the slight modifications to the title, this paper suggests to present a general method for self-supervised 3D cell segmentation in light-sheet microscopy data. This claim is simply not backed up.

We respectfully disagree; we benchmark on four 3D datasets: three curated by others and used in learning ML conference proceedings, and one that we provide that is a new ground truth 3D dataset - the first of its kind - on mesoSPIM-acquired brain data. We believe benchmarking on four datasets is on par (or beyond) with current best practices in the field. For example, Cellpose curated one dataset and tested on held-out test data on this one dataset (https://www.nature.com/articles/s41592-020-01018-x) and benchmarked against StarDist and Mask R-CNN (two models). StarDist (Star-convex Polyhedra for 3D Object Detection and Segmentation in Microscopy) benchmarked on two datasets and against two models, IFT-Watershed and 3D U-Net. Thus, we feel our benchmarking on more models and more datasets is sufficient to claim our model and associated code is of interest to readers and supports our claims (for comparison, Cellpose’s title is “Cellpose: a generalist algorithm for cellular segmentation”, which is much broader than our claim).

I still think the authors should spell out the assumptions that underlie their method early on (cells need to be well separated and clearly distinguishable from background). A subordinate clause like "often in cleared neural tissue" does not serve this purpose. First, it implies that the method is also suitable for non-cleared tissue (which would have to be shown). Second, this statement does not convey the crucial assumptions of well separated cells and clear foreground/background differences that the method is presumably relying on.

We expanded the manuscript now quite significantly. To be clear, we did show our method works on non-cleared tissue; the Mouse Skull, 3D platynereis-Nuclei, and 3D platynereis-ISH-Nuclei is not cleared tissue, and not all with LSM, but rather with confocal microscopy. We attempted to make that more clear in the main text.

Additionally, we do not believe it needs to be well separated and have a perfectly clean background. While we removed statements like "often in cleared neural tissue", expanded the benchmarking, and added a new demo figure for the readers to judge. As in the last rebuttal, we provide video-evidence (https://www.youtube.com/watch?v=U2a9IbiO7nE) of the WNet3D working on the densely packed and hard to segment by a human, Mouse Skull dataset and linked this directly in the figure caption.

We have re-written the main manuscript in an attempt to clarify the limitations, including a dedicated “limitations” section. Thank you for the suggestion.

It does appear that the proposed method works very well on the two investigated datasets, compared to other pre-trained or fine-tuned models. However, it still remains unclear whether this is because of the proposed method or the properties of those specific datasets (namely: well isolated cells that are easily distinguished from the background). I disagree with the authors that a comparison to non-learning methods "is unnecessary and beyond the scope of this work". In my opinion, this is exactly what is needed to proof that CellSeg3D's performance can not be matched with simple image processing.

We want to again stress we benchmarked WNet3D on four datasets, not two. But now additionally added benchmarking with Cellpose, StarDist and a non-deep learning method as requested (see new Figures 1 and 3).

As I mentioned in the original review, it appears that thresholding followed by connected component analysis already produces competitive segmentations. I am confused about the authors' reply stating that "[this] is not the case, as all the other leading methods we fairly benchmark cannot solve the task without deep learning". The methods against which CellSeg3D is compared are CellPose and StarDist, both are deep-learning based methods.

That those methods do not perform well on this dataset does not imply that a simpler method (like thresholding) would not lead to competitive results. Again, I strongly suggest the authors include a simple, non-learning based baseline method in their analysis, e.g.: * comparison to thresholding (with the same post-processing as the proposed method) * comparison to a normalized cut segmentation (with the same post-processing as the proposed method)

We added a non-deep learning based approach, namely, comparing directly to thresholding with the same post hoc approach we use to go from semantic to instance segmentation. WNet3D (and other deep learning approaches) perform favorably (see Figure 2 and 3).

Regarding my feedback about the napari plugin, I apologize if I was not clear. The plugin "works" as far as I tested it (i.e., it can be installed and used without errors). However, I was not able to recreate a segmentation on the provided dataset using the plugin alone (see my comments in the original review). I used the current master as available at the time of the original review and default settings in the plugin.

We updated the plugin and code for the revision at your request to make this possible directly in the napari GUI in addition to our scripts and Jupyter Notebooks (please see main and/or `pip install --upgrade napari-cellseg3d`’ the current is version 0.2.1). Of course this means the original submission code (May 2024) will not have this in the GUI so it would require you to update to test this. Alternatively, you can see the demo video we now provide for ease: https://www.youtube.com/watch?v=U2a9IbiO7nE (we understand testing code takes a lot of time and commitment).

We greatly thank the review for their time, and we hope our clarifications, new benchmarking, and re-write of the paper now makes them able to change their assessment from incomplete to a more favorable and reflective eLife adjective.

Reviewer #2 (Public review):

Summary:

The authors propose a new method for self-supervised learning of 3d semantic segmentation for fluorescence microscopy. It is based on a WNet architecture (Encoder / Decoder using a UNet for each of these components) that reconstructs the image data after binarization in the bottleneck with a soft n-cuts clustering. They annotate a new dataset for nucleus segmentation in mesoSPIM imaging and train their model on this dataset. They create a napari plugin that provides access to this model and provides additional functionality for training of own models (both supervised and self-supervised), data labeling and instance segmentation via post-processing of the semantic model predictions. This plugin also provides access to models trained on the contributed dataset in a supervised fashion.

Strengths:

-  The idea behind the self-supervised learning loss is interesting.

-  It provides a new annotated dataset for an important segmentation problem.

-  The paper addresses an important challenge. Data annotation is very time-consuming for 3d microscopy data, so a self-supervised method that yields similar results to supervised segmentation would provide massive benefits.

-  The comparison to other methods on the provided dataset is extensive and experiments are reproducible via public notebooks.

Weaknesses:

The experiments presented by the authors support the core claims made in the paper. However, they do not convincingly prove that the method is applicable to segmentation problems with more complex morphologies or more crowded cells/nuclei.

Major weaknesses:

(1) The method only provides functionality for semantic segmentation outputs and instance segmentation is obtained by morphological post-processing. This approach is well known to be of limited use for segmentation of crowded objects with complex morphology. This is the main reason for prediction of additional channels such as in StarDist or CellPose. The experiments do not convincingly show that this limitation can be overcome as model comparisons are only done on a single dataset with well separated nuclei with simple morphology. Note that the method and dataset are still a valuable contribution with this limitation, which is somewhat addressed in the conclusion. However, I find that the presentation is still too favorable in terms of the presentation of practical applications of the method, see next points for details.

Thank you for noting the methods strengths and core features. Regarding weaknesses, we have revised the manuscript again and added direct benchmarking now on four datasets and a fifth “worked example” (https://www.youtube.com/watch?v=3UOvvpKxEAo&t=4s) in a new Figure 4.

We also re-wrote the paper to more thoroughly present the work (previously we adhered to the “Brief Communication” eLife format), and added an explicit note in the results about model assumptions.

(2) The experimental set-up for the additional datasets seems to be unrealistic as hyperparameters for instance segmentation are derived from a grid search and it is unclear how a new user could find good parameters in the plugin without having access to already annotated ground-truth data or an extensive knowledge of the underlying implementations.

We agree that of course with any self-supervised method the user will need a sense of what a good outcome looks like; that is why we provide Google Colab Notebooks

(https://github.com/AdaptiveMotorControlLab/CellSeg3D/tree/main/notebooks) and the napari-plugin GUI for extensive visualization and even the ability to manually correct small subsets of the data and refine the WNet3D model.

We attempted to make this more clear with a new Figure 2 and additional functionality directly into the plugin (such as the grid search). But, we believe this “trade-off” for SSL approaches over very labor intensive 3D labeling is often worth it; annotators are also biased so extensive checking of any GT data is equally required.

We also added the “grid search” functionality in the GUI (please `pip install --upgrade napari-cellseg3d`; the latest v0.2.1) to supplement the previously shared Notebook (https://github.com/C-Achard/cellseg3d-figures/blob/main/thresholds_opti/find_best_threshold s.ipynb) and added a new YouTube video: https://www.youtube.com/watch?v=xYbYqL1KDYE.

(3) Obtaining segmentation results of similar quality as reported in the experiments within the napari plugin was not possible for me. I tried this on the "MouseSkull" dataset that was also used for the additional results in the paper.

Again we are sorry this did not work for you, but we added new functionality in the GUI and made a demo video (https://www.youtube.com/watch?v=U2a9IbiO7nE) where you either update your CellSeg3D code or watch the video to see how we obtained these results.

Here, I could not find settings in the "Utilities->Convert to instance labels" widget that yielded good segmentation quality and it is unclear to me how a new user could find good parameter settings. In more detail, I cannot use the "Voronoi-Otsu" method due to installation issues that are prohibitive for a non expert user and the "Watershed" segmentation method yields a strong oversegmentation.

Sorry to hear of the installation issue with Voronoi-Otsu; we updated the documentation and the GUI to hopefully make this easier to install. While we do not claim this code is for beginners, we do aim to be a welcoming community, thus we provide support on GitHub, extensive docs, videos, the GUI, and Google Colab Notebooks to help users get started.

Comments on revised version

Many of my comments were addressed well:

-  It is now clear that the results are reproducible as they are well documented in the provided notebooks, which are now much more prominently referenced in the text.

Thanks!

-  My concerns about an unfair evaluation compared to CellPose and StarDist were addressed. It is now clear that the experiments on the mesoSPIM dataset are extensive and give an adequate comparison of the methods.

Thank you; to note we additionally added benchmarking of Cellpose and StarDist on the three additional datasets (for R1), but hopefully this serves to also increase your confidence in our approach.

-  Several other minor points like reporting of the evaluation metric are addressed.

I have changed my assessment of the experimental evidence to incomplete/solid and updated the review accordingly. Note that some of my main concerns with the usability of the method for segmentation tasks with more complex morphology / more crowded cells and with the napari plugin still persist. The main points are (also mentioned in Weaknesses, but here with reference to the rebuttal letter):

- Method comparison on datasets with more complex morphology etc. are missing. I disagree that it is enough to do this on one dataset for a good method comparison.

We benchmarked WNet3D (our contribution) on four datasets, and to aid the readers we additionally now added Cellpose and StarDist benchmarking on all four. WNet3D performs favorably, even on the crowded and complex Mouse Skull data. See the new Figure 3 as well as the associated video: https://www.youtube.com/watch?v=U2a9IbiO7nE&t=1s.

-  The current presentation still implies that CellSeg3d **and the napari plugin** work well for a dataset with complex nucleus morphology like the Mouse Skull dataset. But I could not get this to work with the napari plugin, see next points.

- First, deriving hyperparameters via grid search may lead to over-optimistic evaluation results. How would a user find these parameters without having access to ground-truth? Did you do any experiments on the robustness of the parameters?

-  In my own experiments I could not do this with the plugin. I tried this again, but ran into the same problems as last time: pyClesperanto does not work for me. The solution you link requires updating openCL drivers and the accepted solution in the forum post is "switch to a different workstation".

We apologize for the confusion here; the accepted solution (not accepted by us) was user specific as they switched work stations and it worked, so that was their solution. Other comments actually solved the issue as well. For ease this package can be installed on Google Colab (here is the link from our repo for ease: https://colab.research.google.com/github/AdaptiveMotorControlLab/CellSeg3d/blob/main/not ebooks/Colab_inference_demo.ipynb) where pyClesperanto can be installed via: !pip install pyclesperanto-prototype without issue on Google Colab.

This a) goes beyond the time I can invest for a review and b) is unrealistic to expect computationally inexperienced users to manage. Then I tried with the "watershed" segmentation, but this yields a strong oversegmentation no matter what I try, which is consistent with the predictions that look like a slightly denoised version of the input images and not like a proper foreground-background segmentation. With respect to the video you provide: I would like to see how a user can do this in the plugin without having a prior knowledge on good parameters or just pasting code, which is again not what you would expect a computationally unexperienced user to do.

We agree with the reviewer that the user needs domain knowledge, but we never claim our method was for inexperienced users. Our main goal was to show a new computer vision method with self-supervised learning (WNet3D) that works on LSM and confocal data for cell nuclei. To this end, we made you a demo video to show how a user can visually perform a thresholding check https://www.youtube.com/watch?v=xYbYqL1KDYE&t=5s, and we added all of these new utilities to the GUI, thanks for the suggestion. Otherwise, the threshold can also be done in a Notebook (as previously noted).

I acknowledge that some of these points are addressed in the limitations, but the text still implies that it is possible to get good segmentation results for such segmentation problems: "we believe that our self-supervised semantic segmentation model could be applied to more challenging data as long as the above limitations are taken into account." From my point of view the evidence for this is still lacking and would need to be provided by addressing the points raised above for me to further raise the Incomplete/solid rating, especially showing how this can be done wit the napari plugin. As an alternative, I would also consider raising it if the claims are further reduced and acknowledge that the current version of the method is only a good method for well separated nuclei.

We hope our new benchmarking and clear demo on four datasets helps improve your confidence in our evidence in our approach. We also refined our over text and hope our contributions, the limitations and the advantages are now more clear.

I understand that this may be frustrating, but please put yourself in the role of a new reader of this work: the impression that is made is that this is a method that can solve 3D segmentation tasks in light-sheet microscopy with unsupervised learning. This would be a really big achievement! The wording in the limitation section sounds like strategic disclaimers that imply that it is still possible to do this, just that it wasn't tested enough.

But, to the best of my assessment, the current version of the method only enables the more narrow case of well separated nuclei with a simple morphology. This is still a quite meaningful achievement, but more limited than the initial impression. So either the experimental evidence needs to be improved, including a demonstration how to achieve this in practice, including without deriving parameters via grid-search and in the plugin, or the claim needs to be meaningfully toned down.

Thanks for raising this point; we do think that WNet3D and the associated CellSeg3D package - aimed to continue to integrate state of the art models, is a non-trivial step forward. Have we completely solved the problem, certainly not, but given the limited 3D cell segmentation tools that exist, we hope this, coupled with our novel 3D dataset, pushes the field forward. We don’t show it works on the narrow well-separated use case, but rather show this works even better than supervised models on the very challenging benchmark Mouse Skull. Given we now show evidence that we outperform or match supervised algorithms with an unsupervised approach, we respectfully do think this is a noteworthy achievement. Thank you for your time in assessing our work.

Reviewer #2 (Public review):

Summary:

The goal of the paper was to trace the transitions hippocampal microglia undergo along aging. ScRNA-seq analysis allowed the authors to predict a trajectory and hypothesize about possible molecular checkpoints, which keep the pace of microglial aging. E.g. TGF1b was predicted as a molecule slowing down the microglial aging path and indeed, loss of TGF1 in microglia led to premature microglia aging, which was associated with premature loss of cognitive ability. The authors also used the parabiosis model to show how peripheral, blood-derived signals from the old organism can "push" microglia forward on the aging path.

Strengths:

A major strength and uniqueness of this work is the in-depth single-cell dataset, which may be a useful resource for the community, as well as the data showing what happens to young microglia in heterochronic parabiosis setting and upon loss of TGFb in their environment.

Weaknesses:

All weaknesses were addressed during revision.

Overall:

In general, I think the authors did a good job following the initial observations and devised clever ways to test the emerging hypotheses. The resulting data are an important addition to what we know about microglial aging and can be fruitfully used by other researchers, e.g. those working on microglia in a disease context.

Comments on revisions:

All my comments were addressed.

Welcome back, and in this video, I want to talk about how RDS can be backed up and restored, as well as covering the different methods of backup that we have available. Now we do have a lot to cover, so let's jump in and get started. Within RDS, there are two types of backup-like functionality: automated backups and snapshots. Both of these are stored in S3, but they use AWS-managed buckets, so they won't be visible to you within your AWS console. You can see backups in the RDS console, but you can't move to S3 and see any form of RDS bucket, which exists for backups. Keep this in mind because I've seen questions on it in the exam.

Now, the benefits of using S3 is that any data contained in backups is now regionally resilient, because it's stored in S3, which replicates data across multiple AWS availability zones within that region. RDS backups, when they do occur, are taken in most cases from the standby instance if you have multi-AZ enabled. So, while they do cause an I/O pause, this occurs from the standby instance, and so there won't be any application performance issues. If you don't use multi-AZ, for example, with test and development instances, then the backups are taken from the only available instance, so you may have pauses in performance.

Now, I want to step through how backups work in a little bit more detail, and I'm going to start with snapshots. Snapshots aren't automatic; they're things that you run explicitly or via a script or custom application. You have to run them against an RDS database instance. They're stored in S3, which is managed by AWS, and they function like the EBS snapshots that you've covered elsewhere in the course. Snapshots and automated backups are taken of the instance, which means all the databases within it, rather than just a single database. The first snapshot is a full copy of the data stored within the instance, and from then on, snapshots only store data which has changed since the last snapshot.

When any snapshot occurs, there is a brief interruption to the flow of data between the compute resource and the storage. If you're using single AZ, this can impact your application. If you're using multi-AZ, this occurs on the standby, and so won't have any noticeable effect. Time-wise, the initial snapshot might take a while; after all, it's a full copy of the data. From then on, snapshots will be much quicker because only changed data is being stored. Now, the exception to this are instances where there's a lot of data change. In this type of scenario, snapshots after the initial one can also take significant amounts of time. Snapshots don't expire; you have to clear them up yourself. It means that snapshots live on past when you delete the RDS instance. Again, they're only deleted when you delete them manually or via some external process. Remember that one because it matters for the exam.

Now you can run one snapshot per month, one per week, one per day, or one per hour. The choice is yours because they're manual. And one way that lower recovery point objectives can be met is by taking more frequent snapshots. The lower the time frame between snapshots, the lower the maximum data loss that can occur when you have a failure. Now, this is assuming we only have snapshots available, but there is another part to RDS backups, and that's automated backups. These occur once per day, but the architecture is the same. The first one is a full, and any ones which follow only store changed data. So far, you can think of them as though they're automated snapshots, because that's what they are. They occur during a backup window which is defined on the instance. You can allow AWS to pick one at random or use a window which fits your business. If you're using single AZ, you should make sure that this happens during periods of little to no use, as again there will be an I/O pause. If you're using multi-AZ, this isn't a concern, as the backup occurs from the standby.

In addition to this automated snapshot, every five minutes, database transaction logs are also written to S3. Transaction logs store the actual operations which change the data, so operations which are executed on the database. And together with the snapshots created from the automated backups, this means a database can be restored to a point in time with a five-minute granularity. In theory, this means a five-minute recovery point objective can be reached. Now automated backups aren't retained indefinitely; they're automatically cleared up by AWS, and for a given RDS instance, you can set a retention period from zero to 35 days. Zero means automated backups are disabled, and the maximum is 35 days. If you use a value of 35 days, it means that you can restore to any point in time over that 35-day period using the snapshots and transaction logs, but it means that any data older than 35 days is automatically removed.

When you delete the database, you can choose to retain any automated backups, but, and this is critical, they still expire based on the retention period. The way to maintain the contents of an RDS instance past this 35-day max retention period is that if you delete an RDS instance, you need to create a final snapshot, and this snapshot is fully under your control and has to be manually deleted as required. Now, RDS also allows you to replicate backups to another AWS region, and by backups, I mean both snapshots and transaction logs. Now, charges apply for both the cross-region data copy and any storage used in the destination region, and I want to stress this really strongly. This is not the default. This has to be configured within automated backups. You have to explicitly enable it.

Now let's talk a little bit about restores. The way RDS handles restores is really important, and it's not immediately intuitive. It creates a new RDS instance when you restore an automated backup or a manual snapshot. Why this matters is that you will need to update applications to use the new database endpoint address because it will be different than the existing one. When you restore a manual snapshot, you're restoring the database to a single point in time. It's fixed to the time that the snapshot was created, which means it influences the RPO. Unless you created a snapshot right before a failure, then chances are the RPO is going to be suboptimal. Automated backups are different. With these, you can choose a specific point to restore the database to, and this offers substantial improvements to RPO. You can choose to restore to a time which was minutes before a failure.

The way that it works is that backups are restored from the closest snapshot, and then transaction logs are replayed from that point onwards, all the way through to your chosen time. What's important to understand though is that restoring snapshots isn't a fast process. If appropriate for the exam that you're studying, I'm going to include a demo where you'll get the chance to experience this yourself practically. It can take a significant amount of time to restore a large database, so keep this in mind when you think about disaster recovery and business continuity. The RDS restore time has to be taken into consideration.

Now in another video elsewhere in this course, I'm going to be covering read replicas, and these offer a way to significantly improve RPO if you want to recover from failure. So, RDS automated backups are great as a recovery to failure, or as a restoration method for any data corruption, but they take time to perform a restore, so account for this within your RTO planning. Now once again, if appropriate for the exam that you're studying, you're going to get the chance to experience a restore in a demo lesson elsewhere in the course, which should reinforce the knowledge that you've gained within this theory video. If you don't see this then don't worry, it's not required for the exam that you're studying.

At this point though, that is everything I wanted to cover in this video, so go ahead and complete the video, and when you're ready, I'll look forward to you joining me in the next.

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

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Reply to the reviewers

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

__* SUMMARY

This study utilizes the developing chicken neural tube to assess the regulation of the balance between proliferative and neurogenic divisions in the vertebrate CNS. Using single-cell RNAseq and endogenous protein tagging, the authors identify Cdkn1c as a potential regulator of the transition towards neurogenic divisions. Cdkn1c knockdown and overexpression experiments suggest that low Cdkn1c expression enhances neurogenic divisions. Using a combination of clonal analysis and sequential knockdown, the authors find that Cdkn1c lengthens the G1 phase of the cell cycle via inhibition of cyclinD1. This study represents a significant advance in understanding how cells can transition between proliferative and asymmetric modes of division, the complex and varying roles of cycle regulators, and provides technical advance through innovative combination of existing tools.

MAJOR AND MINOR COMMENTS *__

Overall Sample numbers are missing or unclear throughout for all imaging experiments. The authors should add numbers of cells analysed and/or numbers of embryos for their results to be appropriately convincing.

This information is now provided in the figure legends (numbers of cells analyzed and/or numbers of embryos) except for data in Figure 5, which are presented in a new Supplementary Table

Values and error bars on graphs must be defined throughout. Are the values means and error bars SD or SEM?

We have used SD throughout the study. This information has now been added in figure legends.

Results 2

____A reference should be provided for cell type distribution in spinal neural tube, where the authors state that cell bodies of progenitors reside within the ventricular zone.

We now cite a recent review on spinal cord development (Saade and E. Marti, Nature Reviews Neuroscience, 2025) to illustrate this point

The authors state that Cdkn1c "was expressed at low levels in a salt and pepper fashion in the ventricular zone, where the cell bodies of neural progenitors reside, and markedly increased in a domain immediately adjacent to this zone which is enriched in nascent neurons on their way to the mantle zone. In contrast, the transcript was completely excluded from the mantle zone, where HuC/D positive mature neurons accumulate." It is not clear if this is referring only to E4 or also to E3 embryos. Indeed, Cdkn1c expression appears to be much more salt and pepper at E3 and only resolves into a clear domain of high expression adjacent to the mantle zone at E4. It may be helpful if this expression pattern could be described in a bit more detail highlighting the changes that occur between E3 and E4.

We have now reformulated this paragraph as follows: "At E3, the transcript was expressed at low levels in a salt and pepper fashion in the ventricular zone, where the cell bodies of neural progenitors reside (Saade and Marti, 2025)). One day later, at E4, this salt and pepper expression was still detected in the ventricular zone, while it markedly increased in the region of the mantle zone that is immediately adjacent to the ventricular zone. This region is enriched in nascent neurons on their way to differentiation that are still HuC/D negative. In contrast, the transcript was completely excluded from the more basal region of the mantle zone, where mature HuC/D positive neurons accumulate.

It would be useful to annotate the ISH images in Fig 2A to show the ventricular and mantle zones as defined by immunofluorescence.

Thank you for the suggestion. We have now added a dotted line that separates the ventricular zone from the mantle zone at E3 and E4 in Figure 2A

Reference should be included for pRb expression dynamics.

This section has been rewritten in response to comments from Reviewer #3, and now contains several references regarding pRb expression dynamics. See detailed response to Reviewer #3 for the new version

Could the Myc tag insertion approach disrupt protein function or turnover? ____Why was the insertion target site at the C terminus chosen?

The first reason was practical: at the time when we decided to generate a KI in Cdkn1c, we had already generated several successful KIs at C-termini of other genes, in particular using the P2A-Gal4 approach (see Petit-Vargas et al, 2024), and had not yet experimented with N-terminal Gal4-P2A. We therefore decided to use the same approach for Cdkn1c.

We also chose to target the C-terminus to avoid affecting the active CKI domain which is located at the N-terminus.

Nevertheless, the C-terminal targeting may have an impact on the turnover: it has been described that CDK2 phosphorylation of a Threonin close to the C-terminus of Cdkn1c leads to its targeting for degradation by the proteasome from late G1 (Kamura et al, PNAS, 2003; doi: 10.1073/pnas.1831009100). We can therefore not rule out that the addition of the Myc tags close to this phosphorylation site modulates the dynamics of Cdkn1c degradation. We note, however, that we observed little overlap between the Cdkn1c-Myc and pRb signals in cycling progenitors, suggesting that Cdkn1c is effectively degraded from late G1.

OPTIONAL Could a similar approach be used to tag Cdkn1c with a fluorescent protein to enable live imaging of dynamics?

Although it could be done, we have not attempted to do this for CDKN1c because our current experience of endogenous tagging of several genes with a similar expression level (based on our scRNAseq data) and nuclear localization (Hes5, Pax7) with a fluorescent reporter shows that the fluorescent signal is extremely low or undetectable in live conditions; Therefore we favored the multi-Myc tagging approach, and indeed we find that the Myc signal in progenitors is also very low even though it is amplified by the immunohistology method; this suggests that most likely, the only signal that would be detected -if any- with a fluorescent approach would be the peak of expression in newborn neurons.

In suppl Fig 1C nlsGFP-positive cells are shown in the control shRNA condition. How can this be explained and does it impact the interpretation of the findings?

The reviewer refers to the control gRNA condition in panel C, that shows that two small patches of GFP-positive cells are visible in the whole spinal cord of this particular embryo.

Technically, the origin of these "background" cells could be multiple. A spontaneous legitimate insertion at the CDKN1c locus by homologous recombination is possible, although we tend to think it is unlikely, given the extremely short length of the arms of homology; illegitimate insertions of the Myc-P2A-Gal4 cassette at off-target sites of the control gRNA is a possibility. Alternatively, a low-level leakage of Gal4 expression from the donor vector could lead to a detectable nls-GFP expression in a few cells via Gal4-UAS amplification.

In any case, these cells are observed at a very low frequency (1 or 2 patches of cells/embryo) relative to the signal obtained in presence of the CDKN1c gRNA#1 (probably several thousand positive cells per embryo). This suggests that if similar "background" cells are also present in presence of the CDKN1c gRNA, they would not significantly contribute to the signal, and would not impact the interpretation.

In Fig 2B, there are a number of Myc labelled cells in the mantle zone, whereas the in situ images show no appreciable transcript expression. Is this because the protein but not the transcript is present in these cells? Could the authors comment on this?

It is indeed possible that the CDKN1c protein is more stable than the transcript in newborn neurons and remains detectable in the mantle zone after the mRNA disappears. In Gui et al, 2006, where they use an anti-CDKN1c antibody to label the protein in mouse spinal cord transverse sections at E11.5 (Figure 1B), a few positive cells are also visible basally. They could correspond to neurons that have not yet degraded CDKN1c, although it is unclear in the picture whether these cells are really in the mantle zone or in the adjacent dorsal root ganglion; we note that a similar differential expression dynamics between mRNA and protein has been described for Tis21/Btg2 in the developing mouse cortex, where the protein, but not the mRNA, is detected in some differentiated bIII-tubulin-positive neurons (Iacopetti et al, 1999).

However, related to our response above to a previous comment from the same reviewer, we cannot rule out the possibility that the Myc tags modulate the turnover of CDKN1c protein and slow down the dynamics of its degradation in differentiating neurons.

We have added a sentence to indicate the presence of these cells: "In addition, a few Myc-positive cells were located deeper in the mantle zone, where the transcript is no more present, suggesting that the protein is more stable than the transcript."

Results

It should be mentioned how mRNA expression levels were quantified in the shRNA validation experiment (supp Fig 2A).

We did not quantify the level of mRNA reduction, it was just evaluated by eye. The reason for choosing shRNA1 for the whole study was dictated by 1) the fact that we more consistently saw (by eye) a reduction in the signal on the electroporated side with this construct than with the other shRNAs, and 2) that the effect on neurogenesis was also more consistent.

We will perform additional experiments to provide some quantitation of the shRNA effect, as this is also requested by Reviewer #3.

As our Cdkn1c KI approach offers a direct read-out of the protein levels in the ventricular and mantle zones, and since our shRNA strategy of "partial knock-down" is based on the idea that the shRNA effect should be more complete in progenitors expressing Cdkn1c at low levels than in newborn progenitors that express the protein at a higher level, we propose to validate the shRNA in the Cdkn1c-Myc knock-in background, by comparing the Myc signal intensity between control and Cdkn1c shRNA conditions

Figure panels are not currently cited in order. Citation or figure order could be changed.

We have now added a common citation of the panels referring to analyses at 24 and 48 hours after electroporation (now Figure 3A-F), allowing us to display the experimental data on the figure according to the timing post electroporation, while the text details the phenotype at the later time point first.

The authors should provide representative images for the graphs shown in Fig 3A and 3B. These could go into supplementary if the authors prefer.

We have added images in a revised version of the Figure 3, as requested

A supplementary figure showing the Caspase3 experiment should be added.

We have added data showing Caspase3 experiments in Supplementary Figure 3D

OPTIONAL. Identification of sister cells in the clonal analysis experiments is based on static images and cannot be guaranteed. Could live imaging be used to watch divisions followed by fixation and immunostaining to confirm identity?

We agree with the reviewer that direct tracking is the most direct method for the identification of pairs of sister cells. However, it remains technically challenging, and the added value compared to the retrospective identification would be limited, while requiring a great workload, especially considering the many different experimental conditions that we have explored in this study.

Results 4

How did the authors quantify the intensity of endogenous Myc-tagged Cdkn1c to confirm the validity of the Pax7 locus knock in? Can they show that the expression level was consistently lower than the endogenous expression in neurons? Quantification and sample numbers should be shown.

We have not done these quantifications in the original version of the study. We will add a quantification of the signal intensity in the ventricular and mantle zones for the revised version of the manuscript, as also requested by reviewer #3.

In Fig 4B, the brightness of row 2 column 1 is lower than the same image in row 2 column 2, which is slightly misleading, since it makes the misexpressed expression level look lower than it is compared with endogenous in column 3. Is this because only a single z-section is being displayed in the zoomed in image? If so, this should be stated in the figure legend.

All images in the figure are single Z confocal images. Images in Column 2 (showing both electroporated sides of the same tube) were acquired with a 20x objective, whereas the insets shown in Columns 1 and 3 are 100x confocal images. 100x images on both sides were acquired with the same acquisition parameters, and the display parameters are the same for both images in the figure. The signal intensity can therefore be compared directly between columns 1 and 3.

We have modified the legend of the Figure to indicate these points: "The insets shown in Columns 1 and 3 are 100x confocal images acquired in the same section and are presented with the same display parameters".

In Fig 4D, the increase in neurogenic divisions is mainly because of the rise in terminal NN divisions according to the graph, but no clear increase in PN divisions. Could the authors comment on the significance of this?

Our interpretation is that Pax7-CDKN1c misexpression experiments cause both PP to PN and PN to NN conversions. This is coherent with the classical idea of a progressive transition between these three modes of division in the spinal cord. Coincidentally, in our experimental conditions (timing of analysis and level of overexpression), the increase in PN resulting from PP to PN conversions is perfectly balanced by a decrease resulting from PN to NN conversions, giving the artificial impression that the PN compartment is unaffected. A less likely hypothesis would be that misexpression directly transforms symmetric PP into symmetric NN divisions, and that asymmetric PN divisions are insensitive to CDKN1c levels. We do not favor this hypothesis, because one would expect, in that case, that the shRNA approach would also not affect the PN compartment, and it is not what we have observed (see Figure 3H - previously 3F).

We have modified the manuscript to elaborate on our interpretation of this result: "We observed an increase in the proportion of terminal neurogenic (NN) divisions and a decrease in proliferative (PP) divisions (Figure 4D). This suggests that CDKN1c premature expression in PP progenitors converts them to the PN mode of division, while the combined endogenous and Pax7-driven expression of CDKN1c converts PN progenitors to the NN mode of division. Coincidentally, at the stage analyzed, PP to PN conversions are balanced by PN to NN conversions, leaving the PN proportion artificially unchanged. The alternative interpretation of a direct conversion of symmetric PP into symmetric NN divisions is less likely, because the PN compartment was affected in the reciprocal CDKN1c shRNA approach (see Figure 3H)."

Results 5 ____The proportion of pRb-positive progenitors having entered S phase was stated to be higher at all time points; however, it is not significantly higher until 6h30 and is actually trending lower at 2h30.

Thank you for pointing this out. We have modified the sentence in the main text.

"We found that the proportion of pRb positive progenitors having entered S phase (EdU positive cells) was significantly higher at all time points examined more than 4h30 after FT injection in the Cdkn1c knock-down condition compared to the control population (Figure 5D)"

OPTIONAL Could CyclinD1 activity be directly assessed?

This is an interesting suggestion. For example, using the fluorescent CDK4/6 sensor developed by Yang et al (eLife, 2020; https://doi.org/10.7554/eLife.44571) in a CDKN1c shRNA condition would represent an elegant experimental alternative to complement our rescue experiments with the double CDKN1c/CyclinD1 shRNA. However, we fear that setting up and calibrating such a tool for in vivo usage in the chick embryo represents too much of a challenge for incorporation in this study.

General ____Scale bars missing fig s1c s4d.

Thanks for pointing this out. Scale bars have been added in the figures and corresponding legends

OPTIONAL Some of the main findings be replicated in another species, for example, mouse or human to examine whether the mechanism is conserved.

OPTIONAL Could use approaches other than image analysis be used to reinforce findings, for example biochemical methods, RNAseq or FACS?

We agree that it will be interesting and important that our findings are replicated in other species, experimental systems, and even tissues, or by alternative experimental approaches. Nevertheless, it is probably beyond the scope of this study.

A model cartoon to summarise outcomes would be useful.

We thank the reviewer for the suggestion. We will propose a summary cartoon for the revised version of the manuscript.

Unclear how cells were determined to be positive or negative for a label. Was this decided by eye? If so, how did the authors ensure that this was unbiased?

Positivity or negativity was decided by eye. However, for each experiment, we ensured that all images of perturbed conditions and the relevant controls were analyzed with the same display parameters and by the same experimenter to guarantee that the criteria to determine positivity or negativity were constant.

Reviewer #1 (Significance (Required)):

SIGNIFICANCE

Strengths: This manuscript investigates the mechanisms regulating the switch from symmetric proliferative divisions to neurogenic division during vertebrate neuronal differentiation. This is a question of fundamental importance, the answer to which has eluded us so far. As such, the findings presented here are of significant value to the neurogenesis community and will be of broad interest to those interested in cell divisions and asymmetric cell fate acquisition. Specific strengths include:

• Variety of approaches used to manipulate and observe individual cell behaviour within a physiological context.
• A limitation of using the chicken embryo is the lack of available antibodies for immunostaining. The authors take advantage of recent advances in chicken embryo CRISPR strategy to endogenously tag the target protein with Myc, to facilitate immunostaining.
• Innovative combination of genetic and labelling tools to target cells, for example, use of FlashTag and EdU in combination to more accurately assess G1 length than the more commonly used method.
• Premature misexpression demonstrates that the previously observed dynamics indeed regulate cell fate.
• Mechanistic insight by examining downstream target CyclinD1.
• Clearly presented with useful illustrations throughout.
• Logic is clear and examination thorough.
• Conclusions are warranted on the basis of their findings. ____Limitations ____T____his study primarily used visual analysis of fixed tissue images to assess the main outcomes. To reinforce the conclusions, these could be supplemented with live imaging to appreciate dynamics, or biochemical techniques to look at protein expression levels.

Some aspects of quantification require explanation in order for the experiments to be replicated.

It is imperative that precise sample sizes are included for all experiments presented.

Advance: ____First functional demonstration role for Cdkn1c in regulating neurogenic transition in progenitors.

Conceptual advance suggesting Cdkn1c has dual roles in driving neurogenesis: promoting neurogenic divisions of progenitors and the established role of mediating cell cycle exit previously reported.

Technical advances in the form of G1 signposting and endogenous Myc tagging using CRISPR in chicken embryonic tissue.

Audience:

Of broad interest to developmental biologists. Could be relevant to cancer, since Cdkn1c is implicated.

Please define your field of expertise with a few keywords to help the authors contextualize your point

Developmental biology, vertebrate embryonic development, neuronal differentiation, imaging. Please note that we have not commented on RNAseq experiments as these are outside of our area of expertise.

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

The work by Mida and colleagues addresses important questions about neurogenesis in the embryo, using the chicken neural tube as their model system. The authors investigate the mechanisms involved in the transition from stem cell self-renewal to neurogenic progenitor divisions, using a combination of single cell, gene functional and tracing studies.

The authors generated a new single cell data set from the embryonic chicken spinal cord and identify a transitory cell population undergoing neuronal differentiation, which expresses Tis21, Neurog2 and Cdkn1c amongst other genes. They then study the role of Cdkn1c and investigate the hypothesis that it plays a dual role in spinal cord neurogenesis: low levels favour transition from proliferative to neurogenic divisions and high levels drive cell cycle exit and neuronal differentiation.

Major comments

I have only a general comment related to the main point of the paper. The authors claim that Cdkn1c onset in cycling progenitor drives transition towards neurogenic modes of division, which is different from its role in cell cycle exit and differentiation. Figures 3F and 4D are key figures where the authors analysed PP, PN and NN mode of divisions via flash tag followed by analysis of sister cell fate. If their assumption is correct, shouldn't they also see, for example in Fig. 4D, an increase in PN or is this too transient to be observed or is it bypassed?

As already stated in our response to a similar question from reviewer #1, our interpretation is that Pax7-CDKN1c misexpression experiments cause both PP to PN and PN to NN conversions. This is coherent with the classical idea of a progressive transition between these three modes of division in the spinal cord. Coincidentally, in our experimental conditions (timing of analysis and level of overexpression), the increase in PN resulting from PP to PN conversions is perfectly balanced by a decrease resulting from PN to NN conversions, giving the artificial impression that the PN compartment is unaffected. A less likely hypothesis would be that misexpression directly transforms symmetric PP into symmetric NN divisions, and that asymmetric PN divisions are insensitive to CDKN1c levels. We do not favor this hypothesis, because one would expect, in that case, that the shRNA approach would also not affect the PN compartment, and it is not what we have observed (see Figure 3H - previously 3F).

At the moment, the calculations of PN and NN frequencies are merged in the text, so perhaps describing PN and NN numbers separately will help better understand the dynamics of this gradual process (especially since there is little to no difference in PN).

Regarding the results of Pax7 overexpression presented in figure 4D (now Figure 4E in the revised version), we had made the choice to merge PN and NN values in the main text to focus on the neurogenic transition from PP to PN/NN collectively. We agree with this reviewer, as well as with reviewer #1, that it should be more detailed and better discussed. We therefore propose to modify the paragraph as follows (and as already indicated above in the response to reviewer #1):

"We observed an increase in the proportion of terminal neurogenic (NN) divisions and a decrease in proliferative (PP) divisions (Figure 4D). This suggests that Cdkn1c premature expression in PP progenitors converts them to the PN mode of division, while the combined endogenous and Pax7-driven expression of Cdkn1c converts PN progenitors to the NN mode of division. Coincidentally, at the stage analyzed, PP to PN conversions are balanced by PN to NN conversions, leaving the PN proportion artificially unchanged. The alternative interpretation of a direct conversion of symmetric PP into symmetric NN divisions is less likely, because the PN compartment was affected in the reciprocal Cdkn1c shRNA approach (see Figure 3F, now 3H)."

Could the increase in NN be compatible also with a role in cell cycle exit and differentiation, for example from cells that have been targeted and are still undergoing the last division (hence marked by flash tag) or there won't be any GFP cells marked by flash tag a day after expression of high levels of Cdkn1c?

It is likely that a proportion of cells that would normally have done a NN division are pushed to a direct differentiation that bypasses their last division in the Pax7-CDKN1c condition, and that they contribute to the general increase in neuron production observed in our quantification 48hae (Figure 3F -previously 3C). However, these cases would not contribute to the increase in the NN quantification in pairs of sister cells 6 hours after division at 24hae (Figure 4E - previously 4D), because by design they would not incorporate FlashTag. The rise in NN is therefore the result of a PN to NN conversion.

Basically, what would the effect of expressing higher levels of Cdkn1c be? I guess this will really help them distinguish between transition to neurogenic division rather than neuronal differentiation. If not experimentally, any further comments on this would be appreciated.

These experiments have been performed and presented in the study by Gui et al., 2007, which we cite in the paper. Using a strong overexpression of CDKN1c from the CAGGS promoter, they showed a massive decrease in proliferation, assessed by BrdU incorporation, 24hours after electroporation. We will cite this result more explicitly in the main text, and better explain the difference of our approach. We propose the following modification

« We next explored whether low Cdkn1c activity is sufficient to induce the transition to neurogenic modes of division. A previous study has shown that overexpression of Cdkn1c driven by the strong CAGGS promoter triggers cell cycle exit of chick spinal cord progenitors, revealed by a drastic loss of BrdU incorporation 1 day after electroporation (Gui et al., 2007). As this precludes the exploration of our hypothesis, we developed an alternative approach designed to prematurely induce a pulse of Cdkn1c in progenitors, with the aim to emulate in proliferative progenitors the modest level of expression observed in neurogenic progenitors. We took advantage of the Pax7 locus, which is expressed in progenitors in the dorsal domain at a level similar to that observed for Cdkn1c in neurogenic precursors (Supplementary Figure 6A)."

* * Minor comments

Fig 3C my understanding is that HuC/D should be nuclear, but in fig 3C it seems more cytoplasmic (any comment?)

Some studies suggest that HuC/D can, under certain conditions, be observed in the nucleus of neurons. However, HuC/D is a RNA binding protein whose localization is mainly expected to be cytoplasmic. In our experience (Tozer et al, 2017), and in other publications using the antibody in the chick spinal cord (see, for example, le Dreau et al, 2014), it is observed in the cell body of differentiated neurons, as in the current manuscript.

Fig Suppl 3E (and related 4B), immuno for Cdkn1c-Myc: to help the reader understand the difference between the immuno signals when looking at the figure, I would suggest writing on the panel i) Pax7-Cdkn1c-Myc and ii) endogenous Cdkn1c-Myc, rather than 'misexpressed' and 'endogenous', which is slightly confusing (especially because what it is called endogenous expression is higher).

This has now been modified in the figures.

Literature citing: Introduction and discussion are very nicely written, although they could benefit from some more recent literature on the topic. For example, Cdkn1c role as a gatekeeper of stem cell reserve in the stomach, gut, (Lee et al, CellStemCell 2022 PMID: 35523142) or some other work on symmetric/asymmetric divisions and clonal analysis in zebrafish (Hevia et al, CellRep 2022 PMID: 35675784, Alexandre et al, NatNeur PMID: 20453852), mammals (Royal et al, Elife 2023 37882444, Appiah et al, EMBO rep 2023 PMID: 37382163). Also, similar work has been performed in the developing pancreatic epithelium, where mild expression of Cdkn1a under Sox9rtTa control was used to lengthen G1 without overt cell cycle exit and this resulted in Neurog3 stabilization and priming for endocrine differentiation (Krentz et al, DevCell 2017 PMID: 28441528), so similar mechanisms might be in in place to gradually shift progenitor towards stable decision to differentiate. Moreover, in the discussion, alongside Neurog2 control of Cdkn1c, it could be mentioned that the feedback loop between Cdk inhibitors and neurogenic factor is usually established via Cdk inhibitor-mediated inhibition of proneural bHLHs phosphorylation by CDKs (Krentz et al, DevCell 2017 PMID: 28441528, Ali et al, 24821983, Azzarelli et al 2017 - PMID: 28457793; 2024 - PMID:39575884). Further, in the discussion, could they mention anything about the following open questions: is there evidence for Cdkn1c low/high expression in mammalian spinal cord? Or maybe of other Cdk inhibitors? Is Cdkn1c also involved in cell cycle exit during gliogenesis? Or is there another Cdk inhibitor expressed at later developmental stages, hence linking this with specific cell fate decisions?

We will modify the introduction and discussion in several instances, in order to address the above suggestions and we will:

• add references to its role in other contexts and/or species.

• expand the discussion on the cross talk between neurogenic factors and CDK inhibitors in other cellular contexts.

• add a dedicated paragraph in the discussion to answer reviewer#2's questions: is there evidence for Cdkn1c low/high expression in mammalian spinal cord? Or maybe of other Cdk inhibitors? Is Cdkn1c also involved in cell cycle exit during gliogenesis or is there another Cdk inhibitor expressed at later developmental stages?

Reviewer #2 (Significance (Required)):

The work here presented has important implications on neural development and its disorders. The authors used the most advanced technologies to perform gene functional studies, such as CRISPR-HDR insertion of Myc-tag to follow endogenous expression, or expression under endogenous Pax7 promoter, often followed by flash tag experiments to trace sister cell fate, and all of this in an in vivo system. They then tested cell cycle parameters, clonal behaviour and modes of cell division in a very accurate way. Overall data are convincing and beautifully presented. The limitation is potentially in the resolution between the events of switching to neurogenic division versus neuronal differentiation, which might just warrant further discussion. This work advances our knowledge on vertebrate neurogenesis, by investigating a key player in proliferation and differentiation.

____I believe this work will be of general interest to developmental and cellular biologists in different fields. Because it addresses fundamental questions about the coordination between cell cycle and differentiation and fate decision making, some basic concepts can be translated to other tissues and other species, thus increasing the potential interested audience.

My work focuses on stem cell fate decisions in mammalian systems, and I am familiar with the molecular underpinnings of the work here presented. However, I am not an expert in the chicken spinal cord as a model and yet the manuscript was interesting. I am also not sufficiently expert in the bioinformatic analysis, so cannot comment on the technical aspects of Figure 1 and the way they decided to annotate their data.

__*

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

Summary: In this study, Mida et al. analyze large-scale single-cell RNA-seq data from the chick embryonic neural tube and identify Cdkn1c as a key molecular regulator of the transition from proliferative to neurogenic cell divisions, marking the onset of neurogenesis in the developing CNS. To confirm this hypothesis, they employed classical techniques, including the quantification of neural cell-specific markers combined with the flashTAG label, to track and isolate isochronic cohorts of newborn cells in different division modes. Their findings reveal that Cdkn1c expression begins at low levels in neurogenic progenitors and becomes highly expressed in nascent neurons. Using a classical knockdown strategy based on short hairpin RNA (shRNA) interference, they demonstrate that Cdkn1c suppression promotes proliferative divisions, reducing neuron formation. Conversely, novel genetic manipulation techniques inducing low-level CDKN1c misexpression drive progenitors into neurogenic divisions prematurely.

By employing cumulative EdU incorporation assays and shRNA-based loss-of-function approaches, Mida et al. further show that Cdkn1c extends the G1 phase by inhibiting cyclin D, ultimately concluding that Cdkn1c plays a dual role: first facilitating the transition of progenitors into neurogenic divisions at low expression levels, and later promoting cell cycle exit to ensure proper neural development.

This study presents several ambiguities and lacks precision in its analytical methodologies and quantification approaches, which contribute to confusion and potential bias. To enhance the reliability of the conclusions, a more rigorous validation of the methods employed is essential.

This study introduces a novel approach to tracking the fate of sister cells from neural progenitor divisions to infer the division modes. While previous methods for analyzing the division mode of neural progenitor cells have been implemented, rigorous validation of the approach introduced by Mida et al. is necessary. Furthermore, the concept of cell cycle regulators interacting to control the duration of specific cell cycle stages and influencing progenitor cell division modes has been explored before, potentially limiting the novelty of these findings.

Major comments:

1.-The study presents ambiguity and lacks precision in quantifying neural precursor division modes. The authors use phosphorylated retinoblastoma protein (pRb) as a marker for neurogenic progenitors, claiming its reliability in identifying neurogenic divisions.

However, they do not provide a thorough characterization of pRb expression in the developing chick neural tube, leaving its suitability as a neurogenic division marker unverified.

Throughout their comments on the manuscript, this reviewer raises several points regarding the characterization of pRb expression in our model and of our use of this marker in our study. We take these comments into account and propose to expand on pRb characteristics in the first occurrence of pRb as a marker of cycling cells in the manuscript. The modifications rely on:

• the quotation of several studies showing that phosphorylation of Rb is regulated during the cell cycle, and that "it is not detectable during a period of variable length in early G1 in several cell types (Moser et al, 2018;Spencer et al, 2013; Gookin et al, 2017), including neural progenitors in the developing chick spinal cord (Molina et al, 2022). Apart from this absence in early G1, pRb is detected throughout the rest of the cell cycle until mitosis".

• a more detailed description of our own characterization of pRb dynamics in a synchronous cohort of cycling cells, which reveals a similar heterogeneity in the timing of the onset of Rb phosphorylation after mitosis. This description was initially shown in supplementary figure 3 and will be transferred to a new supplementary figure 2 to account for the fact that it will now be cited earlier in the manuscript.

Regarding the specific question the "suitability (of pRb) as a neurogenic division marker": we do not directly "use phosphorylated retinoblastoma protein (pRb) as a marker for neurogenic progenitors", but we use Rb phosphorylation to discriminate between progenitors (pRb+) and neurons (pRb-) identity in pairs of sister cells to retrospectively identify the mode of division of their mother.

Given that Rb is unphosphorylated during a period of variable length after mitosis (see references above), pRb is not a reliable marker of ALL cycling progenitors. We developed an assay to identify the timepoint (the maximal length of this "pRb-negative" phase) after which Rb is phosphorylated in all cycling progenitors (new Supplementary Figure 2). This assay relies on a time course of pRb detection in cohorts of FlashTag-positive pairs of sister cells born at E3. This time course experiment allowed us to identify a plateau after which the proportion of pRb-positive cells in the cohort remains constant. From this timepoint, this proportion corresponds to the proportion of cycling cells in the cohort. Rb phosphorylation therefore becomes a discriminating factor between cycling progenitors (pRb+) and non-cycling neurons (pRb-).

We are confident that this provides a solid foundation for the determination of the identity of pairs of sister cells in all our Flash-Tag based assays, which retrospectively identify the mode of division of a progenitor on the basis of the phosphorylation status of its daughter cells 6 hours after division.

We propose to modify the main text to describe the strategy and protocol more explicitly, by introducing the sentence highlighted in yellow in the following paragraph where the paired-cell analysis is first introduced (in the section on CDKN1c knock-down):

"This approach allows to retrospectively deduce the mode of division used by the mother progenitor cell. We injected the cell permeant dye "FlashTag" (FT) at E3 to specifically label a cohort of progenitors that undergoes mitosis synchronously (Baek et al., 2018; Telley et al., 2016 and see Methods), and let them develop for 6 hours before analyzing the fate of their progeny using pRb immunoreactivity (Figure 3D). Our characterization of pRb immunoreactivity in the tissue had established beforehand that 6 hours after mitosis, all progenitors can reliably be detected with this marker (Supplementary Figure 2, Methods). Therefore, at this timepoint after FT injection, two-cell clones selected on the basis of FT incorporation can be categorized as PP, PN, or NN based on pRb positivity (P) or not (N) (see Methods, new Figure 3G and new Supplementary Figures 2 and 4)."

We also modified accordingly the legend to Supplementary Figure 2 (previously Supplementary Figure 3, which describes the identification of the plateau of pRb.

Furthermore, retinoblastoma protein (Rb) and cyclin D interact crucially to regulate the G1/S phase transition of the cell cycle, with cyclin D/CDK complexes phosphorylating Rb. Since the authors conclude that CDKN1c primarily acts by inhibiting the cyclin D/CDK6 complex, it is likely that CDKN1c influences pRb expression or phosphorylation state. This raises the possibility that pRb could be a direct target of CDKN1c, whose expression and phosphorylation would be altered in gain-of-function (GOF) and loss-of-function (LOF) analyses of CDKN1c.

In light of this, it would be more appropriate to consider pRb as a CDKN1c target and discuss the molecular mechanisms regulating cell cycle components.

We agree with the reviewer that Rb phosphorylation may be a direct or indirect target of Cdkn1c activity, and exploring the molecular aspects of the cellular and developmental phenomena that we describe in our manuscript would represent an interesting follow up study.

____A more precise approach would involve using other markers or targets to quantify neural precursor division modes at earlier stages of neurogenesis.

To complement our analyses of the modes of division, we propose to use a positive marker to assess neural identity in parallel to the absence of pRb within pairs of cells. This approach may be the most meaningful in the gain of function context (Pax7 driven expression of Cdkn1c) because in this context, the time-point to reach the plateau of Rb phosphorylation used in our FT-based assay may indeed be delayed. On the opposite, in the context of loss of functions, the plateau may be reached earlier, which would have no effect on this assay.

2.-Furthermore, the study employs FlashTag labeling to track daughter cells post-division, but the 16-hour post-injection window may result in misidentification of sister cells due to the potential presence of FlashTagged cells that did not originate from the same division.

This introduces a risk of bias in quantification, data misinterpretation, and potential errors in defining division modes. A more rigorous validation of the FlashTag strategy and its specificity in tracking division pairs is necessary to ensure the reliability of their conclusions.

The reviewer probably mistyped and meant 6-hour post injection, which is the duration that we use for paired cell tracking. We would like to emphasize that in addition to the FlashTag label, we benefit from the electroporation reporter to assess clonality. Altogether, we combine 5 criteria to define a clonal relationship :

• 2 cells are positive for Flash Tag
• The Flash Tag intensity is similar between the 2 cells
• The 2 cells are positive for the electroporation reporter
• The electroporation reporter intensity is similar between the two cells
• the position of the two cells is consistent with the radial organization of clones in this tissue (Leber and Sanes, 1995;__; __Loulier et al, 2014): they are found on a shared line along the apico-basal axis, and share the same Dorso-Ventral and Antero-Posterior position . This combination is already described in the Methods section. We propose to modify the paragraph to include the sentence highlighted in yellow in the text below;

"Cell identity of transfected GFP positive cells was determined as follows: cells positive for pRb and FT were classified as progenitors and cells positive for FT and negative for pRb as neurons. In addition, a similar intensity of both the GFP and FT signals within pairs of cells, and a relative position of the two cells consistent with the radial organization of clones in this tissue (Leber and Sanes, 1995; Loulier et al, 2014) were used as criteria to further ascertain sisterhood. This combination restricts the density of events fulfilling all these independent criteria, and can confidently be used to ensure a robust identification of pairs of sister cells."

3.- The knock-in strategy used to tag the endogenous CDKN1c protein in Figure 2 is an elegant tool to infer protein dynamics in vivo. However, since strong conclusions regarding CDKN1c dynamics during the cell cycle are drawn from this section, it would be advisable to strengthen the results by including quantification with adequate replication and proper statistical analysis, as the current findings are preliminary and somewhat speculative.

- "Although pRb is specific for cycling cells, it is only detected once cells have passed the point of restriction during the G1 phase." Please provide literary reference confirming this observation.

We have entirely remodeled this section, which describes the expression of Myc-tagged Cdkn1c relative to pRb and now provide several references that describe the generally accepted view that pRb is specific of cycling cells, regulated during the cell cycle, and in particular absent in early G1. We also remove the mention of the "Restriction point" in the main text to avoid any confusion on the timing of phosphorylation, as the notion of restriction point is not useful in our study. The section now reads as follows:

"To ascertain that Cdkn1c is translated in neural progenitors, we used an anti-pRb antibody, recognizing a phosphorylated form of the Retinoblastoma (Rb) protein that is specifically detected in cycling cells (Gookin et al., 2017; Moser et al., 2018; Spencer et al., 2013) , including neural progenitors of the developing chick spinal cord (Molina et al., 2022). In the ventricular zone of transverse sections at E4 (48hae), we detected triple Cdkn1c-Myc/GFP/pRb positive cells (arrowheads in Figure 2B), providing direct evidence for the Cdkn1c protein in cycling progenitors. We also observed many double GFP/pRb positive cells that were Myc negative (arrowheads in Figure 2B). The observation of UAS-driven GFP in these pRb-positive cells is evidence for the translation of Gal4 and therefore provides a complementary demonstration that the Cdkn1c *transcript is translated in progenitors. The absence of Myc detection in these double GFP/pRb positive cells also suggests that Cdkn1c/Cdkn1c-Myc stability is regulated during the cell cycle. *

Finally, we observed double Myc/GFP-positive cells that were pRb-negative (Figure 2B; asterisks). One characteristic of Rb phosphorylation as a marker of cycling cells is a period in early G1 during which it is not detectable, as described in several cell types (Gookin et al., 2017; Moser et al., 2018; Spencer et al., 2013) including chick spinal cord neural progenitors (Molina et al., 2022). Using a method that specifically labels a synchronous cohort of dividing cells in the neural tube, we similarly observed a period in early G1 during which pRb is not detectable in some progenitors at E3 (See Supplementary Figure 2 and Methods). Hence, the double Myc/GFP positive and pRb negative cells may correspond to progenitors in early G1. Alternatively, they may be nascent neurons whose cell body has not yet translocated basally (see Figure 2C). Finally, we observed a pool of GFP positive/pRb negative nuclei with a strong Myc signal in the region of the mantle zone that is in direct contact with the ventricular zone (VZ), corresponding to the region where the transcript is most strongly detected (see Figure 2A). This pool of cells with a high Cdkn1c expression likely corresponds to immature neurons exiting the cell cycle and on their way to differentiation (Figure 2B; double asterisks). In addition, a few Myc positive cells were located deeper in the mantle zone, where the transcript is no more present, suggesting that the protein is more stable than the transcript.

In summary, our dual Myc and Gal4 knock-in strategy which reveals the history of Cdkn1c transcription and translation confirms that Cdkn1c is expressed at low level in a subset of progenitors in the chick spinal neural tube, as previously suggested (Gui et al., 2007; Mairet-Coello et al., 2012). In addition, the restricted overlap of Cdkn1c-Myc detection with Rb phosphorylation suggests that in progenitors, Cdkn1c is degraded during or after G1 completion. "

This section will again be remodeled in a future revised version of the manuscript, in which we will add quantifications of Myc levels, as requested by Reviewer 1 above, and also by Reviewer #3 below.

Given that pRb immunoreactivity is used as a marker for cycling progenitors to base many of the results of this study, it would be very valuable to characterize the dynamics of pRb in cycling cells in the studied tissue, for instance combined with the cell cycle reporter used by Molina et al. (Development 2022).

In the original version of the manuscript, the section describing the dynamics of CDKN1c-Myc in the KI experiments presented in Figure 2 relied on the idea that the dynamics of pRb in chick spinal progenitors is similar to what I described in other tissues and cell types, without providing any references to substantiate this fact. Actually, Molina et al provide a characterization of pRb in combination with their cell cycle reporter and conclude that pRb negative progenitors are in G1 ("We also verified that phospho-Rb- and HuC/D-negative cells were in G1 by using our FUCCI G1 and PCNA reporters"). We will now cite this reference to support our claim. In addition, our characterization of Rb progressive phosphorylation in the synchronic Flash-Tag cohort of newborn sister cells provides a complementary demonstration that a fraction of the progenitors are pRb-negative when they exit mitosis (i.e. in early G1). This analysis was initially only introduced in the supplementary Figure 3, as support for the section that presents the Paired-cell assay used in Figure 3. We propose to introduce the data from Supplementary Figure 3 earlier in the manuscript (now Supplementary Figure 2), in order to better introduce the reader with the dynamics of pRb in cycling cells in our model. This will better support our description of the Cdkn1c-Myc dynamics in relation with pRb. We therefore propose to reformulate this whole section as follows.

- It would be valuable to analyse the dynamics of Myc immunoreactivity in combination of pRb in all three gRNAs (highlighted in Supplementary Figure 1), as it would be a strong point in favour that the dynamics reflect the endogenous CDKN1c dynamics.

- It would be very valuable to provide a quantification of said dynamics (e.g. plotting myc intensity / pRb immunoreactivity along the apicobasal axis of the tissue).

These are two interesting suggestions. To complement our data with guide #1, we have performed Myc-immunostaining experiments on transverse sections in the context of guide #3, showing exactly the same pattern of Myc signal, with low expression in the VZ, and a peak of signal in the part of the mantle zone that is immediately touching the VZ. This confirms the specificity of the spatial distribution of the Cdkn1c-Myc signal. These data have been added in a revised version of Supplementary Figure 1.

We will perform the suggested quantifications using guides #1 and #3, which both show a good KI efficiency. We do not think it is useful to do these experiments with guide #2, whose efficiency is much lower, and which would lead to a very sparse signal.

- The characterization of dynamics is performed only with one of the gRNAs (#1) on the basis that it produces the strongest NLS-GFP signal, as a proxy for guide efficiency. It would be nice if the authors could validate guide cutting efficiency via sequencing (e.g. using a Cas9-T2A-GFP plasmid and sorting for positive cells).

We will perform these experiments to validate guide cutting efficiency using the Tide method (Brinkman et al, 2014)

- In order to make sure that the dynamics inferred from Myc-tag immunoreactivity do reflect the cell cycle dynamics of CDKN1c-myc, it would be advisable to confirm in-frame insertion of the myc-tag sequence.

We will perform genomic PCR experiments to confirm in-frame insertion of the Myc tags at the Cdkn1c locus

4.- In Figure 3, the authors use a short-hairpin-mediated knock-down strategy to decrease the levels of Cdkn1c, and show that this manipulation leads to an increase percentage of cycling progenitors and a decrease in the number of neurons in electroporated cells.

The authors claim that their shRNA-based knockdown strategy aims to reduce low-level Cdkn1c expression in neurogenic progenitors while minimally affecting the higher expression in newborn neurons required for cell cycle exit. However, several factors need consideration. Electroporation introduces variability in shRNA delivery, making it difficult to achieve consistent gene inhibition across all cells, especially for dose-dependent genes like Cdkn1c.

Additionally, Cdkn1c generates multiple isoforms, which may not be fully annotated in the chick genome, raising the possibility that the shRNA targets specific isoforms, potentially explaining the observed low expression.

All the predicted isoforms in the chick genome contain the sequence targeted by shRNA1, which is located in the CKI domain, the region of the protein that is most conserved between species. Besides, all the isoforms annotated in the mouse and human genomes also contain the region targeted by shRNA1. We are therefore confident that shRNA1 should target all chick isoforms.

A more rigorous approach, such as qPCR analysis of sorted electroporated cells, would better validate the expression levels, rather than relying on in situ hybridization, presenting electroporated and non-electroporated cells in the same section (Supp. Figure 2).

This approach (qRT-PCR on sorted cells) would enable us to focus solely on electroporated cells, but it would result in an averaged quantification of Cdkn1c depletion. In order to obtain additional information on the shRNA-dependent decrease in Cdkn1C in the different neural cell populations (progenitor versus differentiating neuron), we propose an alternative approach consisting in monitoring the level of Cdkn1c protein, assessed through Cdkn1c-Myc signal in knock-in cells, in the presence versus absence of Cdkn1c shRNA.

- As the authors note, "Unambiguous identification of cycling progenitors and postmitotic neurons is notoriously difficult in the chick spinal cord". "markers of progenitors usually either do not label all the phases of the cell cycle (eg. Phospho-Rb, thereafter pRb), or persist transiently in newborn neurons (eg. Sox2)." Given that pRb immunoreactivity is used as the basis for a lot of the conclusions in this study, it would be valuable to add a characterization of its dynamics as mentioned in Figure 2, as well as provide literary references/proof that Sox2 expression persists in newborn neurons.

We have addressed the case of pRb dynamics in progenitors above and added a reference documented pRb expression during the cell cycle of chick neural progenitors (Molina et al, 2022).

Regarding Sox2 persistence: we consistently detect a small fraction of double positive Sox2+/HuC/D+ cells in chick spinal cord transverse sections. We have shown that this marker of differentiating neurons (HuC/D) only becomes detectable more than 8 hours after mitosis in newborn neurons at E3 (Baek et al, 2018), indicating that Sox2 protein can persist for up to at least 8 hours in newborn neurons.

We now cite a paper showing that a similar persistence of Sox2 protein is reported in differentiating neurons of the human neocortex, where double Sox2/NeuN positive cells are frequently observed in cerebral organoids (Coquand et al, Nature Cell Biology 2024__)__

- The undefined population (pRb-/HuCD-) introduces an unknown that assumes that the percentage of progenitors in G1 phase before the restriction point and the number of newborn neurons are equal for both conditions in an experiment. Can the authors provide explanation for this assumption?

We do not think that these numbers are equal for both conditions, and we did not formulate this assumption. We only indicate (in the methods section) that this undefined/undetermined population (based on negativity for both markers) is a mix of two possible cell types. However, we do not offer any interpretation of the CDKN1c phenotypes based on the changes in this population. Indeed, our interpretation of the knock-down phenotype is solely based on the increase in pRb-positive and decrease in HuC/D-positive cells, which both suggest a delay in neurogenesis. We understand from the reviewer's comment that depicting an "undefined" population on the graph may cause some confusion. We therefore propose to present the data on pRb and HuC/D in different graphs, rather than on a combined plot, and to remove the reference to undefined cells in Figure 3, as well as in Figures 4 and 5 depicting the gain of function and double knock-down experiments. We have implemented these changes in updated versions of the figures.

- In Gui et al. (Dev Biol 2006), authors showed that a knockdown of Cdkn1c leads to a failure of nascent neurons to exit the cell cycle and causes them to re-entry the cell cycle, shown by ectopic mitoses. In that study, cells born from those ectopic mitoses eventually leave the cell cycle leading to an increase in the number of neurons. Can the authors check for ectopic mitoses at 24hpe and 48hpe?

We have now performed experiments with an anti phospho Histone 3 antibody, which labels mitotic cells, at 24 and 48 hours post electroporation. We do not see any ectopic mitoses upon Cdkn1c knock-down with this marker, and we have produced a Supplementary Figure with these data. This is consistent with the fact that we also do not see ectopic pRb or Sox2 positive cells in the mantle zone in the knock-down experiments. These data (pH3 and Sox2) have been added in the new Supplementary Figure 3E and F.

We have now modified the main text to include these data:

"In the context of a full knock-out of Cdkn1c in the mouse spinal cord, a reduction in neurogenesis was also observed, which was attributed to a failure of prospective neurons to exit the cell cycle, resulting in the observation of ectopic mitoses in the mantle zone (Gui et al, 2007). In contrast with this phenotype, using an anti phospho-Histone3 antibody, we did not observe any ectopic mitoses 24 or 48 hours after electroporation in our knock-down condition (Supplementary Figure 3E-F). This is consistent with the fact that we also do not observe ectopic cycling cells with pRb (Figure 3A and D) and Sox2 (Supplementary Figure 3E-F) antibodies. We therefore postulated that the reduced neurogenesis that we observe upon a partial Cdkn1c knock-down may result from a delayed transition of progenitors from the proliferative to neurogenic modes of division."

- The authors then address the question of whether the decrease in neuron number is due to the failure of newborn neurons to exit the cell cycle or to a delay in the transition from proliferative to neurogenic divisions. For that, they implement a strategy to label a synchronized cohort of progenitors based of incorporation of a FlashTag dye.

- Given that this strategy is the basis of many of the experiments in this article, it would be very valuable to expand on the validation of this technique as cited in major comment #2. In figure 3E, the close proximity of cell pairs in PP and PN clones shown in the pictures makes their sibling status apparent. However, this is not the case for the NN clone. Can the authors further explain with what criteria they determined the clonal status of two FlashTag labelled cells?

The key criterion for cells that are not directly touching each other is that their relative position corresponds to the classical "radial" organization of clones in this tissue (Leber and Sanes, 1995__; __Loulier et al, Neuron, 2014). In other words, we make sure that they are located on a same apico-basal axis, as is the case for the NN clone presented on the figure. As stated above in our response to major comment #2, we have modified the Methods section accordingly.

Can they provide further image examples of different types of clones?

We now provide additional examples in a new Supplementary Figure 4

- Can the authors show that the plateau reached in Sup Figure 3 for pRb immunoreactivity corresponds to a similar dynamic for HuC/D immunoreactivity?

The plateau for Rb phosphorylation in progenitors is reached before 6 hours post mitosis at E3. At the same age, we have previously shown (Baek et al, PLoS Biology 2018) in a similar time course experiment in pairs of FT+ cells that the HuC/D signal is not detected in newborn neurons 8 hours after mitosis. HuC/D only starts to appear between 8 and 12 hours, and still increases between 8 and 16 hours. The plateau would therefore be very delayed for HuC/D compared to pRb. This long delay in the appearance of this « positive » marker of neural differentiation is the main reason why we chose to use Rb phosphorylation status for the analysis of synchronous cohorts of pairs of sister cells, because pRb becomes a discriminating factor much earlier than HuC/D after mitosis.

- In order to further validate the strategy, could the authors use it at different stages to validate if they can replicate the different percentages of PP/PN/NN reported in the literature (e.g. Saade Cell Rep 2013)?

We have carried out similar experiments at E2, showing a plateau of 95% of pRb-positive cells in the FT-positive population (see graph on the right). This provides a retrospective estimate of the mode of division of the mother cells at this stage (roughly 90% of PP and 10% of PN) which is consistent with the vast majority of PP divisions described by Saade et al (2013, see Figure S1) at this stage.

5.- In Figure 4, the strategy used to induce a low-dose overexpression of CDKN1c is an elegant method to introduce CDKN1c-Myc expression under the control of the endogenous Pax7 promoter, active in proliferative progenitors. The main point to address is:

- Please provide proof that Pax7 expression is not altered in guides with a successful knock-in event (e.g. sorting and WB against the Pax7 protein) or the immunohistochemistry as performed in the Pax7-P2A-Gal4 tagging in Petit-Vargas et al., 2024.

We have now performed Pax7 immunostainings on transverse sections at 24 and 48 hours post electroporation, both with the Pax7-CDKN1c-Gal4 and with the Pax7-Gal4 control constructs. We present these data in the new supplementary figure 7. In both conditions, we find that the Pax7 protein is still present in KI-positive cells. We observe a modest increase in Pax7 signal intensity in these cells, suggesting either that the insertion of exogenous sequences stabilizes the Pax7 transcript, or that the C-terminal modification of Pax7 protein with the P2A tag increases its stability. This does not affect the interpretation of the CDKN1c overexpression phenotype, because we used the Pax7-Gal4 construct that shows the same modification of Pax7 stability as a control for this experiment. We have introduced this comment in the legend of Supplementary Figure 7.

- Given the cell cycle regulated expression and activity of CDKN1c, can the authors elaborate on whether this is regulated at the promoter level?

Cdkn1c transcription is regulated by multiple transcription factors and non-coding RNAs (see for example Creff and Besson, 2020, or Rossi et al, 2018 for a review). To our knowledge, these studies focus more on the regulation of Cdkn1c global expression than on the regulation of its levels during cell cycle progression. Although it is very likely that transcriptional regulation contributes, post-translational regulation, and in particular degradation by the proteasome, is also a key factor in the cell cycle regulation of Cdkn1c activity

If so, how does this differ from the promoter activity of Pax7?

The transcriptional regulation of Pax7 and Cdkn1c is probably controlled by different regulators, since their expression profiles are very different. Regardless of the mechanisms that control their expression, the rationale for choosing Pax7 as a driver for Cdkn1c expression was that Pax7 expression precedes that of Cdkn1c in the progenitor population, and that it disappears in newborn neurons, when that of Cdkn1c peaks. This provided us with a way to advance the timing of Cdkn1c expression onset in proliferative progenitors.

- It would be advisable to characterize the dynamics along the cell cycle for the overexpressed form of CDKN1c-Myc relative to pRb, similarly to what was done in Figure 2B.

We will carry out experiments similar to those shown in Figure 2B in order to characterise the dynamics of Cdkn1c in a context of overexpression, in relation to pRb.

In addition, we will include a more precise quantification of the "misexpressed" compared to "endogenous" Cdkn1c -Myc levels, as already mentioned in the answer to a request by reviewer1.

6.-In figure 5, the authors use a double knock-down strategy to test the hypothesis that the effect of Cdkn1c in G1 length is partially at least through its inhibition of CyclinD1. Results show that double shRNA-mediated knock-down of CyclinD1 and Cdkn1c counteracts the effects of Cdkn1c-sh alone on EdU incorporation, PP/PN/NN cell divisions and overall rations of progenitors and neurons.

- In the measurement of progenitor cell cycle length in Figure 5A, it would be more appropriate to present the nonlinear regression method described by Nowakowski et al. (1989), as has been commonly used in the field (Saade et al., 2013, PMID: 23891002, Le Dreau et al., 2014, PMID: 24515346, Arai et al., 2011, PMID: 21224845).

The Nowakowski non linear regression method has been used often in the literature in the same tissue, and is generally used to calculate fixed values for Tc, Ts, etc... This method is based on several selective criteria, and in particular the assumption that "all of the cells have the same cycle times". Yet, many studies have documented that cell cycle parameters change during the transition from proliferative to neurogenic modes of division during which our analysis is performed; live imaging data in the chick spinal cord have illustrated very different cell cycle durations at a given time point (see Molina et al). We therefore think that the proposed formulas do not reflect the heterogenous reality of neural progenitors of the embryonic spinal cord. However, the cumulative approach described by Nowakowski is useful to show qualitative differences between populations (e.g. a global decrease of the cycle length, like in our comparison between control and shRNA conditions). For these reasons, we prefer to display only the raw measurements rather than the regression curves.

- Cumulative EdU incorporation in spinal progenitors (pRb-positive) at E3 (24 hours after injection) showed that the proportion of EdU-positive progenitors reached a plateau at 14 hours in control conditions, which is later than what has been reported in Le Dreau et al., 2014 (PMID: 24515346). Can you explain why?

Le Dreau et al count the EdU+ proportion of cells in the total population of electroporated cells located in the VZ (which includes progenitors, but also future neurons that have been labelled during the previous cycles -at least for the time points after 2hours- and have not yet translocated to the mantle zone), whereas we only consider pRb+ progenitors in the analysis. In addition, the experiments are not performed at the same developmental stage. Altogether, this may account for the different curves obtained in our study.

- It would be interesting to measure G1 length as in Figure 5D for the double cdkn1c-sh - ccnd1-sh knock down condition, to see if it rescues G1 length. As well as in the Ccnd1 knock down condition alone to see if it increases G1 length in this context as well.

We will perform cumulative EDU incorporation experiments similar to that shown in Figure 5D to measure G1 length for the cdkn1c-sh - ccnd1-sh knock down double conditions, as well as in the Ccnd1 knock down condition alone.

Minor comments

__*Introduction:

• The introduction should include references of studies of the role of Cdkn1c in cortical development (Imaizumi et al. Sci Rep 2020, Colasante et al. Cereb Cortex 2015, Laukoter et al. ____Nature Communications 2020).*__

We will modify the introduction in several instances, in order to address suggestions by Reviewers #2 (see above) and #3, in particular to expand the description of the role of Cdkn1c during cortical development

1) Transcriptional signature of the neurogenic transition (Figure 1).

- In the result section, it would be informative to include the genes used to determine the progenitor and neuron score (instead of in Methods).

We have now listed the genes used to determine the progenitor and neuron score in the main text of the result section

- Figure 1A. It would be informative to add in the diagram what "filtering" means (eg. Neural crest cells).

We have now added the detail of what 'filtering' means in the diagram

- In the result section, "However, while Tis21 expression is switched off in neurons, Cdkn1c transiently peaks at high levels in nascent neurons before fading off in more mature cells." Missing literary reference or data to clearly demonstrate this point.

We have reworded this sentence, adding a reference to the expression profile of Tis 21. The paragraph now reads as follows:

« However, Cdkn1c expression is maintained longer and transiently peaks at high levels after Tis21 expression is switched off. Given that Tis21 is no more expressed in neurons (Iacopetti et al, 1999), this suggests that Cdkn1c expression is transiently upregulated in nascent neurons before fading off in more mature cells. »

- "Interestingly, the gene cluster that contained Tis21 also contained genes encoding proteins with known expression and/or functions at the transition from proliferation to differentiation, such as the Notch ligand Dll1, the bHLH transcription factors Hes6, NeuroG1 and NeuroG2, and the coactivator Gadd45g." Missing references.

We have now added references linking the function and/or expression profile of these genes to the neurogenic transition: Dll1 (Henrique et al., 1995), the bHLH transcription factors Hes6 (Fior and Henrique, 2005), NeuroG1 and NeuroG2 (Lacomme et al., 2012; Sommer et al., 1996) and the coactivator Gadd45g (Kawaue et al., 2014).

- There is an error in the color code in Cell Clusters in Figure 1C (cluster 4 yellow in the legend but ocre in the figure)

- Figure Sup3B colour code is switched (green for PP and red for NN) compared to the rest of the paper.

We have corrected the colour code errors in Figure 1c and Supp Figure 3B (now changed to Supplementary Figure 5 in the modified revision)

____It would be valuable to assign cell cycle stage to neural progenitor cells (based on cell cycle score) and determine whether cdkn1c at the transcript level also shows enrichment in G1 cells considered to be progenitors.

We have so far refrained from performing the suggested combined analysis based on cell cycle and cell type scores, as the "neurogenic progenitor population" (based on neurogenic progenitor score values) in which Cdkn1c expression is initiated represents a small number of cells in our scRNAseq, and felt that the significance of such an analysis is uncertain. We will perform this analysis in the revised version

2) Progressive increase in Cdkn1c/p57kip2 expression underlie different cellular states in the embryonic spinal neural tube (Figure 2).

- Figure 2A. Scale bar is missing in E3 and E4. It is important to consider the growth of the developing spinal cord and present it accordingly (E3 transverse section, Figure 2).

The scale bar is actually valid for the whole panel A. The E2 section in the original figure appeared as "large" as the E3 section along the DV axis probably because the cutting angle was not perfectly transverse at E2, artificially lengthening the section. In a new version of the figure, we have replaced the E2 images with another section from the same experiment. The scale bar remains valid for the whole panel.

- Figure 2 could use a diagram of the knock-in strategy used, similar as the one in Figure 4A.

We have now added a diagram for the knock-in strategy in Figure 2B, and modified the legend of the figure accordingly.

- Indicate hours post-electroporation. Indicate which guide is used in the main text.

We have now added the post-electroporation timing and guide used in the main text.

3) Downregulation of Cdkn1c in neural progenitors delays the transition from proliferative to neurogenic modes of division (Figure 3).

- In methods: "Thus, to reason on a more homogeneous progenitor population, we restricted all our analysis to the dorsal one half or two thirds of the neural tube." Indicate when and depending on what one half or two thirds of the neural tube were analysed.

- Are the clonal analysis experiments (Fig 3D, E and F) also restricted to the dorsal region?

__We have modified this sentence as follows: "__Thus, to reason on a more homogeneous progenitor population, we restricted all our analysis to the dorsal two thirds of the neural tube, except for the Pax7-Cdkn1c misexpression analysis, which was performed in the more dorsal Pax7 domain."

This is valid both for the whole population and clonal analyses

- Figure 3. Would have a better flow if 3C preceded 3A and 3B.

We have modified the Figure accordingly.

- Figure 3C. it would be informative to show pictures of the electroporated NT at both 24hpe and 48hpe, as well as highlighting the dorsal part of the neural tube that was used for quantification.

We have modified the Figure accordingly

- In methods "At each measured timepoint (1h, 4h, 7h, 10h, 12h, 14 and 17h after the first EdU injection), we quantified the number of EdU positive electroporated progenitors (triple positive for EdU, pRb and GFP) over the total population of electroporated progenitor cells (pRb and GFP positive) (Figure 3B)." Explanation does not correspond to Figure 3B.

This explanation corresponds indeed to Figure 5A. We have corrected this mistake in the new version of the manuscript.

4) Inducing a premature expression of Cdkn1c in progenitors triggers the transition to neurogenic modes of division (Figure 4.).

- "We took advantage of the Pax7 locus, which is expressed in progenitors in the dorsal domain at a level similar to that observed for Cdkn1c in neurogenic precursors (Supplementary Figure 4A)". Missing reference or data showing that Pax7 is restricted to the dorsal domain.

We have added references to the expression profile of Pax7 in the dorsal neural tube (Jostes et al, 1990). In addition, the new Supplementary Figure 7 shows anti-Pax7 staining that confirm this expression pattern at E3 and E4

- "its intensity was similar to the one observed for endogenous Myc-tagged Cdkn1c in progenitors (Figure 4B and Supplementary Figure 4E), and remained below the endogenous level of Myc-tagged Cdkn1c observed in nascent neurons, confirming the validity of our strategy". It would be valuable to add a quantification to demonstrate this point, either by fluorescence levels or WB of nls-GFP cells.

As stated in the response to Major Point 5 above, we will perform a quantification based on Myc immunofluorescence to compare endogenous Cdkn1c expression versus Cdkn1c expression upon overexpression.

- "At the population level, at E4, Cdkn1c expression from the Pax7 locus resulted in a strong reduction in the number of progenitors (pRb positive cells)". Indicate in the main text that this is 48hpe.

We have added in the main text that the quantification was performed 48hae.

- Legend of figure 4D should indicate that the quantification has been done 24hpe.

We have added the timing of quantification in the legend of Figure 4D.

- "To circumvent the cell cycle arrest that is triggered in progenitors by strong overexpression of Cdkn1c (Gui et al., 2007)". It would be advisable to expand on this reference on the text, or ideally to include a simple Cdkn1c overexpression experiment.

These experiments have been performed and presented in the study by Gui et al., 2007, which we cite in the paper. Using a strong overexpression of CDKN1c from the CAGGS promoter, they showed a massive decrease in proliferation, assessed by BrdU incorporation, 24hours after electroporation. We will cite this result more explicitly in the main text, and better explain the difference of our approach. We propose the following modification:

« We next explored whether low Cdkn1c activity is sufficient to induce the transition to neurogenic modes of division. A previous study has shown that overexpression of Cdkn1c driven by the strong CAGGS promoter triggers cell cycle exit of chick spinal cord progenitors, revealed by a drastic loss of BrdU incorporation 1 day after electroporation (Gui et al., 2007). As this precludes the exploration of our hypothesis, we developed an alternative approach designed to prematurely induce a pulse of Cdkn1c in progenitors, with the aim to emulate in proliferative progenitors the modest level of expression observed in neurogenic progenitors. We took advantage of the Pax7 locus, which is expressed in progenitors in the dorsal domain at a level similar to that observed for Cdkn1c in neurogenic precursors (Supplementary Figure 4A)."

- "We observed a massive increase in the proportion of neurogenic (PN and NN) divisions rising from 57% to 84% at the expense of proliferative pairs (43% PP pairs in controls versus 16% in misexpressing cells, Figure 4D)." adding the percentages in the main text is a bit inconsistent with how the rest of the data is presented in the rest of the sections.

This whole section has been modified in response to a question from reviewer 1. The new version does not contain percentages in the main text, and reads as follows:

« Using the FlashTag cohort labeling approach described above, we traced the fate of daughter cells born 24 hae. We observed an increase in the proportion of terminal neurogenic (NN) divisions and a decrease in proliferative (PP) divisions (Figure 4D). This suggests that CDKN1c premature expression in PP progenitors converts them to the PN mode of division, while the combined endogenous and Pax7-driven expression of CDKN1c converts PN progenitors to the NN mode of division. Coincidentally, at the stage analyzed, PP to PN conversions are balanced by PN to NN conversions, leaving the PN proportion artificially unchanged. The alternative interpretation of a direct conversion of symmetric PP into symmetric NN divisions is less likely, because the PN compartment was affected in the reciprocal CDKN1c shRNA approach (see Figure 3F). Overall, these data show that inducing a premature low-level expression of Cdkn1c in cycling progenitors is sufficient to accelerate the transition towards neurogenic modes of division. »

- Figure sup 4C includes references to 3 gRNAs even when only one is used in the study.

The three guides listed in the original Supplementary Figure 4C correspond to the guides that we tested in Petit-Vargas et al. 2024. In this study, we only used the most efficient of these three guides. We have modified Figure 4C by quoting only this guide.

5) The proneurogenic activity of Cdkn1c in progenitors is mediated by modulation of cell cycle dynamics (Figure 5)

- "we targeted the CyclinD1/CDK4-6 complex, which promotes cell cycle progression and proliferation, and is inhibited by Cdkn1c." reference missing

We have included references related to the activity of the CyclinD1/CDK4-6 complex in the developing CNS, and the antagonistic activities of CyclinD1 and Cdkn1c in this model

- "we targeted the CyclinD1/CDK4-6 complex, which promotes cell cycle progression and proliferation in the developing CNS (Lobjois et al, 2004, 2008, Lange 2009, Gui et al 2007), and is inhibited by Cdkn1c (Gui et al, 2007)."

- It would be informative to include experimental set-up information (e.g. hae) in Figures 5A, 5B, 5F and 5G.

We have added the experimental set-up information in Figure 5.

- Clarify if analysis is restricted to the dorsal progenitors or the whole dorsoventral length of the tube.

The analyses were carried out on two thirds of the neural tube (dorsal 2/3), excluding the ventral zone, as specified above (and in the Methods section)

- It would be valuable to add an image to illustrate what is quantified in Figure 5D, Figure F and Figure G.

- For Figure 4C and D, it would be valuable to add images to illustrate the quantification.

We have added images:

• in Supplementary Figure 7C to illustrate what is quantified in Figures 4C (now 4C and 4D);
• In Figure 5E to illustrate what is quantified in Figure 5D
• In Supplementary Figure 8B to illustrate what is quantified in Figure 5G (now Figure 5H and 5I) Regarding the requested images for Figures 4D and 5F, they correspond to the same types of images already shown in Figure 3E. Since we have now added several additional examples of representative pairs of each type of mode of division in the new Supplementary Figure 4, we do not think that adding more of these images in figures 4 and 5 would strengthen the result of the quantifications.

Discussion:

- "Nonetheless, studies in a wide range of species have demonstrated that beyond this binary choice, cell cycle regulators also influence the neurogenic potential of progenitors, i.e the commitment of their progeny to differentiate or not (Calegari and Huttner, 2003; FUJITA, 1962; Kicheva et al., 2014; Lange et al., 2009; Lukaszewicz and Anderson, 2011a; Pilaz et al., 2009; Smith and Schoenwolf, 1987; Takahashi et al., 1995)." Should include maybe references to Peco et al. Development 2012, Roussat et al. J Neurosci. 2023).

We have now included the references suggested by the reviewer.

- "This occurs through a change in the mode of division of progenitors, acting primarily via the inhibition of the CyclinD1/CDK6 complex." The data shown in the paper does not demonstrate that Cdkn1c is inhibiting CyclinD1, only that knocking down both mRNAs counteracts the effect of knocking down Cdkn1c alone at the general tissue level and in the percentage of PP/PN/NN clones. This statement should be qualified.

We propose to reformulate this paragraph in the discussion as follows to take this remark into account

"This allows us to re-interpret the role of Cdkn1c during spinal neurogenesis: while previously mostly considered as a binary regulator of cell cycle exit in newborn neurons, we demonstrate that Cdkn1c is also an intrinsic regulator of the transition from the proliferative to neurogenic status in cycling progenitors. This occurs through a change in their mode of division, and our double knock-down experiments suggest that the onset of Cdkn1c expression may promote this change by counteracting a CyclinD1/CDK6 complex dependent mechanism."

Other comments:

- To improve clarity for the reader, it would help if electroporation was shown consistently on the same side of the neural tube. If electroporation has been performed at different sides and this is reflected in the figures, it would be advisable to explain on the figure legend.

We have modified the figures to systematically show the electroporated side of the neural tube on the same side of the image for single electroporations.

____- Figure legends should include the number of embryos/tissue sections analysed for each experiment, as well as information on whether the sections were cryostat or vibratome.

This information is now provided in the figure legends (numbers of cells analysed and/or numbers of embryos), except for data in Figure 5, which are presented in a new Supplementary Table 1.

All experiments were performed on vibratome sections, except for in situ hybridization experiments, which were performed on cryostat sections. This last information was already indicated in the relevant figure legends

- Overall, there is a lack of consistency in the figures regarding how much information is available to the reader (e.g. Sup Figure 2A, in the panel mRNA in situ hybridisation of Cdkn1c is referred to only as Cdkn1c whereas in Sup figure 5 the in situ reads as CCND1 mRNA). Readability would improve a lot if figures included information on what is an electroporated fluorescent tag or an immunostaining (similar to the label in sup 4D) as well as the exact stage and hours after electroporation where relevant.

- There is a general lack of consistency in indicating the timing of the experiments, both in terms of embryonic stage/day and in terms of hours-post-electroporation.

We have now homogenized the nomenclature in the figures.

- "Primary antibodies used are: chick anti-GFP (GFP-1020 - 1:2000) from Aves Labs; goat antiSox2 (clone Y-17 - 1:1000) from Santa Cruz". There is no Sox2 immunostaining in the article.

In the original version of the manuscript, the anti-Sox2 antibody was not used; we have now added experiments using this antibody in the modified version of the manuscript; this sentence in the Methods thus remains unchanged.

Reviewer #3 (Significance (Required)):

__*Significance:

In neural development, there is a progressive switch in competence in neural progenitor cells, that transition from a proliferative (able to expand the neural progenitor pool) to neurogenic (able to produce neurons). Several factors are known to influence the transition of neural progenitor cells from a proliferative to a neurogenic state, including the activity of extracellular signalling pathways (e.g. SHH) (Saade et al. 2013, Tozer et al. 2017). In this study, the authors perform scRNA-seq of the cervical neural tube of chick at a stage of both proliferative and neurogenic progenitors are present, and identify transcriptional differences between the two populations. Among the differently expressed transcripts, they identify Cdkn1c (p57-Kip2) as enriched in neurogenic progenitors. Initially characterized as a driver of cell cycle exit in newborn neurons, the authors investigate the role of Cdkn1c in cycling progenitors. *__

The authors find that knock-down of Cdkn1c leads to an increase in proliferative divisions at the expense of neurogenic divisions. Conversely, misexpression of Cdkn1c in proliferative progenitors leads to a switch to neurogenic divisions. Furthermore, they find that knock-down of Cdkn1c shortens G1 phase of the cell cycle, suggesting a link between G1 length and neurogenic competence in neural progenitor cells. Cell cycle length has previously been linked to competence of neural progenitors, and it has been described that longer G1 duration is linked to neurogenic competence (e.g. Calegari F, Huttner WB. 2003).

The strengths of the study include:

The identification of a subset of genes enriched in neurogenic vs. proliferative progenitors. Since the transition from proliferative to neurogenic competence is a gradual process at the tissue level, the classification of proliferative vs. neurogenic progenitors based on a score of transcripts and the identification of a subset of transcripts that are enriched in neurogenic progenitors is a valuable contribution to the neurodevelopmental field.

- The somatic knock-in strategy used to induce low-level overexpression of Cdkn1c in proliferative progenitors is an elegant strategy to induce overexpression in a subset of cells in a controlled manner and is a valuable technical advance.

- The characterization of a specific role of Cdkn1c in regulating cell cycle length in cycling progenitors is novel and valuable knowledge contributing to our understanding of how regulation of cell cycle length impacts competence of neural progenitors.

The aspects to improve:

- The sc-RNAseq isolated genes enriched in neurogenic versus proliferative progenitors, providing valuable insight into the gradual transition from proliferative to neurogenic competence at the tissue level. However, this gene subset requires clearer representation and detailed characterization. Additionally, the full scRNA-seq dataset should be made publicly available to support further research in neurodevelopment.

The sequencing dataset has been deposited in NCBI's Gene Expression Omnibus database. It is currently under embargo, but will be made available upon acceptance and publication of the peer reviewed manuscript. Access is nonetheless available to the reviewers via a token that can be retrieved from the Review Commons website.

The following information will be added in the final manuscript.

Data availability

Single cell RNA sequencing data have been deposited in NCBI's Gene Expression Omnibus (GEO) repository under the accession number GSE273710, and are available at https://www.ncbi.nlm.nih.gov/geo/query/acc.cgi?acc=GSE273710."

- The characterization of Cdkn1c dynamics in cycling progenitors using endogenous tagging of the Cdkn1c transcript with a Myc tag is an elegant way to investigate the dynamics of Cdkn1c-myc along the cell cycle. However, it would be much more powerful if combined with a careful characterization of pRb immunostaining along the cell cycle in this tissue, as well as the quantifications and controls proposed. - Retinoblastoma protein (Rb) and cyclin D play a key role in regulating the G1/S transition, with cyclin D/CDK complexes phosphorylating Rb. Given that CDKN1c primarily inhibits the cyclin D/CDK6 complex, it likely affects pRb expression or phosphorylation. This suggests pRb may be a direct target of CDKN1c, making it an unreliable marker for tracking and quantifying neurogenic progenitors through CDKN1c modulation. In light of this, it would be more appropriate to consider pRb as a CDKN1c target and discuss the molecular mechanisms regulating cell cycle components. A more precise approach would involve using other markers or targets to quantify neural precursor division modes at earlier stages of neurogenesis.

- Many of the conclusions of the study are based on experiments performed using the FlashTag dye in order to perform clonal analysis of proliferative vs. neurogenic divisions. It would be very valuable to further characterize the reliability of this tool as well as to provide more information on the criteria used to determine the fate of the pairs of sister cells.

- The somatic knock-in strategy used to induce low-level overexpression of Cdkn1c in proliferative progenitors is an elegant strategy to induce overexpression in a subset of cells in a controlled manner. It would be valuable to further characterize the dynamics of Cdkn1c expression using this too and to provide proof that Pax7 expression is not altered in guides with the knock-in event.

- The presentation of the existing literature could be more up to date.

- The presentation of the data in the figures could be improved for readability. The sc-RNA seq data and the technical advances could be of interest for an audience of researchers using chick as a model organism, and working on neurodevelopment in general. Furthermore, the characterization of Cdkn1c as a regulator of G1 length in cycling progenitors and its implications for neurogenic competence could be of general interest for people working on basic research in the neurodevelopmental field.

Field of expertise of the reviewer: neural development, cell biology, embryology.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This study addresses the question of how task-relevant sensory information affects activity in the motor cortex. The authors use various approaches to address this question, looking at single units and population activity. They find that there are three subtypes of modulation by sensory information at the single unit level. Population analyses reveal that sensory information affects the neural activity orthogonally to motor output. The authors then compare both single unit and population activity to computational models to investigate how encoding of sensory information at the single unit level is coordinated in a network. They find that an RNN that displays similar orbital dynamics and sensory modulation to the motor cortex also contains nodes that are modulated similarly to the three subtypes identified by the single unit analysis.

Strengths:

The strengths of this study lie in the population analyses and the approach of comparing single-unit encoding to population dynamics. In particular, the analysis in Figure 3 is very elegant and informative about the effect of sensory information on motor cortical activity.

The task is also well designed to suit the questions being asked and well controlled.

We appreciate these kind comments.

It is commendable that the authors compare single units to population modulation. The addition of the RNN model and perturbations strengthen the conclusion that the subtypes of individual units all contribute to the population dynamics. However, the subtypes (PD shift, gain, and addition) are not sufficiently justified. The authors also do not address that single units exhibit mixed modulation, but RNN units are not treated as such.

We’re sorry that we didn’t provide sufficient grounds to introduce the subtypes. We have updated this in the revised manuscript, in Lines 102-104 as:

“We determined these modulations on the basis of the classical cosine tuning model (Georgopoulos et al., 1982) and several previous studies (Bremner and Andersen, 2012; Pesaran et al., 2010; Sergio et al., 2005).”

In our study, we applied the subtype analysis as a criterion to identify the modulation in neuron populations, rather than sorting neurons into exclusively different cell types.

Weaknesses:

The main weaknesses of the study lie in the categorization of the single units into PD shift, gain, and addition types. The single units exhibit clear mixed selectivity, as the authors highlight. Therefore, the subsequent analyses looking only at the individual classes in the RNN are a little limited. Another weakness of the paper is that the choice of windows for analyses is not properly justified and the dependence of the results on the time windows chosen for single-unit analyses is not assessed. This is particularly pertinent because tuning curves are known to rotate during movements (Sergio et al. 2005 Journal of Neurophysiology).

In our study, the mixed selectivity or specifically the target-motion modulation on reach- direction tuning is a significant feature of the single neurons. We categorized the neurons into three subclasses, not intending to claim their absolute cell types, but meaning to distinguish target-motion modulation patterns. To further characterize these three patterns, we also investigated their interaction by perturbing connection weights in RNN.

Yes, it’s important to consider the role of rotating tuning curves in neural dynamics during interception. In our case, we observed population neural state with sliding windows, and we focused on the period around movement onset (MO) due to the unexpected ring-like structure and the highest decoding accuracy of transferred decoders (Figure S7C). Then, the single-unit analyses were implemented.

This paper shows sensory information can affect motor cortical activity whilst not affecting motor output. However, it is not the first to do so and fails to cite other papers that have investigated sensory modulation of the motor cortex (Stavinksy et al. 2017 Neuron, Pruszynski et al. 2011 Nature, Omrani et al. 2016 eLife). These studies should be mentioned in the Introduction to capture better the context around the present study. It would also be beneficial to add a discussion of how the results compare to the findings from these other works.

Thanks for the reminder. We’ve introduced these relevant researches in the updated manuscript in Lines 422-426 as:

“To further clarify, the discussing target-motion effect is different from the sensory modulation in action selection (Cisek and Kalaska, 2005), motor planning (Pesaran et al., 2006), visual replay and somatosensory feedback (Pruszynski et al., 2011; Stavisky et al., 2017; Suway and Schwartz, 2019; Tkach et al., 2007), because it occurred around movement onset and in predictive control trial-by-trial.”

This study also uses insights from single-unit analysis to inform mechanistic models of these population dynamics, which is a powerful approach, but is dependent on the validity of the single-cell analysis, which I have expanded on below.

I have clarified some of the areas that would benefit from further analysis below:

(1) Task:

The task is well designed, although it would have benefited from perhaps one more target speed (for each direction). One monkey appears to have experienced one more target speed than the others (seen in Figure 3C). It would have been nice to have this data for all monkeys.

A great suggestion; however, it is hardly feasible as the Utah arrays have already been removed.

(2) Single unit analyses:

In some analyses, the effects of target speed look more driven by target movement direction (e.g. Figures 1D and E). To confirm target speed is the main modulator, it would be good to compare how much more variance is explained by models including speed rather than just direction. More target speeds may have been helpful here too.

A nice suggestion. The fitting goodness of the simple model (only movement direction) is much worse than the complex models (including target speed). We’ve updated the results in the revised manuscript in Lines 119-122, as “We found that the adjusted R2 of a full model (0.55 ± 0.24, mean ± sd.) can be higher than that of the PD shift (0.47 ± 0.24), gain (0.46 ± 0.22), additive (0.41 ± 0.26), and simple models (only reach direction, 0.34 ± 0.25) for three monkeys (1162 neurons, ranksum test, one-tailed, p<0.01, Figure S5).”

The choice of the three categories (PD shift, gain addition) is not completely justified in a satisfactory way. It would be nice to see whether these three main categories are confirmed by unsupervised methods.

A good point. It is a pity that we haven’t found an appropriate unsupervised method.

The decoder analyses in Figure 2 provide evidence that target speed modulation may change over the trial. Therefore, it is important to see how the window considered for the firing rate in Figure 1 (currently 100ms pre - 100ms post movement onset) affects the results.

Thanks for the suggestion and close reading. Because the movement onset (MO) is the key time point of this study, we colored this time period in Figure 1 to highlight the perimovement neuronal activity.

(3) Decoder:

One feature of the task is that the reach endpoints tile the entire perimeter of the target circle (Figure 1B). However, this feature is not exploited for much of the single-unit analyses. This is most notable in Figure 2, where the use of a SVM limits the decoding to discrete values (the endpoints are divided into 8 categories). Using continuous decoding of hand kinematics would be more appropriate for this task.

This is a very reasonable suggestion. In the revised manuscript, we’ve updated the continuous decoding results with support vector regression (SVR) in Figure S7A and in Lines 170-173 as:

“These results were stable on the data of the other two monkeys and the pseudopopulation of all three monkeys (Figure S6) and reconfirmed by the continuous decoding results with support vector regressions (Figure S7A), suggesting that target motion information existed in M1 throughout almost the entire trial.”

(4) RNN:

Mixed selectivity is not analysed in the RNN, which would help to compare the model to the real data where mixed selectivity is common. Furthermore, it would be informative to compare the neural data to the RNN activity using canonical correlation or Procrustes analyses. These would help validate the claim of similarity between RNN and neural dynamics, rather than allowing comparisons to be dominated by geometric similarities that may be features of the task. There is also an absence of alternate models to compare the perturbation model results to.

Thank you for these helpful suggestions. We have performed decoding analysis on RNN units and updated in Figure S12A and Lines 333-334 as: “First, from the decoding result, target motion information existed in nodes’ population dynamics shortly after TO (Figure S12A).”

We also have included the results of canonical correlation analysis and Procrustes analysis in Table S2 and Lines 340-342 as: “We then performed canonical component analysis (CCA) and Procrustes analysis (Table S2; see Methods), the results also indicated the similarity between network dynamics and neural dynamics.”

Reviewer #2 (Public Review):

Summary:

In this manuscript, Zhang et al. examine neural activity in the motor cortex as monkeys make reaches in a novel target interception task. Zhang et al. begin by examining the single neuron tuning properties across different moving target conditions, finding several classes of neurons: those that shift their preferred direction, those that change their modulation gain, and those that shift their baseline firing rates. The authors go on to find an interesting, tilted ring structure of the neural population activity, depending on the target speed, and find that (1) the reach direction has consistent positioning around the ring, and (2) the tilt of the ring is highly predictive of the target movement speed. The authors then model the neural activity with a single neuron representational model and a recurrent neural network model, concluding that this population structure requires a mixture of the three types of single neurons described at the beginning of the manuscript.

Strengths:

I find the task the authors present here to be novel and exciting. It slots nicely into an overall trend to break away from a simple reach-to-static-target task to better characterize the breadth of how the motor cortex generates movements. I also appreciate the movement from single neuron characterization to population activity exploration, which generally serves to anchor the results and make them concrete. Further, the orbital ring structure of population activity is fascinating, and the modeling work at the end serves as a useful baseline control to see how it might arise.

Thank you for your recognition of our work.

Weaknesses:

While I find the behavioral task presented here to be excitingly novel, I find the presented analyses and results to be far less interesting than they could be. Key to this, I think, is that the authors are examining this task and related neural activity primarily with a singleneuron representational lens. This would be fine as an initial analysis since the population activity is of course composed of individual neurons, but the field seems to have largely moved towards a more abstract "computation through dynamics" framework that has, in the last several years, provided much more understanding of motor control than the representational framework has. As the manuscript stands now, I'm not entirely sure what interpretation to take away from the representational conclusions the authors made (i.e. the fact that the orbital population geometry arises from a mixture of different tuning types). As such, by the end of the manuscript, I'm not sure I understand any better how the motor cortex or its neural geometry might be contributing to the execution of this novel task.

This paper shows the sensory modulation on motor tuning in single units and neural population during motor execution period. It’s a pity that the findings were constrained in certain time windows. We are still working on this task, please look forward to our following work.

Main Comments:

My main suggestions to the authors revolve around bringing in the computation through a dynamics framework to strengthen their population results. The authors cite the Vyas et al. review paper on the subject, so I believe they are aware of this framework. I have three suggestions for improving or adding to the population results:

(1) Examination of delay period activity: one of the most interesting aspects of the task was the fact that the monkey had a random-length delay period before he could move to intercept the target. Presumably, the monkey had to prepare to intercept at any time between 400 and 800 ms, which means that there may be some interesting preparatory activity dynamics during this period. For example, after 400ms, does the preparatory activity rotate with the target such that once the go cue happens, the correct interception can be executed? There is some analysis of the delay period population activity in the supplement, but it doesn't quite get at the question of how the interception movement is prepared. This is perhaps the most interesting question that can be asked with this experiment, and it's one that I think may be quite novel for the field--it is a shame that it isn't discussed.

It’s a great idea! We are on the way, and it seems promising.

(2) Supervised examination of population structure via potent and null spaces: simply examining the first three principal components revealed an orbital structure, with a seemingly conserved motor output space and a dimension orthogonal to it that relates to the visual input. However, the authors don't push this insight any further. One way to do that would be to find the "potent space" of motor cortical activity by regression to the arm movement and examine how the tilted rings look in that space (this is actually fairly easy to see in the reach direction components of the dPCA plot in the supplement--the rings will be highly aligned in this space). Presumably, then, the null space should contain information about the target movement. dPCA shows that there's not a single dimension that clearly delineates target speed, but the ring tilt is likely evident if the authors look at the highest variance neural dimension orthogonal to the potent space (the "null space")-this is akin to PC3 in the current figures, but it would be nice to see what comes out when you look in the data for it.

Thank you for this nice suggestion. While it was feasible to identify potent subspaces encoding reach direction and null spaces for target-velocity modulation, as suggested by the reviewer, the challenge remained that unsupervised methods were insufficient to isolate a pure target-velocity subspace from numerous possible candidates due to the small variance of target-velocity information. Although dPCA components can be used to construct orthogonal subspaces for individual task variables, we found that the targetvelocity information remained highly entangled with reach-direction representation. More details can be found in Figure S8C and its caption as below:

“We used dPCA components with different features to construct three subspaces (same data in A, reach-direction space #3, #4, #5; target-velocity space #10, #15, #17; interaction space #6, #11, #12), and we projected trial-averaged data into these orthogonal subspaces using different colormaps. This approach allowed us to obtain a “potent subspace” coding reach direction and a “null space” for target velocity. The results showed that the reach-direction subspace effectively represented the reach direction. However, while the target-velocity subspace encoded the target velocity information, it still contained reach-direction clusters within each target-velocity condition, corroborating the results of the addition model in the main text (Figure 4). The interaction subspace revealed that multiple reach-direction rings were nested within each other, similar to the findings from the gain model (Figure 3 & 4). The interaction subspace also captured more variance than target-velocity subspace, consistent with our PCA results, suggesting the target-velocity modulation primarily coexists with reach-direction coding. Furthermore, we explored alternative methods to verify whether orthogonal subspaces could effectively separate the reach direction and target velocity. We could easily identify the reach-direction subspace, but its orthogonal subspace was relatively large, and the target-velocity information exhibited only small variance, making it difficult to isolate a subspace that purely encodes target velocity.”

(3) RNN perturbations: as it's currently written, the RNN modeling has promise, but the perturbations performed don't provide me with much insight. I think this is because the authors are trying to use the RNN to interpret the single neuron tuning, but it's unclear to me what was learned from perturbing the connectivity between what seems to me almost arbitrary groups of neurons (especially considering that 43% of nodes were unclassifiable). It seems to me that a better perturbation might be to move the neural state before the movement onset to see how it changes the output. For example, the authors could move the neural state from one tilted ring to another to see if the virtual hand then reaches a completely different (yet predictable) target. Moreover, if the authors can more clearly characterize the preparatory movement, perhaps perturbations in the delay period would provide even more insight into how the interception might be prepared.

We are sorry that we did not clarify the definition of “none” type, which can be misleading. The 43% unclassifiable nodes include those inactive ones; when only activate (taskrelated) nodes included, the ratio of unclassifiable nodes would be much lower. We recomputed the ratios with only activated units and have updated Table 1. By perturbing the connectivity, we intended to explore the interaction between different modulations.

Thank you for the great advice. We considered moving neural states from one ring to another without changing the directional cluster. However, we found that this perturbation design might not be fully developed: since the top two PCs are highly correlated with movement direction, such a move—similar to exchanging two states within the same cluster but under different target-motion conditions—would presumably not affect the behavior.

Reviewer #3 (Public Review):

Summary:

This experimental study investigates the influence of sensory information on neural population activity in M1 during a delayed reaching task. In the experiment, monkeys are trained to perform a delayed interception reach task, in which the goal is to intercept a potentially moving target.

This paradigm allows the authors to investigate how, given a fixed reach endpoint (which is assumed to correspond to a fixed motor output), the sensory information regarding the target motion is encoded in neural activity.

At the level of single neurons, the authors found that target motion modulates the activity in three main ways: gain modulation (scaling of the neural activity depending on the target direction), shift (shift of the preferred direction of neurons tuned to reach direction), or addition (offset to the neural activity).

At the level of the neural population, target motion information was largely encoded along the 3rd PC of the neural activity, leading to a tilt of the manifold along which reach direction was encoded that was proportional to the target speed. The tilt of the neural manifold was found to be largely driven by the variation of activity of the population of gain-modulated neurons.

Finally, the authors studied the behaviour of an RNN trained to generate the correct hand velocity given the sensory input and reach direction. The RNN units were found to similarly exhibit mixed selectivity to the sensory information, and the geometry of the “ neural population” resembled that observed in the monkeys.

Strengths:

- The experiment is well set up to address the question of how sensory information that is directly relevant to the behaviour but does not lead to a direct change in behavioural output modulates motor cortical activity.

- The finding that sensory information modulates the neural activity in M1 during motor preparation and execution is non trivial, given that this modulation of the activity must occur in the nullspace of the movement.

- The paper gives a complete picture of the effect of the target motion on neural activity, by including analyses at the single neuron level as well as at the population level. Additionally, the authors link those two levels of representation by highlighting how gain modulation contributes to shaping the population representation.

Thank you for your recognition.

Weaknesses:

- One of the main premises of the paper is the fact that the motor output for a given reach point is preserved across different target motions. However, as the authors briefly mention in the conclusion, they did not record muscle activity during the task, but only hand velocity, making it impossible to directly verify how preserved muscle patterns were across movements. While the authors highlight that they did not see any difference in their results when resampling the data to control for similar hand velocities across conditions, this seems like an important potential caveat of the paper whose implications should be discussed further or highlighted earlier in the paper.

Thanks for the suggestion. We’ve highlighted the resampling results as an important control in the revised manuscript in Figure S11 and Lines 257-260 as:

“To eliminate hand-speed effect, we resampled trials to construct a new dataset with similar distributions of hand speed in each target-motion condition and found similar orbital neural geometry. Moreover, the target-motion gain model provided a better explanation compared to the hand-speed gain model (Figure S11).”

- The main takeaway of the RNN analysis is not fully clear. The authors find that an RNN trained given a sensory input representing a moving target displays modulation to target motion that resembles what is seen in real data. This is interesting, but the authors do not dissect why this representation arises, and how robust it is to various task design choices. For instance, it appears that the network should be able to solve the task using only the motion intention input, which contains the reach endpoint information. If the target motion input is not used for the task, it is not obvious why the RNN units would be modulated by this input (especially as this modulation must lie in the nullspace of the movement hand velocity if the velocity depends only on the reach endpoint). It would thus be important to see alternative models compared to true neural activity, in addition to the model currently included in the paper. Besides, for the model in the paper, it would therefore be interesting to study further how the details of the network setup (eg initial spectral radius of the connectivity, weight regularization, or using only the target position input) affect the modulation by the motion input, as well as the trained population geometry and the relative ratios of modulated cells after training.

Great suggestions. In the revised manuscript, we’ve added the results of three alternative modes in Table S4 and Lines 355-365 as below:

“We also tested three alternative network models: (1) only receives motor intention and a GO-signal; (2) only receives target location and a GO-signal; (3) initialized with sparse connection (sparsity=0.1); the unmentioned settings and training strategies were as the same as those for original models (Table S4; see Methods). The results showed that the three modulations could emerge in these models as well, but with obviously distinctive distributions. In (1), the ring-like structure became overlapped rings parallel to the PC1PC2 plane or barrel-like structure instead; in (2), the target-motion related tilting tendency of the neural states remained, but the projection of the neural states on the PC1-PC2 plane was distorted and the reach-direction clusters dispersed. These implies that both motor intention and target location seem to be needed for the proposed ring-like structure. The initialization of connection weights of the hidden layer can influence the network’s performance and neural state structure, even so, the ring-like structure”

- Additionally, it is unclear what insights are gained from the perturbations to the network connectivity the authors perform, as it is generally expected that modulating the connectivity will degrade task performance and the geometry of the responses. If the authors wish the make claims about the role of the subpopulations, it could be interesting to test whether similar connectivity patterns develop in networks that are not initialized with an all-to-all random connectivity or to use ablation experiments to investigate whether the presence of multiple types of modulations confers any sort of robustness to the network.

Thank you for these great suggestions. By perturbations, we intended to explore the contribution of interaction between certain subpopulations. We’ve included the ablation experiments in the updated manuscript in Table S3 and Lines 344-346 as below: “The ablation experiments showed that losing any kind of modulation nodes would largely deteriorate the performance, and those nodes merely with PD-shift modulation could mostly impact the neural state structure (Table S3).”

- The results suggest that the observed changes in motor cortical activity with target velocity result from M1 activity receiving an input that encodes the velocity information. This also appears to be the assumption in the RNN model. However, even though the input shown to the animal during preparation is indeed a continuously moving target, it appears that the only relevant quantity to the actual movement is the final endpoint of the reach. While this would have to be a function of the target velocity, one could imagine that the computation of where the monkeys should reach might be performed upstream of the motor cortex, in which case the actual target velocity would become irrelevant to the final motor output. This makes the results of the paper very interesting, but it would be nice if the authors could discuss further when one might expect to see modulation by sensory information that does not directly affect motor output in M1, and where those inputs may come from. It may also be interesting to discuss how the findings relate to previous work that has found behaviourally irrelevant information is being filtered out from M1 (for instance, Russo et al, Neuron 2020 found that in monkeys performing a cycling task, context can be decoded from SMA but not from M1, and Wang et al, Nature Communications 2019 found that perceptual information could not be decoded from PMd)?

How and where sensory information modulating M1 are very interesting and open questions. In the revised manuscript, we discuss these in Lines 435-446, as below: “It would be interesting to explore whether other motor areas also allow sensory modulation during flexible interception. The functional differences between M1 and other areas lead to uncertain speculations. Although M1 has pre-movement activity, it is more related to task variables and motor outputs. Recently, a cycling task sets a good example that the supplementary motor area (SMA) encodes context information and the entire movement (Russo et al., 2020), while M1 preferably relates to cycling velocity (Saxena et al., 2022). The dorsal premotor area (PMd) has been reported to capture potential action selection and task probability, while M1 not (Cisek and Kalaska, 2005; Glaser et al., 2018; Wang et al., 2019). If the neural dynamics of other frontal motor areas are revealed, we might be able to tell whether the orbital neural geometry of mixed selectivity is unique in M1, or it is just inherited from upstream areas like PMd. Either outcome would provide us some insights into understanding the interaction between M1 and other frontal motor areas in motor planning.”

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

At times the writing was a little hard to parse. It could benefit from being fleshed out a bit to link sentences together better.

There are a few grammatical errors, such as:

"These results support strong and similar roles of gain and additive nodes, but what is even more important is that the three modulations interact each other, so the PD-shift nodes should not be neglected."

should be

"These results support strong and similar roles of gain and additive nodes, but what is even more important is that the three modulations interact WITH each other, so the PDshift nodes should not be neglected."

The discussion could also be more extensive to benefit non-experts in the field.

Thank you. We have proofread and polished the updated manuscript.

Reviewer #2 (Recommendations For The Authors):

Other comments:

- The authors mention mixed selectivity a few times, but Table 1 doesn't have a column for mixed selective neurons--this seems like an important oversight. Likewise, it would be good to see an example of a "mixed" neuron.

- The structure of the writing in the results section often talked about the supplementary results before the main results - this seems backwards. If the supplementary results are important enough to come before the main figures, then they should not be supplementary. Otherwise, if the results are truly supplementary, they should come after the main results are discussed.

- Line 305: Authors say "most" RNN units could be classified, and this is technically true, but only barely, according to Table 1. It might be good to put the actual percentage here in the text.

- Figure 5a: typo ("Motion intention" rather than "Motor")

- I couldn't find any mention of code or data availability in the manuscript.

- There were a number of lines that didn't make much sense to me and should probably be rewritten or expanded on:

- Lines 167-168: "These results qualitatively imply the interaction as that target speeds..." - Lines 178-179: "However, these neural trajectories were not yet the ideal description, because they were shaped mostly by time."

- Lines 187-188: "...suggesting that target motion affects M1 neural dynamics via a topologically invariant transformation."

- Lines 224-226: "Note that here we performed an linear transformation on all resulting neural state points to make the ellipse of the static condition orthogonal to the z-axis for better visualization." Does this mean that the z-axis is not PC 3 anymore?

- Lines 272-274: "These simulations suggest that the existence of PD-shift and additive modulation would not disrupt the neural geometry that is primarily driven by gain modulation; rather it is possible that these three modulations support each other in a mixed population."

Thank you for these detailed suggestions. By “mixed selectivity”, we mean the joint tuning of both target-motion and movement. In this case, the target-motion modulated neurons (regardless of the modulation type) are of mixed selectivity. The term “motor intention” refers to Mazzoni et al., 1996, Journal of Neurophysiology. We also revised the manuscript for better readership.

We have updated the data and code availability in Data availability as below:

“The example experimental datasets and relevant analysis code have been deposited in Mendeley Data at https://data.mendeley.com/datasets/8gngr6tphf. The RNN relevant code and example model datasets are available at https://github.com/yunchenyc/RNN_ringlike_structure.“

Reviewer #3 (Recommendations For The Authors):

Minor typos:

Line 153: “there were”

Line 301: “network was trained to generate”

Line 318: “interact with each other”

Suggested reformulations :

Line 310 : “tilting angles followed a pattern similar to that seen in the data” Line 187 : the claim of a “topologically invariant transformation” seems strong as the analysis is quite qualitative.

Suggested changes to the paper (aside from those mentioned in the main review): It could be nice to show behaviour in a main figure panel early on in the paper. This could help with the task description (as it would directly show how the trials are separated based on endpoint) and could allow for discussing the potential caveats of the assumption that behaviour is preserved.

Thank you. We have corrected these typos and writing problems. As the similar task design has been reported, we finally decided not to provide extra figures or videos. Still, we thank this nice suggestion.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this manuscript by Thronlow Lamson et al., the authors develop a "beads-on-a-string" or BOAS strategy to link diverse hemagglutinin head domains, to elicit broadly protective antibody responses. The authors are able to generate varying formulations and lengths of the BOAS and immunization of mice shows induction of antibodies against a broad range of influenza subtypes. However, several major concerns are raised, including the stability of the BOAS, that only 3 mice were used for most immunization experiments, and that important controls and analyses related to how the BOAS alone, and not the inclusion of diverse heads, impacts humoral immunity.

Strengths:

Vaccine strategy is new and exciting.

Analyses were performed to support conclusions and improve paper quality.

Weaknesses:

Controls for how different hemagglutinin heads impact immunity versus the multivalency of the BOAS.

Only 3 mice were used for most experiments.

There were limited details on size exclusion data.

We appreciate the reviewer’s comments and have made the following changes to the manuscript.

(1) We recognize that deconvoluting the effect of including a diverse set of HA heads and multivalency in the BOAS immunogens is necessary to understand the impact on antigenicity. Therefore, we now include a cocktail of the identical eight HA heads used in the 8-mer and BOAS nanoparticle (NP) as an additional control group. While we observed similar HA binding titers relative to the 8-mer and BOAS NP groups, the cocktail group-elicited sera was unable to neutralize any of the viruses tested; multivalency thus appears to be important for eliciting neutralizing responses

(2) We increased the sample size by repeated immunizations with n=5 mice, for a total of n=8 mice across two independent experiments.

(3) We expanded the details on size exclusion data to include:

a) extended chromatograms from Figure 2C as Supplemental Figure 3.

b) additional details in the materials and methods section (lines 370-372):

“Recovered proteins were then purified on a Superdex 200 (S200) Increase 10/300 GL (for trimeric HAs) or Superose 6 Increase 10/300 GL (for BOAS) size-exclusion column in Dulbecco’s Phosphate Buffered Saline (DPBS) within 48 hours of cobalt resin elution.”

Reviewer #2 (Public Review):

Summary:

The authors describe a "beads-on-a-string" (BOAS) immunogen, where they link, using a non-flexible glycine linker, up to eight distinct hemagglutinin (HA) head domains from circulating and non-circulating influenzas and assess their immunogenicity. They also display some of their immunogens on ferritin NP and compare the immunogenicity. They conclude that this new platform can be useful to elicit robust immune responses to multiple influenza subtypes using one immunogen and that it can also be used for other viral proteins.

Strengths:

The paper is clearly written. While the use of flexible linkers has been used many times, this particular approach (linking different HA subtypes in the same construct resembling adding beads on a string, as the authors describe their display platform) is novel and could be of interest.

Weaknesses:

The authors did not compare to individuals HA ionized as cocktails and did not compare to other mosaic NP published earlier. It is thus difficult to assess how their BOAS compare.<br /> Other weaknesses include the rationale as to why these subtypes were chosen and also an explanation of why there are different sizes of the HA1 construct (apart from expression). Have the authors tried other lengths? Have they expressed all of them as FL HA1?

We appreciate the reviewer’s comments. We responded to the concerns below and modified the manuscript accordingly.

(1) We recognize that including a “cocktail” control is important to understand how the multivalency present in a single immunogen affects the immune response. We now include an additional control group comprised of a mixture of the same eight HA heads used in the 8-mer and the BOAS nanoparticle (NP). While this cocktail elicited similar HA binding titers relative to the 8-mer and BOAS NP immunogens (Fig. 6G), there was no detectable neutralization any of the viruses tested (Fig. 7).

(2) In the introduction we reference other multivalent display platforms but acknowledge that distinct differences in their immunogen design platforms make direct comparisons to ours difficult—which is ultimately why we did not use them as comparators for our in vivo studies. Perhaps most directly relevant to our BOAS platform is the mosaic HA NP from Kanekiyo et al. (PMID 30742080). Here, HA heads, with similar boundaries to ours, were selected from historical H1N1 strains. These NPs however were significantly less antigenic diverse relative to our BOAS NPs as they did not include any group 2 (e.g., H7, H9) or B influenza HAs; restricting their multivalent display to group 1 H1N1s likely was an important factor in how they were able to achieve broad, neutralizing H1N1 responses. Additionally, Cohen et al. (PMID 33661993) used similarly antigenically distinct HAs in their mosaic NP, though these included full-length HAs with the conserved stem region, which likely has a significant impact on the elicited cross-reactive responses observed. Lastly, we reference Hills et al. (PMID 38710880), where authors designed similar NPs with four tandemly-linked betacoronoavirus receptor binding domains (RBDs) to make “quartets”. In contrast to our observations, the authors observed increased binding and neutralization titers following conjugation to protein-based NPs. We acknowledge potential differences between the studies, such as the antigen and larger VLP NP, that could lead to the different observed outcomes.

(3) We intended to highlight the “plug-and-play” nature of the BOAS platform; theoretically any HA subtype could be interchanged into the BOAS. To that end, our rationale for selecting the HA subtypes in our proof-of-principle immunogen was to include an antigenically diverse set of circulating and non-circulating HAs that we could ultimately characterize with previously published subtype-specific antibodies that were also conformation-specific. In doing so, these diagnostic antibodies could confirm presence and conformation integrity of each component. We intentionally did not include HA subtypes that we did not have a conformation-specific antibody for.

The different sizes of HA head domains was determined exclusively by expression of the recombinant protein. We have not attempted expression of full-length HA1 domains. Furthermore, we have not attempted to express the full-length HA (inclusive of HA1 and HA2) in our BOAS platform. The primary reason was to avoid including the conserved stem region of HA2 which may distract from the HA1 epitopes (e.g., receptor binding site, lateral patch) that can be engaged by broadly neutralizing antibodies. Additionally, the full-length HA is inherently trimeric and may not be as amenable to our BOAS platform as the monomeric HA1 head domain.

Reviewer #3 (Public Review):

This work describes the tandem linkage of influenza hemagglutinin (HA) receptor binding domains of diverse subtypes to create 'beads on a string' (BOAS) immunogens. They show that these immunogens elicit ELISA binding titers against full-length HA trimers in mice, as well as varying degrees of vaccine mismatched responses and neutralization titers. They also compare these to BOAS conjugated on ferritin nanoparticles and find that this did not largely improve immune responses. This work offers a new type of vaccine platform for influenza vaccines, and this could be useful for further studies on the effects of conformation and immunodominance on the resulting immune response.

Overall, the central claims of immunogenicity in a murine model of the BOAS immunogens described here are supported by the data.

Strengths included the adaptability of the approach to include several, diverse subtypes of HAs. The determination of the optimal composition of strains in the 5-BOAS that overall yielded the best immune responses was an interesting finding and one that could also be adapted to other vaccine platforms. Lastly, as the authors discuss, the ease of translation to an mRNA vaccine is indeed a strength of this platform.

One interesting and counter-intuitive result is the high levels of neutralization titers seen in vaccine-mismatched, group 2 H7 in the 5-BOAS group that differs from the 4-BOAS with the addition of a group 1 H5 RBD. At the same time, no H5 neutralization titers were observed for any of the BOAS immunogens, yet they were seen for the BOAS-NP. Uncovering where these immune responses are being directed and why these discrepancies are being observed would constitute informative future work.

There are a few caveats in the data that should be noted:

(1) 20 ug is a pretty high dose for a mouse and the majority of the serology presented is after 3 doses at 20 ug. By comparison, 0.5-5 ug is a more typical range (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC6380945/, https://www.ncbi.nlm.nih.gov/pmc/articles/PMC9980174/). Also, the authors state that 20 ug per immunogen was used, including for the BOAS-NP group, which would mean that the BOAS-NP group was given a lower gram dose of HA RBD relative to the BOAS groups.

We agree that this is on the “upper end” of recombinant protein dose. While we did not do a dose-response, we now include serum analyses after a single prime. The overall trends and reactivity to matched and mis-matched BOAS components remained similar across days d28 and d42. However, the differences between the BOAS and BOAS NP groups and the mixture group were more pronounced at d28, which reinforces our observation that the multivalency of the HA heads is necessary for eliciting robust serum responses to each component. These data are included in Supplemental Figure 5, and we’ve modified the text (lines 185-187) to include;

“Similar binding trends were also observed with d28 serum, though the difference between the 8mer and mix groups was more pronounced at d28 (Supplemental Figure 5).”

Additionally, we acknowledge that there is a size discrepancy between the BOAS NP and the largest BOAS, leading to an approximately ~15-fold difference on a per mole basis of the BOAS immunogen. The smallest and largest BOAS also differ by ~ 2.5-fold on a per mole basis; this could favor the overall amount of the smaller immunogens, however because vaccine doses are typically calculated on a mg per kg basis, we did not calculate on a molar basis for this study. Any promising immunogens will be evaluated in dose-response study to optimize elicited responses.

(2) Serum was pooled from all animals per group for neutralization assays, instead of testing individual animals. This could mean that a single animal with higher immune responses than the rest in the group could dominate the signal and potentially skew the interpretation of this data.

We repeated the neutralization assays with data points for individual mice. There does appear to be variability in the immune response between mice. This is most noticeable for responses to the H5 component. We are currently assessing what properties of our BOAS immunogen might contribute to the variability across individual mice.

(3) In Figure S2, it looks like an apparent increase in MW by changing the order of strains here, which may be due to differences in glycosylation. Further analysis would be needed to determine if there are discrepancies in glycosylation amongst the BOAS immunogens and how those differ from native HAs.

There does appear to be a relatively small difference in MW between the two BOAS configurations shown in Figure S2. This could be due to differences in glycosylation, as the reviewer points out, and in future studies, we intend to assess the influence of native glycosylation on antibody responses elicited by our BOAS immunogens.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Major Concerns

(1) From Figure 2D-E, it looks like BOAS are forming clusters, rather than a straight line. Do these form aggregates over time? Both at 4 degrees over a few days or after freeze-thaw cycle(s)? It is unclear from the SEC methods how long after purification this was performed and stability should be considered.

Due to the inherent flexibility of the Gly-Ser linker between each component we do not anticipate that any rigidity would be imposed resulting in a “straight line”. Nevertheless, we appreciate the reviewers concern about the long-term stability of the BOAS immunogens. To address this, we include 1) the extended chromatograms from Figure 2C as Supplemental Figure 3 to show any aggregates present, 2) traces from up to 48 hours post-IMAC, and 3) chromatograms following a freeze-thaw cycle. Post-IMAC purification there is a minor (<10% total peak height) at ~9mL corresponding to aggregation. Note, we excluded this aggregation for immunizations. Post freeze-thaw cycle, we can see that upon immediate (<24hrs) thawing, the BOAS maintain a homogeneous peak with no significant (<10%) aggregation or degradation peak. However, after ~1 week post-freeze-thaw cycle at 4C, additional peaks within the chromatogram correspond to degradation of the BOAS.

We modified the materials and methods section to state (lines 370-372)

“Recovered proteins were then purified on a Superdex 200 (S200) Increase 10/300 GL (for trimeric HAs) or Superose 6 Increase 10/300 GL (for BOAS) size-exclusion column in Dulbecco’s Phosphate Buffered Saline (DPBS) within 48 hours of cobalt resin elution.”

We commented on BOAS stability in the results section (lines 142-148)

“Following SEC, affinity tags were removed with HRV-3C protease; cleaved tags, uncleaved BOAS, and His-tagged enzyme were removed using cobalt affinity resin and snap frozen in liquid nitrogen before immunizations. BOAS maintained monodispersity upon thawing, though over time, degradation was observed following longer term (>1 week) storage at 4C (Supplemental Figure 3). This degradation became more significant as BOAS increased in length (Supplemental Figure 3).”

We also included in the discussion (lines 277-279):

“Notably, for longer BOAS we observed degradation following longer term storage at 4C, which may reflect their overall stability.”

(2) Figures 3-4 and 6-7, to make conclusions off of 3 mice per group is inappropriate. A sample size calculation should have been conducted and the appropriate number of mice tested. In addition, two independent mouse experiments should always be performed. Moreover, the reliability of the statistical tests performed seems unlikely, given the very small sample size.

We agree that additional mice are necessary to make assessments regarding immunogenicity and cross-reactivity differences between the immunogens. To address this, we repeated the immunization with 5 additional mice, for a total of n=8 mice over two independent experiments. We incorporated these data into Figure 3B-D, as well as an additional Figure 3E (see below). We also now report the log-transformed endpoint titer (EPT) values rather than reciprocal EC50 values and added clarity to statistical analyses used. We have added the following lines to the methods section

lines 427-431:

“Serum endpoint titer (EPT) were determined using a non-linear regression (sigmoidal, four-parameter logistic (4PL) equation, where x is concentration) to determine the dilution at which dilution the blank-subtracted 450nm absorbance value intersect a 0.1 threshold. Serum titers for individual mice against respective antigens are reported as log transformed values of the EPT dilution.”

lines 406-408:

“C57BL/6 mice (Jackson Laboratory) (n=8 per group for 3-, 4-, 5-, 6-, 7-, and 8mer cohorts; n=5 for BOAS NP, NP, and mix cohorts) were immunized with 20µg of BOAS immunogens of varying length and adjuvanted with 50% Sigmas Adjuvant for a total of 100µL of inoculum.”

lines 482-490:

“Statistical Analysis

Significance for ELISAs and microneutralization assays were determined using Prism (GraphPad Prism v10.2.3). ELISAs comparing serum reactivity and microneutralization and comparing >2 samples were analyzed using a Kruskal-Wallis test with Dunn’s post-hoc test to correct for multiple comparisons. Multiple comparisons were made between each possible combination or relative to a control group, where indicated. ELISAs comparing two samples were analyzed using a Mann-Whitney test. Significance was assigned with the following: * = p<0.05, ** = p<0.01, *** = p<0.001, and **** = p<0.0001. Where conditions are compared and no significance is reported, the difference was non-significant.”

(3) One critical control that is missing is a homogenous BOAS, for example, just linking one H1 on a BOAS. Does oligomerization and increasing avidity alone improve humoral immunity?

We agree that this is an interesting point, However, to address the impact of oligomerization and avidity on humoral immunity, we now include an additional control with a cocktail of HA heads used in the 8mer. We have incorporated this into Figure 3A, 3D and 3E, Figure 6G, and Figure 7.

Additionally, we have added the following lines in the manuscript:

lines 38-40:

“Finally, vaccination with a mixture of the same HA head domains is not sufficient to elicit the same neutralization profile as the BOAS immunogens or nanoparticles.”

lines 105-106:

“Additionally, we showed that a mixture of the same HA head components was not sufficient to recapitulate the neutralizing responses elicited by the BOAS or BOAS NP.”

lines 169-172:

“To determine immunogenicity of each BOAS immunogen, we performed a prime-boost-boost vaccination regimen in C5BL/6 mice at two-week intervals with 20µg of immunogen and adjuvanted with Sigma Adjuvant (Figure 3A). We compared these BOAS to a control group immunized with a mixture of the eight HA heads present in the 8mer.”

lines 265-267:

“There were qualitatively immunodominant HAs, notably H4 and H9, and these were relatively consistent across BOAS in which they were a component. This effect was reduced in the mix cohort.”

(4) While some cross-reactivity is likely (Figure 6G), there is considerable loss of binding when there is a mismatch. Of the antibodies induced, how much of this is strain-specific? For example, how well do serum antibodies bind to a pre-2009 H1?

We agree with the reviewer that there is a considerable loss of binding when there is a mismatched HA component. To better understand this and incorporate a mismatched strain into our analysis of the 8mer and BOAS NP, we looked at serum binding titers to a pre-2009 H1, H1/Solomon Islands/2006, and an antigenically distinct H3, H3/Hong Kong/1968. We have incorporated this data into Figures 3D, 3E, 6F and 6G. We observed relatively high titers against both a mismatched H1 and H3, indicating that the BOAS maintain high titers against subtype-specific strains that are conserved over considerable antigenic distance. However, this was similar in the mixture group, indicating that this may not be specific to oligomerization of BOAS immunogens.

We added the following to the methods section:

lines 357-361

“Head subdomains from these HAs were used in the BOAS immunogens, and full-length soluble ectodomain (FLsE) trimers were used in ELISAs. Additional H1 (H1/A/Solomon Islands/3/2006) and H3 (H3/A/Hong Kong/1/1968) FLsEs were used in ELISAs as mismatched, antigenically distinct HAs for all BOAS.”

Minor Concerns

(1) Line 44-46, the deaths per year are almost exclusively due to seasonal influenza outbreaks caused by antigenically drifted viruses in humans, not those spilling over from avian sp. and swine. For accuracy, please adjust this sentence.

We have adjusted lines 45-48 to say “This is largely a consequence of viral evolution and antigenic drift as it circulates seasonally within humans and ultimately impacts vaccine effectiveness. Additionally, the chance for spillover events from animal reservoirs (e.g., avian, swine) is increasing as population and connectivity also increase.”

(2) Figure 4D-E, provide a legend for what the symbols indicate, or simply just put the symbol next to either the homology score and % serum competition labels on the y-axis.

We have included a legend in Figures 4D,E to distinguish between homology score and % serum competition

(3) I am a bit confused by the data presented in Figure 7. The figure legend says the two symbols represent technical replicates. How? Is one technical replicate of all the mice in a group averaged and that's what's graphed? If so, this is not standard practice. I would encourage the authors to show the average technical replicates of each animal, which is standard.

We thank the reviewer for their suggestion, and we have revised Figure 7 such that each symbol represents a single animal for n=5 animals. We have also adjusted the figure caption to the following:

“Figure 7: Microneutralization titers to matched and mis-matched virus- Microneutralization of matched and mis-matched psuedoviruses: H1N1 (green, top left), H3N2 (orange, top right), H5N1 (yellow, bottom left), and H7N9 viruses (pink, bottom right) with d42 serum. Solid bars below each plot indicate a matched sub-type, and striped bars indicate a mis-matched subtype (i.e. not present in the BOAS). NP negative controls were used to determine threshold for neutralization. Upper and lower dashed lines represent the first dilution (1:32) (for H1N1, H3N2, and H5N1) or neutralization average with negative control NP serum (H7N9), and the last serum dilution (1:32,768), respectively, and points at the dashed lines indicate IC50s at or outside the limit of detection. Individual points indicate IC50 values from individual mice from each cohort (n=5). The mean is denoted by a bar and error bars are +/- 1 s.d., * = p<0.05 as determined by a Kruskal-Wallis test with Dunn’s multiple comparison post hoc test relative to the mix group.”

(4) Paragraphs 298-313, multiple studies are referred to but not referenced.

We have added the following references to this section:

(38) Kanekiyo, M. et al. Self-assembling influenza nanoparticle vaccines elicit broadly neutralizing H1N1 antibodies. Nature 498, 102–106 (2013).

(48) Hills, R. A. et al. Proactive vaccination using multiviral Quartet Nanocages to elicit broad anti-coronavirus responses. Nat. Nanotechnol. 1–8 (2024) doi:10.1038/s41565-024-01655-9.

(65) Jardine, J. et al. Rational HIV immunogen design to target specific germline B cell receptors. Science 340, 711–716 (2013).

(66) Tokatlian, T. et al. Innate immune recognition of glycans targets HIV nanoparticle immunogens to germinal centers. Science 363, 649–654 (2019).

(67) Kato, Y. et al. Multifaceted Effects of Antigen Valency on B Cell Response Composition and Differentiation In Vivo. Immunity 53, 548-563.e8 (2020).

(68) Marcandalli, J. et al. Induction of Potent Neutralizing Antibody Responses by a Designed Protein Nanoparticle Vaccine for Respiratory Syncytial Virus. Cell 176, 1420-1431.e17 (2019).

(69) Bruun, T. U. J., Andersson, A.-M. C., Draper, S. J. & Howarth, M. Engineering a Rugged Nanoscaffold To Enhance Plug-and-Display Vaccination. ACS Nano 12, 8855–8866 (2018).

(70) Kraft, J. C. et al. Antigen- and scaffold-specific antibody responses to protein nanoparticle immunogens. Cell Reports Medicine 100780 (2022) doi:10.1016/j.xcrm.2022.100780.

Reviewer #2 (Recommendations For The Authors):

Can the authors define "detectable titers"?

Maybe add a threshold value of reciprocal EC on the figure for each plot.

We recognize the reviewers concern with reporting serum titers in this way, and we have adjusted our reported titers as endpoint titers (EPT) with a dotted line for the first detectable dilution (1:50). We have also adjusted the methods section to reflect this change:

(lines 427-431)

“Serum endpoint titer (EPT) were determined using a non-linear regression (sigmoidal, four-parameter logistic (4PL) equation, where x is concentration) to determine the dilution at which dilution the blank-subtracted 450nm absorbance value intersect a 0.1 threshold. Serum titers for individual mice against respective antigens are reported as log transformed values of the EPT dilution.”

It also appears that not all X-mer elicits an immune response against matched HA, e.g. for the 7 and 8 -mer. Not sure why the authors do not mention this. It could be due to too many HAs, not sure.

We apologize for the confusion, and agree that our original method of reporting EC50 values does not reflect weak but present binding titers. Upon further analysis with additional mice as well as adjusting our method of reporting titers, it is easier to see in Figure 3D that all X-mer BOAS do indeed elicit binding detectable titers to matched HA components.

It will be nice to add a conclusion to the cross-reactivity - again it appears that past 6-mer there has been a loss in cross-reactivity even though there are more subtypes on the BOAS.

Also, the TI seemed to be the more conserved epitope targeted here.

(Of note these two are mentioned in the discussion)

We have updated the results section to include the following:

(lines 281-294)

“Based on the immunogenicity of the various BOAS and their ability to elicit neutralizing responses, it may not be necessary to maximize the number of HA heads into a single immunogen. Indeed, it qualitatively appears that the intermediate 4-, 5-, and 6mer BOAS were the most immunogenic and this length may be sufficient to effectively engage and crosslink BCR for potent stimulation. These BOAS also had similar or improved binding cross-reactivity to mis-matched HAs as compared to longer 7- or 8mer BOAS. Notably, the 3mer BOAS elicited detectable cross-reactive binding titers to H4 and H5 mismatched HAs in all mice. This observed cross-reactivity could be due to sequence conservation between the HAs, as H3 and H4 share ~51% sequence identity, and H1 and H2 share ~46% and ~62% overall sequence identity with H5, respectively (Supplemental Figure 6). Additionally, the degree of surface conservation decreased considerably beyond the 5mer as more antigenically distinct HAs were added to the BOAS. These data suggest that both antigenic distance between HA components and BOAS length play a key role in eliciting cross-reactive antibody responses, and further studies are necessary to optimize BOAS valency and antigenic distance for a desired response.”

Figure 5E, the authors could indicate which subtype each mab is specific to for those who are not HA experts. (They have them color-coded but it is hard to see because very small).

The authors also do not explain why 3E5 does not bind well to H1, H2, H3, H4 4-mer BOA, etc...

We apologize for the lack of clarity in this figure. We updated Figure 5E to include the subtype it is specific for as well as listing the antibodies and their subtype and targeted epitope in the figure caption.

Minor

Figure 1B zoom looks like the line is hidden to the structure - should come in front

We adjusted the figure accordingly.

Line 127 - whether the order

Corrected

What is the rationale for thinking that a different order will lead to a different expression and antigenic results?

We thank the reviewer for this question. We did not necessarily anticipate a difference in protein expression based on BOAS order We, however, wanted to verify that our platform was indeed “plug-and-play” platform and we could readily exchange components and order. We do, however, hypothesize that a different order may in fact lead to different antigenic results. We think that the conformation of the BOAS as well as physical and antigenic distance of HA components may influence cross-linking efficiency of BCRs and lead to different antigenic results with different levels of cross-reactivity. For example, a BOAS design with a cluster of group 1 HAs followed by a cluster of group 2 HAs, rather than our roughly alternating pattern could impact which HAs are in proximity to each other or could be potentially shielded in certain conformations, and thus could affect antigenic results. We expand on this rationale in the discussion in lines 310-314:

“Further studies with different combinations of HAs could aid in understanding how length and composition influences epitope focusing. For example, a BOAS design with a cluster of group 1 HAs followed by a cluster of group 2 HAs, rather than our roughly alternating pattern could impact which HAs are in close proximity to one other or could be potentially shielded in certain conformations, and thus could affect antigenic results.”

Maybe list HA#1 HA#2 HA#3 instead of HA1, HA2, HA3 to make sure it is not confounded with HA2 and HA2

We agree that this may be confusing for readers, and have adjusted Figure 1C to show HA#1, HA#2, etc.

For nsEM, do the authors have 2D classes and even 3D reconstructions? Line 148-149: maybe or just because there are more HAs.

We did not obtain 2D class or 3D reconstructions of these BOAS. However, we do agree with the reviewer that the collapsed/rosette structure of the 8mer BOAS may be a consequence of the additional HA heads as well as the flexible Gly-Ser linkers between the components. We have added clarify to our statement in the discussion to read:

lines 154-156:

“This is likely a consequence of the flexible GSS linker separating the individual HA head components as well as the addition of significantly more HA head components to the construct.”.

Line 153 " interface-directed" - what does this mean?

We apologize for any confusion- we intend for “interface-directed” to refer antibodies that engage the trimer interface (TI) epitope between HA protomers. We have adjusted the manuscript to use the same terminology throughout, i.e. trimer interface or its abbreviation, TI.

For Figure 2 F - do you have a negative control? Usually one does not determine an ELISA KD, it is not very accurate but shows binding in terms of OD value.

We did include a negative control, MEDI8852, a stem-directed antibody, though it was not shown in the figure because we observed no binding, as expected. This negative control antibody was also used in Figure 5E for characterizing the BOAS NPs, and also shows no binding. We recognize that in an ELISA the KD is an equilibrium measurement and we do not report kinetic measurements as determined by a method such as bio-layer interferometry (BLI), and have this adjusted the figure caption to denote the values as “apparent K_D values”.

Line 169 - reads strangely, "BOAS-elicited serum, regardless of its length, reacted<br /> The length is the one of the Immunogen, not the serum

We agree that this statement is unclear, and we have modified the sentence to read:

lines 177-178:

“Each of the BOAS, regardless of its length, elicited binding titers to all matched full-length HAs representing individual components (Figure 3D).”

What is the adjuvant used (add in results)?

We used Sigma adjuvant for all immunizations, and have included this information in the results section:

lines 169-171:

“To determine immunogenicity of each BOAS, we performed a prime-boost-boost vaccination regimen in C5BL/6 mice at two-week intervals with 20µg of immunogen and adjuvanted with Sigma Adjuvant (Figure 3A).”

This information is also included in the methods section in lines 406-412.

Line 178 - remove " across"

We have removed the word “across” in this sentence and replaced it with “on” (line 194)

Trimer- interface, and interface epitopes are used exchangeably - maybe keep it as trimer interface to be more precise

As stated above, we have adjusted the manuscript to use the same term throughout, i.e., trimer interface or its abbreviation, TI.

Line 221 - no figure 6H (6G?)

We apologize for this typo and have corrected to Figure 6G (line 231)

Reviewer #3 (Recommendations For The Authors):

(1) Since 20 ug x3 doses is quite a high amount of vaccine, differences between immunogens may become blurred. Thus, it may be informative to compare post-prime serology for all immunogens or select immunogens to compare to the post-3rd dose data.

We agree with the reviewer that this is on the upper end of vaccine dose and thus we explored the serum responses after a single boost. The overall trends and reactivity to matched and mis-matched BOAS components remained similar across days d28 and d42. However, the differences between the BOAS and BOAS NP groups and the mixture group were more pronounced at d28, which bolsters our claim that the presentation of the HA heads is important for eliciting strong serum responses to all components. We have included this data in Supplemental Figure 5, and have acknowledged this in the text:

lines 185-187:

“Similar binding trends were also observed with d28 serum, though the difference between the 8mer and mix groups was more pronounced at d28 (Supplemental Figure 5).”

(2) Significance statistics for all immunogenicity data should be added and discussed; it is particularly absent in Figures 3D and 7.

We have added statistical analyses to Figure 3 and Figure 7 to reflect changes in immunogenicity. We have also added the following to the methods section:

lines 482-490:

“Statistical Analysis

Significance for ELISAs and microneutralization assays were determined using either a Mann-Whitney test or a Kruskal-Wallis test with Dunn’s post-hoc test in Prism (GraphPad Prism v10.2.3) to correct for multiple comparisons. Multiple comparisons were made between each possible combination or relative to a control group, where indicated. Significance was assigned with the following: * = p<0.05, ** = p<0.01, *** = p<0.001, and **** = p<0.0001. Where conditions are compared and no significance is reported, the difference was non-significant.”

(3) Figure 2F: the figure has K03.12 listed for the H3-specific mAb and in the main text, but the caption says 3E5 - is the 3E5 in the caption a typo? 3E5 is listed for the competition ELISAs as an RBS mAb, but its binding site is distal to the RBS at residues 165-170 (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC9787348/), H7.167 binds in the RBS periphery and not directly within the RBS, and the epitope for P2-D9 is undetermined/not presented. This could mean that there is actually a higher proportion of RBS-directed antibodies than what is determined from this serum competition data. Also, reference to these as 'RBS-directed' in the serum competition methods section should be revised for accuracy.

We sincerely apologize for this error and the resulting confusion. 3E5 in the caption is incorrect and should be K03.12 (https://www.rcsb.org/structure/5W08) and does engage the receptor binding site. We also apologize for the oversight that H7.167 is in the RBS periphery and not directly in the RBS. The additional P2-D9 in the panel of RBS-directed antibodies was also in error, as we do not believe it is RBS-directed, but is indeed H4 specific. We also included a reference to the paper and immunogen that elicited this antibody. We agree that this indicates that there could be a higher proportion of RBS-directed antibodies in the serum and have modified the text in the results and methods sections to read:

lines 300-306:

“Notably, this proportion is approximate, as at the time of reporting, antibodies that bind the receptor binding site of all components were not available. RBS-directed antibodies to the H4 and H9 component were not available, and the RBS-directed antibodies used targeting the other HA components have different footprints around the periphery of the RBS. Additionally, there are currently no reported influenza B TI-directed antibodies in the literature. Therefore, this may be an underestimate of the serum proportion focused to the conserved RBS and TI epitopes.”

lines 435-439:

“Following blocking with BSA in PBS-T, blocking solution was discarded and 40µL of either DPBS (no competition control), a cocktail of humanized antibodies targeting the RBS and periphery (5J8, 2G1, K03.12, H5.3, H7.167, H1209), a cocktail of humanized TI-directed antibodies (S5V2-29, D1 H1-17/H3-14, D2 H1-1/H3-1), or a negative control antibody (MEDI8852) were added at a concentration of 100µg/mL per antibody.”

(4) Only nsEM data is shown for the 3-BOAS and 8-BOAS, where differences in morphology were seen between these longer and shorter proteins. Including nsEM images for all BOAS immunogens may show trends in morphology or organization that could correlate with immune responses, e.g. if the 5-BOAS also forms a higher proportion of rosette-like structures, while the the 4-BOAS is still a mix between extended and rosette-like, this could be a factor in the better immune responses seen for 5-BOAS.

We appreciate the reviewer’s suggestion for further analysis of morphology between the intermediate BOAS sizes. We agree that the relationship between BOAS length and morphology should be explored more in depth, and we intend to do so in future studies and to also vary linker length and rigidity.

Welcome back and in this fundamentals video I want to briefly talk about Kubernetes which is an open source container orchestration system, and you use it to automate the deployment, scaling and management of containerized applications. At a super high level, Kubernetes lets you run containers in a reliable and scalable way, making efficient use of resources and lets you expose your containerized applications to the outside world or your business. It's like Docker, only with robots to automate it and super intelligence for all of the thinking. Now Kubernetes is a cloud agnostic product so you can use it on-premises and within many public cloud platforms. Now I want to keep this video to a super high level architectural overview but that's still a lot to cover, so let's jump in and get started.

Let's quickly step through the architecture of a Kubernetes cluster. A cluster in Kubernetes is a highly available cluster of compute resources and these are organized to work as one unit. The cluster starts with the cluster control plane which is the part which manages the cluster; it performs scheduling, application management, scaling and deployment and much more. Compute within a Kubernetes cluster is provided via nodes and these are virtual or physical servers which function as a worker within the cluster; these are the things which actually run your containerized applications. Running on each of the nodes is software and at minimum this is container D or another container runtime which is the software used to handle your container operations, and next we have KubeLit which is an agent to interact with the cluster control plane. KubeLit running on each of the nodes communicates with the cluster control plane using the Kubernetes API. Now this is the top level functionality of a Kubernetes cluster — the control plane orchestrates containerized applications which run on nodes.

But now let's explore the architecture of control planes and nodes in a little bit more detail. On this diagram I've zoomed in a little — we have the control plane at the top and a single cluster node at the bottom, complete with the minimum Docker and KubeLit software running for control plane communications. Now I want to step through the main components which might run within the control plane and on the cluster nodes — keep in mind this is a fundamental level video, it's not meant to be exhaustive, Kubernetes is a complex topic so I'm just covering the parts that you need to understand to get started. The cluster will also likely have many more nodes — it's rare that you only have one node unless this is a testing environment.

First I want to talk about pods and pods are the smallest unit of computing within Kubernetes; you can have pods which have multiple containers and provide shared storage and networking for those pods, but it's very common to see a one container one pod architecture which as the name suggests means each pod contains only one container. Now when you think about Kubernetes don't think about containers — think about pods — you're going to be working with pods and you're going to be managing pods, the pods handle the containers within them. Architecturally you would generally only run multiple containers in a pod when those containers are tightly coupled and require close proximity and rely on each other in a very tightly coupled way. Additionally although you'll be exposed to pods you'll rarely manage them directly — pods are non-permanent things; in order to get the maximum value from Kubernetes you need to view pods as temporary things which are created, do a job and are then disposed of. Pods can be deleted when finished, evicted for lack of resources or if the node itself fails — they aren't permanent and aren't designed to be viewed as highly available entities. There are other things linked to pods which provide more permanence but more on that elsewhere.

So now let's talk about what runs on the control plane. Firstly I've already mentioned this one — the API known formally as kube-api server — this is the front end for the control plane, it's what everything generally interacts with to communicate with the control plane and it can be scaled horizontally for performance and to ensure high availability. Next we have ETCD and this provides a highly available key value store — so a simple database running within the cluster which acts as the main backing store for data for the cluster. Another important control plane component is kube-scheduler and this is responsible for constantly checking for any pods within the cluster which don't have a node assigned, and then it assigns a node to that pod based on resource requirements, deadlines, affinity or anti affinity, data locality needs and any other constraints — remember nodes are the things which provide the raw compute and other resources to the cluster and it's this component which makes sure the nodes get utilized effectively.

Next we have an optional component — the cloud controller manager — and this is what allows kubernetes to integrate with any cloud providers. It's common that kubernetes runs on top of other cloud platforms such as AWS, Azure or GCP and it's this component which allows the control plane to closely interact with those platforms. Now it is entirely optional and if you run a small kubernetes deployment at home you probably won't be using this component.

Now lastly in the control plane is the kube controller manager and this is actually a collection of processes — we've got the node controller which is responsible for monitoring and responding to any node outages, the job controller which is responsible for running pods in order to execute jobs, the end point controller which populates end points in the cluster (more on this in a second but this is something that links services to pods — again I'll be covering this very shortly), and then the service account and token controller which is responsible for account and API token creation. Now again I haven't spoken about services or end points yet — just stick with me, I will in a second.

Now lastly on every node is something called kproxy known as kube proxy and this runs on every node and coordinates networking with the cluster control plane — it helps implement services and configures rules allowing communications with pods from inside or outside of the cluster. You might have a kubernetes cluster but you're going to want some level of communication with the outside world and that's what kube proxy provides.

Now that's the architecture of the cluster and nodes in a little bit more detail but I want to finish this introduction video with a few summary points of the terms that you're going to come across. So let's talk about the key components — so we start with the cluster and conceptually this is a deployment of kubernetes, it provides management, orchestration, healing and service access. Within a cluster we've got the nodes which provide the actual compute resources and pods run on these nodes — a pod is one or more containers and is the smallest admin unit within kubernetes and often as I mentioned previously you're going to see the one container one pod architecture — simply put it's cleaner. Now a pod is not a permanent thing, it's not long lived — the cluster can and does replace them as required.

Services provide an abstraction from pods so the service is typically what you will understand as an application — an application can be containerized across many pods but the service is the consistent thing, the abstraction — service is what you interact with if you access a containerized application. Now we've also got a job and a job is an ad hoc thing inside the cluster — think of it as the name suggests as a job — a job creates one or more pods, runs until it completes, retries if required and then finishes — now jobs might be used as back end isolated pieces of work within a cluster.

Now something new that I haven't covered yet and that's ingress — ingress is how something external to the cluster can access a service — so you have external users, they come into an ingress, that's routed through the cluster to a service, the service points at one or more pods which provides the actual application. So an ingress is something that you will have exposure to when you start working with Kubernetes. And next is an ingress controller and that's a piece of software which actually arranges for the underlying hardware to allow ingress — for example there is an AWS load balancer ingress controller which uses application and network load balancers to allow the ingress, but there are also other controllers such as engine X and others for various cloud platforms.

Now finally and this one is really important — generally it's best to architect things within Kubernetes to be stateless from a pod perspective — remember pods are temporary — if your application has any form of long running state then you need a way to store that state somewhere. Now state can be session data but also data in the more traditional sense — any storage in Kubernetes by default is ephemeral provided locally by a node and thus if a pod moves between nodes then that storage is lost. Conceptually think of this like instance store volumes running on AWS EC2. Now you can configure persistent storage known as persistent volumes or PVs and these are volumes whose life cycle lives beyond any one single pod which is using them and this is how you would provision normal long running storage to your containerised applications — now the details of this are a little bit beyond this introduction level video but I wanted you to be aware of this functionality.

Ok so that's a high level introduction to Kubernetes — it's a pretty broad and complex product but it's super powerful when you know how to use it. This video only scratches the surface. If you're watching this as part of my AWS courses then I'm going to have follow up videos which step through how AWS implements Kubernetes with their EKS service. If you're taking any of the more technically deep AWS courses then maybe other deep dive videos into specific areas that you need to be aware of. So there may be additional videos covering individual topics at a much deeper level. If there are no additional videos then don't worry because that's everything that you need to be aware of. Thanks for watching this video, go ahead and complete the video and when you're ready I look forward to you joining me in the next.

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Manuscript number: RC-2025-02860

Corresponding author(s): Duncan, Sproul

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We thank the reviewers for recognizing that our work contributes 'both conceptually and mechanistically to our understanding of how DNA methylation patterns are regulated during cancer development' and their insightful suggestions to improve the manuscript. We note that the reviewers suggest that the data are 'comprehensive', 'well-controlled', 'rigorously done' and 'diligently analysed'.

Our planned revisions focus on further elucidating the broader implications of our findings for partially methylated domain formation in cancer, the effects of the methylation changes we observe on gene expression and the potential mechanisms underpinning the formation of the hypermethylated domains we observe.

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February 21, 2025
*RE: Review Commons Refereed Preprint #RC-2025-02860 *

*Kafetzopoulos *

DNMT1 loss leads to hypermethylation of a subset of late replicating domains by DNMT3A

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

The DNA methylation landscape is frequently altered in cancers, which may contribute to genome misregulation and cancer cell behavior. One phenomenon is the emergence of "partially methylated domains (PMDs)": intermediately methylated regions of the genome that are generally heterochromatic and late replicating. The prevailing explanation is that the DNA methyltransferase, DNMT1, is not able to maintain DNAme levels at late replicating sites in proliferating cancer cells. This could result in genome instability. In this study, Kafetzopoulos and colleagues interrogated this possibility using a common laboratory colorectal cancer cell line (HCT116). Additionally, they utilized a DNMT1 mutant line that they refer to as a knockout, even though, more accurately, it is a hypomorphic truncation. They performed several genomic assays, such as whole genome bisulfite sequencing, ChIP and repli-seq, in order to assess the effect of reduced DNMT1 activity. While expectedly, global DNAme levels are decreased, they discovered a subset of PMDs gain DNA methylation, which they term hyperPMDs. There seems to be no impact on DNA replication timing, but the authors did go on to show that the de novo DNA methyltransferase, DNMT3Α, is likely responsible for this counterintuitive increase in DNAme levels.

*Reviewer #1 (Significance (Required)): *

Overall, I found the data well-presented and diligently analyzed, as we have come to expect from the Sproul group. However, I am somewhat at a loss to understand both the rationale for the experimental set-up and the meaning of the results. The HCT116 cell line is already transformed but was treated as though it was a wild-type control. I was more curious to see how the PMD chromatin state and replication compare to a healthy cell.

We focused on the comparison between WT and DNMT1 KO cells as we wanted to understand the role of DNMT1 in maintaining the organisation of the cancer methylome. We agree that, strictly, this could differ from its role in normal cells. However, we are unaware of a suitable cell line to test the consequences of DNMT1 KO in normal colon cells and testing this in vivo would be beyond the time-scale of a manuscript revision.

To further understand the relevance of our findings in the context of carcinogenesis, we propose to analyse data derived from normal and cancerous colon tissue in the revised manuscript. Preliminary analysis shows that HCT116 PMDs are hypomethylated in a colorectal tumour but not in the normal colon (revision plan figure 1). This suggests that HCT116 cells are a model that can be used to understand PMD formation in tumours and we will extend this analysis in the revised manuscript. We will also add discussion of the caveat that DNMT1 may function differently in normal tissues and cancer cells.

Note, revision plan figure 1 was included with the full submission but cannot be uploaded in this format.

Revision plan figure 1. HCT116 PMDs are hypomethylated in colorectal tumours. Heatmaps and pileup plots of HCT116, normal colon and colorectal tumour DNA methylation levels for HCT116 PMDs (n=546 domains) and HMDs (n=558 domains). DNA methylation levels are mean % mCpG. PMDs and HMDs are aligned and scaled to the start and end points of each domain and ranked based on their mean methylation levels in HCT116 cells. Colon and tumour data re-analysed from a previous publication (Berman et al 2011, PMID: 22120008).

Moreover, the link between late replication and PMDs would indicate that a DNMT1 gain-of- function line would potentially be more interesting: could more increased DNMT activity rescue the PMDs, and how would this impact the chromatin and replication states? Perhaps this is not trivial to create; I do not know if simply overexpressing DNMT1 and/or UHRF1 could act as a gain-of-function.

We agree with the reviewer that a DNMT1 overexpression or a gain-of-function mutation cell line would be interesting to analyse and potentially informative as to the mechanism of PMD formation. However, as the reviewer notes, this is a complex experiment that could require the overexpression of partners such as UHRF1 or generation of an unknown gain-of-function mutation. In addition, the full dissection of the implications of this separate experimental strategy would entail the repetition of the majority of our experiments in DNMT1 KO cells. Instead, in the revised manuscript, we will focus on a related experiment suggested by reviewer 2 and ask whether re-expression of DNMT1 rescues DNA methylation patterns DNMT1 KO cells.

Nevertheless, the appearance of hyperPMDs was a curious finding worth publishing. However, it is unclear what the biological relevance is. There is no effect on replication timing, and no assessment on cell behavior (eg, proliferation assays).* In other words, is DNMT3A performing some kind of compensatory action, or is it just a curiosity? Below in the significance section, I have highlighted some additional specific points *

PMDs are important to study because cancer-associated hypomethylation is believed to drive carcinogenesis through genomic instability (Eden et al 2003, PMID: 12702868). However, the mechanisms underpinning their formation remain unclear. At present the predominant hypothesis is that PMDs emerge in heterochromatin because their late replication timing leaves insufficient time for re-methylation following DNA replication (Zhou et al 2018, PMID: 29610480 and Petryk et al 2021, PMID: 33300031). We believe that our observations of hypermethylated PMDs in DNMT1 KO cells provides important evidence contrary to this hypothesis because they disconnect domain-level methylation patterns from the replication timing program. Our work instead suggests that the localization of de novo DNMTs plays a key role in the formation of PMDs by protecting euchromatin from hypomethylation.

To further explore this hypothesis, we propose to analyze data derived from tumours in our revised manuscript to understand the degree to which our findings are reflected in vivo. As shown above, our preliminary analysis suggests that HCT116 cell PMDs are also hypomethylated in a colorectal tumour but not the normal colon (revision plan figure 1). We will also analyze how the changes in methylome affect gene expression using our RNA-seq data.

- Why were DNMT3A and 3B transgenes used for ChIP instead of endogenous proteins? I know the authors cited work justifying this strategy, but this still merits explanation. Also, the expression level of transgenes compared to the endogenes was not shown (neither protein nor RNA level).

DNMT3A and B transgenes were used because antibodies against the endogenous proteins are not suitable for ChIP. Furthermore, performing these experiments using endogenously tagged proteins, required generating 3 knock-in tagged lines (we have already generated HCT116 cells with tagged DNMT3B, Masalmeh et al 2021, PMID: 33514701).

We have previously shown that our constructs do indeed result in overexpression of DNMT3B compared to endogenous protein in this system (Masalmeh et al 2021, PMID: 33514701). However, our previous results also demonstrate that overexpressed DNMT3B recapitulates the localization of the endogenously tagged protein to the genome (Taglini et al 2024, PMID: 38291337). Others have similarly demonstrated that ectopically expressed DNMT3A and DNMT3B can be used to understand their localization on the genome (Baubec et al 2015, PMID: 25607372 and Weinberg et al 2019, PMID: 31485078).

To address this point, we propose to add further justification of our approach and discussion of this potential limitation to a revised version of the manuscript.

- The DNMT3A binding profile appears as though it is on the edges of the PMDs and fairly depleted within (Fig 4A,D). Could the authors comment on this?

This is an interesting point. We note that although mean DNMT3A signal is indeed higher at the edges of hypermethylated PMDs than inside these domains, its levels are both above background and the levels observed in HCT116 cells. As suggested by reviewer 3, this could be consistent with H3K36me2 and DNMT3A spreading in from the boundaries of hypermethylated PMDs in DNMT1 KO cells. We propose to add discussion of this possibility to the revised version of the manuscript.

- A more compelling experiment would be to assess the loss of DNMT3A genetically. How would this affect PMD DNA methylation? Maybe in this case there would be an effect on replication timing. Could a KO or KD (eg, siRNA) strategy be employed to assess this on top of either the HCT116 or DNMT1 KO.

As the reviewer suggests, functional experiments aimed at understanding the role of DNMT3A in our system are likely to be informative. We therefore propose to include such experiments in a revised version of the manuscript.

- What is the major H3K36me2 methylatransferase in these cells? Could an Nsd1 KO or KD strategy be used, for example, to show that indeed H3K36 methylation is required for HyperPMDs? This would complement the DNMT3A experiment above.

H3K36 methylation is thought to be deposited in the mammalian genome by at least 8 different methyltransferase enzymes, NSD1, NSD2, NSD3, ASH1L, SETD2, SETMAR, SMYD2 and SETD3 (Wagner and Carpenter 2023, PMID: 22266761). To understand which of these might be responsible for the deposition of H3K36me2 in hypermethylated PMDs, we have examined their expression in HCT116 and DNMT1 KO cells using our RNA-seq data. This suggests that 5 of these enzymes are highly expressed in HCT116 cells and their expression levels are similar in DNMT1 KO cellsrevision plan figure 2). The other 3 putative methyltransferases have lower expression levels and, although SMYD2 is significantly upregulated in DNMT1 KO cells, its expression remains low (revision plan figure 2). It is currently unclear whether SMYD2 is a bona fide H3K36 methyltransferase (Wagner and Carpenter 2023, PMID: 22266761). We also note that in a recent study, cells lacking NSD1, NSD2, NSD3, ASH1L and SETD2 had no detectable H3K36 methylation, although expression levels of SMYD2 were not reported (Shipman et al, 2024. PMID: 39390582). Based on this analysis, it is therefore unclear which enzyme(s) might be responsible for H3K36me2 deposition in hypermethylated PMDs and delineation of this enzyme would require multiple perturbation and sequencing experiments. We therefore suggest that assessing the consequences of knocking out H3K36me2 methyltransferase activity on hypermethylated PMDs is beyond the scope of a manuscript revision. We propose to include discussion of the expression of the different H3K36me2 depositing enzymes in the revised manuscript.

Note, revision plan figure 2 was included with the full submission but cannot be uploaded in this format.

Revision plan figure 2. HCT116 cells express multiple H3K36 methyltransferases. Barplot of mean expression levels for putative mammalian H3K36 methyltransferases in HCT116 and DNMT1 KO cells. Expression levels are counts per million (CPM) derived from RNA-seq. Mean expression levels are derived from 9 and 4 independent cultures of HCT116 and DNMT1 KO cells respectively.

- Based on Figure 2C, it seems that a general predictive pattern of hyperPMDs is H3K9me3-enriched and H3K27me3-depleted. Is this an accurate interpretation? Given the authors' expertise in the relationship between DNMT3A and polycomb, could they perhaps give an explanation for this phenomenon?

The reviewer is correct. In HCT116 cells, those PMDs that become hypermethylated in DNMT1 KO cells are marked by H3K9me3 and are H3K27me3-depleted (except at their boundaries). DNMT3A is recruited to polycomb-marked regions associated with H3K27me3 through interaction of its N-terminal region with H2AK119ub. However, this mark is depleted from hypermethylated-PMDs in DNMT1 KO cells (current manuscript Figure S5D) meaning that this pathway of recruitment is unlikely to explain DNMT3A's localisation to these regions in DNMT1 KO cells. This is discussed in the current manuscript:

We and others have reported that DNMT3A is also recruited to the polycomb-associated H2AK119ub mark through its N-terminal region (Chen et al, 2024; Gretarsson et al, 2024; Gu et al, 2022; Wapenaar et al, 2024; Weinberg et al, 2021). However, we do not observe the polycomb-associated H3K27me3 mark, which is generally tightly correlated with H2AK119ub (Ku et al, 2008), at hypermethylated PMDs suggesting that H2AK119ub does not play a role in the recruitment of DNMT3A to these regions.

Furthermore, DNMT3A's localisation is predominantly driven by its PWWP-dependent H3K36me2 recruitment pathway unless its PWWP domain is mutated (Heyn et al 2019, PMID: 30478443, Sendžikaitė et al 2019, PMID: 31015495, Kibe et al 2021, PMID: 34048432 and Weinberg et al, 2021, PMID: 33986537). Our observations of DNMT3A at hypermethylated PMDs marked by H3K36me2 is therefore consistent with previous findings. We propose to discuss this point in the revised manuscript.

- This is a minor point, but calling the DNMT1 mutant a "KO" seemed a bit misleading, as it is a truncation mutant. Perhaps there is a more accurate way to describe this line.

We propose to amend the manuscript to reflect this point as suggested by the reviewer. To ensure our responses are consistent with the reviewer comments we continue to refer to this line as DNMT1 KO cells in our revision plan.

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

*In this study, Kafetzopoulos et al. investigated the role of DNMT1-mediated methylation maintenance in cancer partially methylated domains (PMDs) using DNMT1 knockout HCT116 colorectal cancer cells. They used a range of sequencing-based approaches, including whole-genome bisulfite sequencing (WGBS), chromatin immunoprecipitation sequencing (ChIP-seq), and replication timing sequencing (Repli-seq), to define the dynamics of DNA methylation loss and gain in PMDs during DNA synthesis. Interestingly, they demonstrate that specific PMDs marked by H3K9me3 undergo a gain of DNA methylation in DNMT1-deficient HCT116 cells. This increase in methylation is associated with the loss of H3K9me3, an enrichment of H3K36me2, and the recruitment of DNMT3A. These findings suggest that de novo methyltransferase activity plays a critical role in determining which genomic regions become PMDs in cancer. *

*The authors use a comprehensive and well-controlled set of sequencing-based techniques. While the sequencing depth for DNA methylation is somewhat limited, the inclusion of multiple biological replicates strengthens the reliability of the data. The study effectively integrates multiple layers of epigenomic information, providing a nuanced view of PMD regulation in the context of DNMT1 loss. *

*Overall, this paper provides valuable insights into the epigenetic regulation of PMDs in cancer, and its conclusions are well supported by the data. It significantly advances our understanding of how DNMT1 loss reshapes the epigenome and highlights the interplay between de novo and maintenance methylation mechanisms in cancers. *

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*Reviewer #2 (Significance (Required)): *

General assessment

-The main strength of the study lies in the clear presentation of the data, which follows a cohesive and well-defined storyline.

*-The authors demonstrate that both hypomethylated and hypermethylated domains occur at the late replication stage. They further investigate the dynamics of histone modifications and DNA methylation, focusing on the acquisition and loss of these marks, particularly in relation to DNMT3A and DNMT3B. *

Limitation

-Although the study is compelling, its primary limitation is the correlative nature of most of the data. While the high-level representations (e.g., tracks, heat maps) are convincing, the study would have been more informative if it had explored the impact of these changes on a specific set of genes or regions critical to cancer initiation and progression. For example, in the DNMT1 knockout model, how does the loss of H3K9me3, the gain of H3K36me2, and the recruitment of DNMT3A in hypermethylated PMDs affect the expression of key genes involved in colorectal cancer?

To understand how the remodeling of DNA methylation and chromatin structure in DNMT1 KO cells affects gene expression, we propose to include an analysis of our RNA-seq data in the revised manuscript. We will also cross reference these results and our ChIP-seq with lists of colorectal cancer genes.

Additional experiments that could provide deeper insights

-Cross-validation in other cancer cell lines would have enable to define if these signatures are observed beyond HCT116.

As the reviewer suggests, we propose to undertake analyses of additional samples in the revised manuscript to understand how our findings relate to domain-level methylation patterns beyond HCT116 cells. As noted above in response to reviewer 1, our preliminary analysis suggests our findings are relevant for primary colorectal tumours (revision plan figure 1).

-Are the observed signatures permanent, or could they be reversed by reinstating the full activity of DNMT1? Since DNMT1 might be dysregulated but never completely deleted.

To address this suggestion, we propose to include the results of a DNMT1 rescue experiment in the revised manuscript.

-Use knockdown and overexpression experiments to track the dynamics and occurrence of these molecular events over time, providing insight into the progression and reversibility of epigenetic changes.

This is an interesting suggestion. As the reviewer suggests, we propose to analyse data derived from time-course experiments to understand the dynamics of changes in different genomic compartments following perturbation of DNMT1.

Advances

-The study provides new insights into the establishment of PMD types in colorectal cancer cell lines.

-These findings contribute both conceptually and mechanistically to our understanding of how DNA methylation patterns are regulated during cancer development.

Audience:

-This study will appeal to a broad audience, from researchers primarily focused on epigenetics and cancer biology to those interested in the mechanistic underpinnings of DNA methylation and its role in cancer progression. It will also be relevant to those exploring therapeutic strategies targeting epigenetic regulators in cancer.

We thank the reviewer for their kind comments on our manuscript.

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

Summary:
*Cancer is linked to the acquisition of an atypical DNA methylation landscape, with broad domains of partial DNA methylation (termed PMDs). This study investigates PMDs in a colorectal cancer cell line and evaluates the contribution of DNMT1 in maintaining PMDs, using a DNMT1 KO line. The authors find that PMDs preferentially lose DNA methylation upon loss of DNMT1, but they find a number of domains that paradoxically gain DNA methylation (hyperPMDs). They attribute this gain of methylation to the action of DNMT3A through the accumulation of H3K36me2 and loss of heterochromatin mark H3K9me3. Together this work sheds light on the dynamic mechanisms regulating the atypical DNA methylation landscape in colorectal cancer cells. *

General comments:
The introduction is informative and well written. Additionally, the work is rigorously done and analyses are clear. However, the conclusions and summary figure largely focus on the relationship between PMDs with H3K9me3 and H3K36me2, but I think the role for H3K27me3 should be revisited based on the results presented. H3K9me3 is present at PMDs and hyperPMDs, but H3K27me3 level appears to be a much more defining feature of whether they lose or gain methylation upon loss of DNMT1 (Figure 2, Figure S2C- D). There is a reported interplay between PRC2 and DNMT3A activity at DNA methylation valleys in other cell contexts (e.g., mouse embryogenesis, hematopoietic cells), so couldn't H3K27me3 be performing a 'boundary' function at PMDs and when sufficiently low, permits spread of H3K36me2 in the absence of DNMT1? I think it is worth further exploring the H3K27me3 data.

The reviewer makes an interesting point about the potential for H3K27me3 to act as a boundary preventing H3K36me2 spread into PMDs. Multiple studies have shown that H3K36me2 restricts H3K27me3 deposition in the genome (Streubel et al 2018, PMID: 29606589, Shirane et al 2020, PMID: 32929285 and Farhangdoost et al 2021, PMID: 3362635). The structural nature of this inhibitory effect has also been resolved, demonstrating that the PRC2 catalytic subunit, EZH2 directly binds H3K36 and this is inhibited when the residue is methylated (Jani et al 2019, PMID: 30967505, Finogenova et al 2020, PMID: 33211010 and Cookis et al 2025, PMID: 39774834). The effect of H3K27me3 on H3K36me2 is less well characterised. However, previous work has suggested that inhibiting EZH2 leads to elevated H3K36me2 being established on newly replicated chromatin (Alabert et al 2020, PMID: 31995760). Expression of the EZH2-inhibiting oncohistone H3.3K27M has also been reported to lead to increased H3K36me2 dependent on NSD1/2 in diffuse intrinsic pontine gliomas (DIPG) (Stafford et al 2018, PMID: 30402543 and Yu et al 2021, PMID: 34261657). However, this increase was not reported by an independent study of H3.3K27M DIPG cells (Harutyunyan et al 2020, PMID: 33207202) and the molecular basis of the effect of H3K27me3 on H3K36me2 remains unclear.

As the reviewer suggests, we propose to explore the relationship between H3K27me3 and H3K36me2 further in a revised manuscript along with the including further discussion of previous findings in this area.

Additionally, a key point that is illustrated in the summary figure, is the localization of H3K36me2 at HMDs and its mutual exclusivity with H3K9me3 (a mark typically associated with high DNA methylation). However, because the H3K36me2 is introduced quite late in the analysis, I feel that a rigorous evaluation of its enrichment and anti-correlation with H3K9me3 at highly methylated domains (HMDs) is missing.

The relationship between H3K36me2 and H3K9me3 is far less explored than that of H3K27me3 and H3K36me2. Interestingly, we note that a recent study reported that depletion of H3K36me2 results in H3K9me3 re-distribution suggesting that H3K9me3 is restricted by H3K36me2 (Padilla et al 2024, DOI: 10.1101/2024.08.10.607446, also cited in the original manuscript).

To understand this relationship further, we therefore propose to explore the relationship between H3K9me3 and H3K36me2 in our datasets as part of revised manuscript along with including additional discussion of relevant experimental findings.

In general, I also found that I was jumping between figures a lot and needed to look at the supplements to gain the full picture. It may be beneficial to re-organize the figures.

In accordance with the reviewer's suggestion, we propose to re-organise the revised manuscript to make it easier to follow.

Specific Comments/Questions:

• An expanded explanation of the truncated DNMT1 in the DNMT1 KO cells would be helpful for context**
* As suggested by the reviewer, we will amend the manuscript to include an expanded discussion of the DNMT1 truncation present in the cell line.

• Does the DNMT expression in HCT116 cells reflect the levels seen in primary colorectal cancers? Hence, do you think these cultured cells reflect aspects of DNA methylation dynamics that would be seen in tumors?**
*

While differences between cancer cell line and tumour methylation patterns have previously been noted (for example Anne Rogers et al 2018, PMID: 30559935), we have previously demonstrated that HCT116 cells recapitulate CpG island methylation patterns observed in colorectal tumours (Masalmeh et al 2021, PMID: 33514701). As stated above in response to reviewer 1, we have now examined the methylation status of HCT116 PMDs in a colorectal tumour. This analysis shows that HCT116 PMDs have reduced methylation levels in a colorectal tumour but not in the normal colon (revision plan figure 1). We propose to extend this analysis of colorectal tumour samples and add them to the revised manuscript to address this point.

Regarding the expression of DNMTs in colorectal tumours, DNMT1 is ubiquitously expressed to our knowledge. DNMT3B is reported to be overexpressed in 15-20% of cases of colorectal cancer, often as a result of amplification (Nosho et al 2009, PMID: 19470733, Ibrahim et al 2011, PMID: PMID: 21068132, Zhang et al 2018, PMID: 30468428 and Mackenzie et al 2020, PMID: 32058953). DNMT3A expression in colorectal tumours is less studied but one report suggests upregulation in at least some tumours (Robertson et al 1999, PMID: 10325416 and Zhang et al 2018, PMID: 30468428). We propose to add additional discussion of DNMT expression in colorectal cancer to the revised manuscript to clarify the degree to which our results reflect methylation regulation in primary colorectal tumours.

• Although DNMT3A/B mRNA levels are similar between DNMT1 KO and HCT116 cells, is the protein abundance altered? I think there would be value in showing a Western blot analysis, as the loss of DNMT1 protein may alter the stability of the de novo DNMTs. Is a similar level of expression of the ectopic T7-DNMT3A and T7-DNMT3B achieved in HCT116 and DNMT1 KO cells? A western blot showing this would also be valuable.**
*

As part of our work towards revising the manuscript, we have undertaken blots of DNMT3A in our cell lines. This shows that DNMT3A levels in DNMT1 KO cells are similar to those in HCT116 cells which (revision plan figure 3). We propose to include this in the revised manuscript alongside a similar analysis of DNMT3B. We will also include an analysis of T7-DNMT3A and T7-DNMT3B levels to understand whether they are expressed to similar levels in HCT116 and DNMT1 KO cells.

Note, revision plan figure 3 was included with the full submission but cannot be uploaded in this format.

Revision plan figure 3. DNMT3A protein levels are similar in HCT116 and DNMT1 KO cells. Left, representative DNMT3A Western blot. Right, bar plot quantifying relative DNMT3A levels. The bar height indicates the mean levels observed in protein extracts from 3 independent cell cultures. Individual points indicate the level of each replicate.

• Do you think that the increase in DNMT3A over HyperPMD compared to H3K9me3-marked PMDs is related to an increase in protein bound at these domains or an altered residence time?*

The reviewer makes an interesting point with regard to a potential alteration of DNMT3A residence at hypermethylated PMDs. Given that ChIP-seq signal is affected by residence time (Schmiedeberg et al 2009, PMID: 19247482), it is possible that our findings could reflect this rather than increased DNMT3A localisation. We propose to add discussion of this point as a limitation of the current study to the manuscript.

It would also be valuable to move the plot showing levels of DNMT3A/3B at HMDs, from the S4C/D to the main Figure 4, for reference. It would also be interesting to see the enrichment of DNMT3A/B at all PMDs (not just H3K9me3-marked PMDs).*
*

As the reviewer suggests, we will include the data on HMDs to the main Figure 4 and include enrichments at all PMDs in the supplementary figures.

• It appears that the same genomic locus is used multiple times across figures Fig 1A, Fig 2B, Fig 3A, Fig 4A, Fig 5B to illustrate the trends reported from the global analyses. While this has value in showing the dynamics across datasets at this region, I think it is important to illustrate that these trends can be observed elsewhere. Please add or replace some plots with additional loci. Furthermore, please add the genomic region coordinates to the figure or figure legend.*

We had shown a single locus for consistency and to not overcomplicate figures which already contain multiple panels. As the reviewer suggests, we will add additional loci in the supplementary figures of our revised manuscript. We had also included the chromosome co-ordinates in the figures. In the revised version we will ensure that the precise co-ordinates are included in the legends.

• The ChIP-seq data is quantified as IP/input. This quantitation can be prone to introducing artefacts into analyses if the input coverage is substantially uneven over AT-rich regions or CpG islands, or if the sequencing depth is insufficient. I would encourage the authors to check that the trends observed are still present if quantified without correcting against the inputs. If using IP/input, in the supplementary figures, I think it would be valuable to show the uncorrected quantitation of inputs across PMDs, to demonstrate that there is even coverage and this isn't contributing to any of the changes observed.**
*

We thank the reviewer for this point and we propose to examine the quantification of the ChIP-seq without normalizing to input to ensure that uneven input signal does not substantially contribute to our results.

• Generally, the n numbers for different groups of probes can be confusing and increased clarity would be helpful.*

We will clarify the explanation of n numbers in the revised manuscript.

*Reviewer #3 (Significance (Required)): *

This study adds to the accumulating body of evidence that DNMT3A recruitment is mediated primarily through H3K36me2 across cell contexts, shedding light on the interplay between histone modifications and de novo DNA methylation. Understanding these mechanisms is important to appreciate the role for DNMT3A in establishing DNA methylation in development and disease contexts. It does remain unclear why, upon loss of DNMT1 in colorectal cancer cells, some PMDs accumulate H3K36me2 and consequently DNA methylation, while others do not. Further study into the chromatin dynamics will be valuable in understanding determinants of the DNA methylation landscape in cancer.

We thank the reviewer for their insightful comments and believe that our proposed revisions will further clarify the points they raise.

3. Description of the revisions that have already been incorporated in the transferred manuscript

Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. If no revisions have been carried out yet, please leave this section empty.

We have not yet incorporated revisions into the manuscript.

4. Description of analyses that authors prefer not to carry out

Please include a point-by-point response explaining why some of the requested data or additional analyses might not be necessary or cannot be provided within the scope of a revision. This can be due to time or resource limitations or in case of disagreement about the necessity of such additional data given the scope of the study. Please leave empty if not applicable.

As stated in our responses to the reviewer comments above, we plan to address all comments. However, we suggest that two experiments proposed by the reviewers are beyond the scope of a manuscript revision and we will instead address these comments in the following manner:

Analysis of a DNMT1 gain-of-function line (Reviewer 1). As suggested by the reviewer such a line is non-trivial to generate. It would also require extensive profiling of this new line to fully understand its implications for our findings. We therefore believe it is outwith the scope of a manuscript revision. Instead, we propose to address this comment by undertaking the related experiment suggested by Reviewer 2 and perform a DNMT1 rescue experiment in the DNMT1 KO line. Analysis of H3K36me2 methyltransferase knockout cells (Reviewer 1). Our preliminary analysis suggests that HCT116 cells express multiple H3K36 methyltransferases and that their expression does not vary greatly in DNMT1 KO cels (revision plan figure 2). This means that it is unclear which enzyme(s) might be responsible for depositing H3K36me2 in hypermethylated PMDs. Delineation of this would require the generation and analysis of multiple knockouts and we suggest it is therefore outwith the scope of a manuscript revision. To address this point we will instead include discussion of the spectrum of H3K36 methyltransferases expressed in our cells in the revised manuscript as detailed in the specific response above.

This work has been published in GigaByte Journal under a CC-BY 4.0 license (https://doi.org/10.46471/gigabyte.153). These reviews (including a protocol review) are as follows.

Reviewer 1. Yanshuo Liang

The manuscript by Conn et al. detail the high-quality genome assembly of Acropora pulchra, a Acropora of ecological and evolutionary significance, and also analyzes its genome-wide DNA methylation characteristics. These data complement the genetic resources of the Acropora genome. This manuscript is well written and represents a valuable contribution to the field. I have some comments below for the authors to address but look forward to seeing this research published. Q1: In the first sentence of the second paragraph of the Context: This is the first study to utilize PacBio long-read HiFi sequencing to generate a high quality genome with high BUSCO completeness, in tandem with its DNA methylome for scleractinian corals. Language such as "new", "first", "unprecedented", etc, should be avoided because it often leads to unproductive controversy. As far as I know, the genome you assembled is not the first stony coral to be sequenced using PacBio long-read HiFi sequencing. Back in 2024, He et al. assembled Pocillopora verrucosa (Scleractinia) to the chromosome level using PacBio HiFi long-read sequencing and Hi-C technology. Here I would suggest please rephrase. Reference： He CP, Han TY, Huang WL, et al. Deciphering omics atlases to aid stony corals in response to global change, 11 March 2024, PREPRINT (Version 1) available at Research Square [https://doi.org/10.21203/rs.3.rs-4037544/v1]. Q2: In this sentence: “On 23 October 2022, sperm samples were collected from the spawning of A.pulchra and preserved in Zymo DNA/RNA shield.” Please “A.pulchra” to “A. pulchra”. Q3: Please change all “k-mer” into “k-mer” in the manuscript. Q4: Please change “Long-Tandem Repeats” to “Long Terminal Repeats” Q5: In this sentence: “Funannotate train uses Trinity [18] and PASA [19] for ab initio predictions. Funannotate predict was then run to assign gene models using AUGUSTUS [20], GeneMark [21], and Evidence Modeler [19] to estimate final gene models.” Please write versions of these software. Q6: [20] Later references do not correspond well in the manuscript, please check!

Reference 2. Jason Selwyn

Is the language of sufficient quality? Yes. There are some minor grammatical issues throughout that warrent a closer reading to correct. E.g. Abstract: "...urgency to identify how genetic, epigenetic, and environmental...", "...management and and conservation...". Context: "...we aim to provide..." etc. Are all data available and do they match the descriptions in the paper? Yes. The link to the OSF repository in the PDF did not work. However, the link to the OSF repository from the github did work. Is the data acquisition clear, complete and methodologically sound? No. It isn't mentioned in the manuscript where the RNAseq data used to annotate the genome is from, nor any quality filtering steps that may have been applied to the RNA data prior to its use for annotation. Is there sufficient detail in the methods and data-processing steps to allow reproduction? Yes. Excluding the above comment about the RNA data. Additional Comments: This is a well assembled, and annotated genome that will contribute to the growing database of Acropora genomes. The manuscript could do with a simple pass to identify and correct some relatively minor grammatical issues and inconsistencies (Table 1 includes a thousands comma separator in some instances and not others) and needs to include details about the source of the RNA data used to train the ab initio gene predictors. There also appears to be a problem with the citation numbering after 20.

**Reviewer 3. Benjamin Young ** Are all data available and do they match the descriptions in the paper? Yes. Raw reads, metadata, and genome assembly are publicly available and have a NCBI project number in which they are all linked. Is the data acquisition clear, complete and methodologically sound? Yes. Collection of sperm samples, HMW DNA extraction, and SMRT Bell Library prep are written clearly. I have asked for a few clarifications on wording in this section in the attached edited pdf document. Is there sufficient detail in the methods and data-processing steps to allow reproduction? Yes. I think the pipeline used for de-novo genome generation (including raw read cleaning and assembly), repeat masking, and gene prediction and annotation is of high quality and best practices. With the inclusion of the GitHub and all analyses scripts, it is possible to reproduce the assembly generated. Is there sufficient data validation and statistical analyses of data quality? Yes. This is not super relevant for a genome assembly paper so I have no additional comments here. Is the validation suitable for this type of data? Yes. The authors use tools such as GenomeScope2 and BUSCO for validation of their data. It would be nice to see the tool they used to identify N50 and L50 (maybe Quast) included in the methods. Additionally, I would like to see a Merqury analysis of the HifiAsm primary and alternate assemblies to show that duplicate purging was successful. Additional Comments: I would first like to commend the authors for a well assembled genome resource for a coral species that will be greatly beneficial to the wider coral and scientific community. I have provided a PDF with comments throughout for the authors to address. The majority of these are easy fixes, including things such as sentence structure, inconsistent capitalisation of subheadings, additional references for methods, clarification of statements, and other suggestions. I do have a few larger requests for this to be published, and these are the reasons for selecting the major revision option as there may need to be figure updates, and quick additional analyses to be run. 1. Can you please correct the verbiage around BUSCO analysis throughout the manuscript. It is often stated "BUSCO completeness of xx%". BUSCO doesn't directly measure completeness, rather completeness of single copy orthologs against a specific database. I have left comments throughout on potential rewording for these instances. Please also specify the exact database you used (i.e. odb10_metazoa). Finally, can you please be more specific when stating BUSCO results, specifically when you use 96.9% this is single copy and duplicated complete BUSCOS. I have left comments in the pdf again for this. 2. In the results for Genome Assembly section can you please include results (i.e. length, N50, L50, number contigs/scaffolds) for the primary assembly and the scaffolded assembly. 3. I think it would be not much work and provide additional information to show successful duplicate purging to run a Merqury analysis on the primary and alternative assemblies from HiFiAsm. 4. Can you include some additional information in the "Structural and Functional Annotation section". Specifically, can you provide information on the results from the funannoatate predict step, and then how funannotate update improved this (if at all). 5. Please double check the methods section for funannotate. From reading the funannoatate documentation I think there may be some confusion on what each step (train, predict, update, annotate) is doing. I have provided comments in the pdf to help clarify, and have also linked the funnannotate documentation. 6. On NCBI I see that an additional Acropora pulchra genome has just been made available (29th Jan 2025), with this to the chromosome level (https://www.ncbi.nlm.nih.gov/datasets/genome/GCA_965118205.1/). I think it would be prudent to include this assemblies statistics in your Table 1, and also run a BUSCO analysis on this other assembly to compare with your one. While they got to chromosome level, you do have markedly less contigs. I do not think this is necessary for this manuscript, but future work you could look to use their chromosome assembly to get your scaffolded assembly to chromosome level. Again, I want to say this is a wonderful resource for the coral and wider scientific community, and the pipeline for de-novo assembly and annotation is best practices in my opinion. Annotated additional file: https://gigabyte-review.rivervalleytechnologies.comdownload-api-file?ZmlsZV9wYXRoPXVwbG9hZHMvZ3gvRFIvNTk0L2Nvbm5ldGFsMjAyNV9yZXZpZXdjb21tZW50cy5wZGY=

Re-review:

The authors have addressed all my comments and queries, and included nearly all recommendations. Thank you ! A few quick notes to fix before publication -

"The input created Funannotate train uses Trinity v.2.15.2 [22] and PASA v.2.5.3 [23] for transcript assembly prior to ab initio predictions". This sentence reads weird, reword before publishing. I think maybe just remove "created Funannotate train" and then it reads correctly. Or "Funnannotate trains uses .....". - "PFAM v.37.0 [28], CAZyme [29], UniProtKB v[30] and GO [31]." Missing a few version numbers, and UniProt just has a v. - "The mitochondrial genome was successfully assembled and circularized using MitoHifi v3.2.2 The final assembled A. pulchra mitogenome is". Just missing a period i think before "The final assembly". Great job and a very useful resource for the coral community !!

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

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Reply to the reviewers

We thank the reviewers for their feedback on our paper. We have taken all their comments into account in revising the manuscript. We provide a point-by-point response to their comments, below.

Reviewer #1

Major comments:

The manuscript is clearly written with a level of detail that allows others to reproduce the imaging and cell-tracking pipeline. Of the 22 movies recorded one was used for cell tracking. One movie seems sufficient for the second part of the manuscript, as this manuscript presents a proof-of-principle pipeline for an imaging experiment followed by cell tracking and molecular characterisation of the cells by HCR. In addition, cell tracking in a 5-10 day time-lapse movie is an enormous time commitment.

My only major comment is regarding "Suppl_data_5_spineless_tracking". The image file does not load. It looks like the wrong file is linked to the mastodon dataset. The "Current BDV dataset path" is set to "Beryl_data_files/BLB mosaic cut movie-02.xml", but this file does not exist in the folder. Please link it to the correct file.

We have corrected the file path in the updated version of Suppl. Data 5.

Minor comments:

The authors state that their imaging settings aim to reduce photo damage. Do they see cell death in the regenerating legs? Is the cell death induced by the light exposure or can they tell if the same cells die between the movies? That is, do they observe cell death in the same phases of regeneration and/or in the same regions of the regenerating legs?

Yes, we observe cell death during Parhyale leg regeneration. We have added the following sentence to explain this in the revised manuscript: "During the course of regeneration some cells undergo apoptosis (reported in Alwes et al., 2016). Using the H2B-mRFPruby marker, apoptotic cells appear as bright pyknotic nuclei that break up and become engulfed by circulating phagocytes (see bright specks in Figure 2F)."

We now also document apoptosis in regenerated legs that have not been subjected to live imaging in a new supplementary figure (Suppl. Figure 3), and we refer to these observations as follows: "While some cell death might be caused by photodamage, apoptosis can also be observed in similar numbers in regenerating legs that have not been subjected to live imaging (Suppl. Figure 3)."

Based on 22 movies, the authors divide the regeneration process into three phases and they describe that the timing of leg regeneration varies between individuals. Are the phases proportionally the same length between regenerating legs or do the authors find differences between fast/slow regenerating legs? If there is a difference in the proportions, why might this be?

Both early and late phases contribute to variation in the speed of regeneration, but there is no clear relationship between the relative duration of each phase and the speed of regeneration. We now present graphs supporting these points in a new supplementary figure (Suppl. Figure 2).

To clarify this point, we have added the following sentence in the manuscript: "We find that the overall speed of leg regeneration is determined largely by variation in the speed of the early (wound closure) phase of regeneration, and to a lesser extent by variation in later phases when leg morphogenesis takes place (Suppl. Figure 2 A,B). There is no clear relationship between the relative duration of each phase and the speed of regeneration (Suppl. Figure 2 A',B')."

Based on their initial cell tracing experiment, could the authors elaborate more on what kind of biological information can be extracted from the cell lineages, apart from determining which is the progenitor of a cell? What does it tell us about the cell population in the tissue? Is there indication of multi- or pluripotent stem cells? What does it say about the type of regeneration that is taking place in terms of epimorphosis and morphallaxis, the old concepts of regeneration?

In the first paragraph of Future Directions we describe briefly the kind of biological information that could be gained by applying our live imaging approach with appropriate cell-type markers (see below). We do not comment further, as we do not currently have this information at hand. Regarding the concepts of epimorphosis and morphallaxis, as we explain in Alwes et al. 2016, these terms describe two extreme conditions that do not capture what we observe during Parhyale leg regeneration. Our current work does not bring new insights on this topic.

Page 5. The authors mention the possibility of identifying the cell ID based on transcriptomic profiling data. Can they suggest how many and which cell types they expect to find in the last stage based on their transcriptomic data?

We have added this sentence: "Using single-nucleus transcriptional profiling, we have identified approximately 15 transcriptionally-distinct cell types in adult Parhyale legs (Almazán et al., 2022), including epidermis, muscle, neurons, hemocytes, and a number of still unidentified cell types."

Page 6. Correction: "..molecular and other makers.." should be "..molecular and other markers.."

Corrected

Page 8. The HCR in situ protocol probably has another important advantage over the conventional in situ protocol, which is not mentioned in this study. The hybridisation step in HCR is performed at a lower temperature (37˚C) than in conventional in situ hybridisation (65˚C, Rehm et al., 2009). In other organisms, a high hybridisation temperature affects the overall tissue morphology and cell location (tissue shrinkage). A lower hybridisation temperature has less impact on the tissue and makes manual cell alignment between the live imaging movie and the fixed HCR in situ stained specimen easier and more reliable. If this is also the case in Parhyale, the authors must mention it.

This may be correct, but all our specimens were treated at 37˚C, so we cannot assess whether hybridisation temperature affects morphological preservation in our specimens.

Page 9. The authors should include more information on the spineless study. What been is spineless? What do the cell lineages tell about the spineless progenitors, apart from them being spread in the tissue at the time of amputation? Do spineless progenitors proliferate during regeneration? Do any spineless expressing cells share a common progenitor cell?

We now point out that spineless encodes a transcription factor. We provide a summary of the lineages generating spineless-expressing cells in Suppl. Figure 6, and we explain that "These epidermal progenitors undergo 0, 1 or 2 cell divisions, and generate mostly spineless-expressing cells (Suppl. Figure 5)."

Page 10. Regarding the imaging temperature, the Materials and Methods state "... a temperature control chamber set to 26 or 27˚C..."; however, in Suppl. Data 1, 26˚C and 29˚C are indicated as imaging temperatures. Which is correct?

We corrected the Methods by adding "with the exception of dataset li51, imaged at 29{degree sign}C"

Page 10. Regarding the imaging step size, the Materials and Methods state "...step size of 1-2.46 µm..."; however, Suppl. Data 1 indicate a step size between 1.24 - 2.48 µm. Which is correct?

We corrected the Methods.

Page 11. Correct "...as the highest resolution data..." to "...at the highest resolution data..."

The original text is correct ("standardised to the same dimensions as the highest resolution data").

Page 11. Indicate which supplementary data set is referred to: "Using Mastodon, we generated ground truth annotations on the original image dataset, consisting of 278 cell tracks, including 13,888 spots and 13,610 links across 55 time points (see Supplementary Data)."

Corrected

p. 15. Indicate which supplementary data set is referred to: "In this study we used HCR probes for the Parhyale orthologues of futsch (MSTRG.441), nompA (MSTRG.6903) and spineless (MSTRG.197), ordered from Molecular Instruments (20 oligonucleotides per probe set). The transcript sequences targeted by each probe set are given in the Supplementary Data."

Corrected

Figure 3. Suggestion to the overview schematics: The authors might consider adding "molting" as the end point of the red bar (representing differentiation).

The time of molting is not known in the majority of these datasets, because the specimens were fixed and stained prior to molting. We added the relevant information in the figure legend: "Datasets li-13 and li-16 were recorded until the molt; the other recordings were stopped before molting."

Figure 4B': Please indicate that the nuclei signal is DAPI.

Corrected

Supplementary figure 1A. Word is missing in the figure legend: ...the image also shows weak...

Corrected

Supplementary Figure 2: Please indicate the autofluorescence in the granular cells. Does it correspond to the yellow cells?

Corrected

Video legend for video 1 and 2. Please correct "H2B-mREFruby" to "H2B-mRFPruby".

Corrected

Reviewer #2

Major comments:

MC 1. Given that most of the technical advances necessary to achieve the work described in this manuscript have been published previously, it would be helpful for the authors to more clearly identify the primary novelty of this manuscript. The abstract and introduction to the manuscript focus heavily on the technical details of imaging and analysis optimization and some additional summary of the implications of these advances should be included here to aid the reader.

This paper describes a technical advance. While previous work (Alwes et al. 2016) established some key elements of our live imaging approach, we were not at that time able to record the entire time course of leg regeneration (the longest recordings were 3.5 days long). Here we present a method for imaging the entire course of leg regeneration (up to 10 days of imaging), optimised to reduce photodamage and to improve cell tracking. We also develop a method of in situ staining in cuticularised adult legs (an important technical breakthrough in this experimental system), which we combine with live imaging to determine the fate of tracked cells. We have revised the abstract and introduction of the paper to point out these novelties, in relation to our previous publications.

In the abstract we explain: "Building on previous work that allowed us to image different parts of the process of leg regeneration in the crustacean Parhyale hawaiensis, we present here a method for live imaging that captures the entire process of leg regeneration, spanning up to 10 days, at cellular resolution. Our method includes (1) mounting and long-term live imaging of regenerating legs under conditions that yield high spatial and temporal resolution but minimise photodamage, (2) fixing and in situ staining of the regenerated legs that were imaged, to identify cell fates, and (3) computer-assisted cell tracking to determine the cell lineages and progenitors of identified cells. The method is optimised to limit light exposure while maximising tracking efficiency."

The introduction includes the following text: "Our first systematic study using this approach presented continuous live imaging over periods of 2-3 days, capturing key events of leg regeneration such as wound closure, cell proliferation and morphogenesis of regenerating legs with single-cell resolution (Alwes et al., 2016). Here, we extend this work by developing a method for imaging the entire course of leg regeneration, optimised to reduce photodamage and to improve cell tracking. We also develop a method of in situ staining of gene expression in cuticularised adult legs, which we combine with live imaging to determine the fate of tracked cells."

MC 2. The description of the regeneration time course is nicely detailed but also very qualitative. A major advantage of continuous recording and automated cell tracking in the manner presented in this manuscript would be to enable deeper quantitative characterization of cellular and tissue dynamics during regeneration. Rather than providing movies and manually annotated timelines, some characterization of the dynamics of the regeneration process (the heterogeneity in this is very very interesting, but not analyzed at all) and correlating them against cellular behaviors would dramatically increase the impact of the work and leverage the advances presented here. For example, do migration rates differ between replicates? Division rates? Division synchrony? Migration orientation? This seems to be an incredibly rich dataset that would be fascinating to explore in greater detail, which seems to me to be the primary advance presented in this manuscript. I can appreciate that the authors may want to segregate some biological findings from the method, but I believe some nominal effort highlighting the quantitative nature of what this method enables would strengthen the impact of the paper and be useful for the reader. Selecting a small number of simple metrics (eg. Division frequency, average cell migration speed) and plotting them alongside the qualitative phases of the regeneration timeline that have already been generated would be a fairly modest investment of effort using tools that already exist in the Mastodon interface, I would roughly estimate on the order of an hour or two per dataset. I believe that this effort would be well worth it and better highlight a major strength of the approach.

The primary goal of this work was to establish a robust method for continuous long-term live imaging of regeneration, but we do appreciate that a more quantitative analysis would add value to the data we are presenting. We tried to address this request in three steps:

First, we examined whether clear temporal patterns in cell division, cell movements or other cellular features can be observed in an accurately tracked dataset (li13-t4, tracked in Sugawara et al. 2022). To test this we used the feature extraction functions now available on the Mastodon platform (see link). We could discern a meaningful temporal pattern for cell divisions (see below); the other features showed no interpretable pattern of variation.

Second, we asked whether we could use automated cell tracking to analyse the patterns of cell division in all our datasets. Using an Elephant deep learning model trained on the tracks of the li13-t4 dataset, we performed automated cell tracking in the same dataset, and compared the pattern of cell divisions from the automated cell track predictions with those coming from manually validated cell tracks. We observed that the automated tracks gave very imprecise results, with a high background of false positives obscuring the real temporal pattern (see images below, with validated data on the left, automated tracking on the right). These results show that the automated cell tracking is not accurate enough to provide a meaningful picture on the pattern of cell divisions.

Third, we tried to improve the accuracy of detection of dividing cells by additional training of Elephant models on each dataset (to lower the rate of false positives), followed by manual proofreading. Given how labour intensive this is, we could only apply this approach to 4 additional datasets. The results of this analysis are presented in Figure 4.

MC 3. The authors describe the challenges faced by their described approach: Using this mode of semi-automated and manual cell tracking, we find that most cells in the upper slices of our image stacks (top 30 microns) can be tracked with a high degree of confidence. A smaller proportion of cell lineages are trackable in the deeper layers.

Given that the authors quantify this in Table 1, it would aid the reader to provide metrics in the manuscript text at this point. Furthermore, the metrics provided in Table 1 appear to be for overall performance, but the text describes that performance appears to be heavily depth dependent. Segregating the performance metrics further, for example providing DET, TRA, precision and recall for superficial layers only and for the overall dataset, would help support these arguments and better highlight performance a potential adopter of the method might expect.

In the revised manuscript we have added data on the tracking performance of Elephant in relation to imaging depth in Suppl. Figure 3. These data confirm our original statement (which was based on manual tracking) that nuclei are more challenging to track in deeper layers.

We point to these new results in two parts of the paper, as follows: "A smaller proportion of cells are trackable in the deeper layers (see Suppl. Figure 3)", and "Our results, summarised in Table 1A, show that the detection of nuclei can be enhanced by doubling the z resolution at the expense of xy resolution and image quality. This improvement is particularly evident in the deeper layers of the imaging stacks, which are usually the most challenging to track (Suppl. Figure 3)."

MC 4. Performance characterization in Table 1 appears to derive from a single dataset that is then subsampled and processed in different ways to assess the impact of these changes on cell tracking and detection performance. While this is a suitable strategy for this type of optimization it leaves open the question of performance consistency across datasets. I fully recognize that this type of quantification can be onerous and time consuming, but some attempt to assess performance variability across datasets would be valuable. Manual curation over a short time window over a random sampling of the acquired data would be sufficient to assess this.

We think that similar trade-offs will apply to all our datasets because tracking performance is constrained by the same features, which are intrinsic to our system; e.g. by the crowding of nuclei in relation to axial resolution, or the speed of mitosis in relation to the temporal resolution of imaging. We therefore do not see a clear rationale for repeating this analysis. On a practical level, our existing image datasets could not be subsampled to generate the various conditions tested in Table 1, so proving this point experimentally would require generating new recordings, and tracking these to generate ground truth data. This would require months of additional work.

A second, related question is whether Elephant would perform equally well in detecting and tracking nuclei across different datasets. This point has been addressed in the Sugawara et al. 2022 paper, where the performance of Elephant was tested on diverse fluorescence datasets.

Reviewer #3

Major comments:

The authors should clearly specify what are the key technical improvements compared to their previous studies (Alwes et al. 2016, Elife; Konstantinides & Averof 2014, Science). There, the approaches for mounting, imaging, and cell tracking are already introduced, and the imaging is reported to run for up to 7 days in some cases.

In Konstantinides and Averof (2014) we did not present any live imaging at cellular resolution. In Alwes et al. (2016) we described key elements of our live imaging approach, but we were never able to record the entire time course of leg regeneration. The longest recordings in that work were 3.5 days long.

We have revised the abstract and introduction to clarify the novelty of this work, in relation to our previous publications. Please see our response to comment MC1 of reviewer 2.

While the authors mention testing the effect of imaging parameters (such as scanning speed and line averaging) on the imaging/tracking outcome, very little or no information is provided on how this was done beyond the parameters that they finally arrived to.

Scan speed and averaging parameters were determined by measuring contrast and signal-to-noise ratios in images captured over a range of settings. We have now added these data in Supplementary Figure 1.

The authors claim that, using the acquired live imaging data across entire regeneration time course, they are now able to confirm and extend their description of leg regeneration. However, many claims about the order and timing of various cellular events during regeneration are supported only by references to individual snapshots in figures or supplementary movies. Presenting a more quantitative description of cellular processes during regeneration from the acquired data would significantly enhance the manuscript and showcase the usefulness of the improved workflow.

The events we describe can be easily observed in the maximum projections, available in Suppl. Data 2. Regarding the quantitative analysis, please see our response to comment MC2 of reviewer 2.

Table 1 summarizes the performance of cell tracking using simulated datasets of different quality. However only averages and/or maxima are given for the different metrics, which makes it difficult to evaluate the associated conclusions. In some cases, only 1 or 2 test runs were performed.

The metrics extracted from each of the three replicates, per dataset, are now included in Suppl. Data 4.

We consistently used 3 replicates to measure tracking performance with each of the datasets. The "replicates" column label in Table 1 referred to the number of scans that were averaged to generate the image, not to the replicates used for estimating the tracking performance. To avoid confusion, we changed that label to "averaging".

OPTIONAL: An imaging approach that allows using the current mounting strategy but could help with some of the tradeoffs is using a spinning-disk confocal microscope instead of a laser scanning one. If the authors have such a system available, it could be interesting to compare it with their current scanning confocal setup.

Preliminary experiments that we carried out several years ago on a spinning disk confocal (with a 20x objective and the CSU-W1 spinning disk) were not very encouraging, and we therefore did not pursue this approach further. The main problem was bad image quality in deeper tissue layers.

Minor comments:

The presented imaging protocol was optimized for one laser wavelength only (561 nm) - this should be mentioned when discussing the technical limitations since animals tend to react differently to different wavelengths. Same settings might thus not be applicable for imaging a different fluorescent protein.

In the second paragraph of the Results section, we explain that we perform the imaging at long wavelengths in order to minimise photodamage. It should be clear to the readers that changing the excitation wavelength will have an impact for long-term live imaging.

For transferability, it would be useful if the intensity of laser illumination was measured and given in the Methods, instead of just a relative intensity setting from the imaging software. Similarly,more details of the imaging system should be provided where appropriate (e.g., detector specifications).

We have now measured the intensity of the laser illumination and added this information in the Methods: "Laser power was typically set to 0.3% to 0.8%, which yields 0.51 to 1.37 µW at 561 nm (measured with a ThorLabs Microscope Slide Power Sensor, #S170C)."

Regarding the imaging system and the detector, we provide all the information that is available to us on the microscope's technical sheets.

The versions of analysis scripts associated with the manuscript should be uploaded to an online repository that permanently preserves the respective version.

The scripts are now available on gitbub and online repositories. The relevant links are included in the revised manuscript.

Welcome back, and in this lesson, I want to cover EC2 purchase options. EC2 purchase options are often referred to as launch types, but the official way to refer to them from AWS is purchase options, and so to be consistent, I think it's worth focusing on that name. So, EC2 purchase options. Let's step through all of the main types with a focus on the situations where you would and wouldn't use each of them. So, let's jump in and get started.

The first purchase option that I want to talk about is the default, which is on demand, and on demand is simple to explain because it's entirely unremarkable in every way. It's the default because it's the average of anything with no specific pros or cons. Now, the way that it works, let's start with two EC2 hosts. Obviously, AWS has more, but it's easy to diagram with just the two. Now, instances of different sizes when launched using on demand will run on these EC2 hosts, and different AWS customers, they're all mixed up on the shared pool of EC2 hosts. So, even though instances are isolated and protected, different AWS customers launch instances which share the same pool of underlying hardware. This means that AWS can efficiently allocate resources, which is why the starting price for on demand in EC2 is so reasonable.

In terms of the price, on demand uses per second billing, and this happens while instances are running, so you're paying for the resources that you consume. If you shut an instance down logically, you don't pay for those resources. Other associated services such as storage, which do consume resources regardless of if the instance is running or in a shutdown state, do charge constantly while those resources are being consumed. So, remember this: while instances only charge while in the running state, other associated resources may charge regardless. This is how on demand works, but what types of situations should it be used for? Well, it's the default purchase option, and so you should always start your evaluation process by considering on demand as your default. For all projects, assume on demand and move to something else if you can justify that alternative purchase option.

With on demand, there are no interruptions. You launch an instance, you pay a per second charge, and barring any failures, the instance runs until you decide otherwise. You don't receive any capacity reservations with on demand. If AWS has a major failure and capacity is limited, the reserved purchase option receives highest provisioning priority on whatever capacity remains, and so if something is critical to your business, then you should consider an alternative rather than using on demand. So, on demand does not give you any priority access to remaining capacity if there are any major failures.

On demand offers predictable pricing, it's defined upfront, you pay a constant price, but there are no specific discounts. This consistent pricing applies to the duration that you use instances. So, on demand is suitable for short term workloads. Anything which you just need to provision, perform a workload and then terminate is ideal for on demand. If you're unsure about the duration or the type of workload, then again, on demand is ideal. And then lastly, if you have short term or unknown workloads, which definitely can't tolerate any interruption, then on demand is the perfect purchase option.

Next, let's talk about spot pricing, and spot is the cheapest way to get access to EC2 capacity. Let's look at how this works visually. Let's start with the same two EC2 hosts. On the left, we have A and on the right B. Then, on these EC2 hosts, we're currently running four EC2 instances, two per host. And let's assume for this example that all of these four instances are using the on demand purchase option. So, right now, with what you see on screen, the hosts are wasting capacity. Enough capacity for four additional instances on each host is being wasted. Spot pricing is AWS selling that spare capacity at a discounted rate.

The way that it works is that within each region for each type of instance, there is a given amount of free capacity on EC2 hosts at any time. AWS tracks this and it publishes a price for how much it costs to use that capacity, and this price is the spot price. Now, you can offer to pay more than the spot price, but this is a maximum. You'll only ever pay the current spot price for the type of instance in the specific region where you provision services. So, let's say that there are two different customers who want to provision four instances each. The first customer sets a maximum price of four gold coins, and the other customer sets a maximum price of two gold coins. Now, obviously, AWS doesn't charge in gold coins, and there are more than two EC2 hosts, but it's just easier to represent it in this way.

Now, because the current spot price set by AWS is only two gold coins, then both customers are only paying two gold coins a second for their instances. Even though customer one has offered to pay more, this is their maximum and they only ever pay the current spot price. So, let's say now that the free capacity is getting a little bit on the low side. AWS are getting nervous, they know that they need to free up capacity for the normal on demand instances, which they know are about to launch, and so they up the spot price to four gold coins. Now, customer one is fine because they've set a maximum price of four coins, and so now they start paying four coins because that's what the current spot price is. Customer two, they've set their maximum price at two coins, and so their instances are terminated.

If the spot price goes above your maximum price, then any spot instances which you have are terminated. That's the critical part to understand because spot instances should not be viewed as reliable. At this point in our example, maybe another customer decides to launch four on demand instances. AWS sell that capacity at the normal on demand rates, which are higher, and no capacity is wasted. Spot pricing offers up to a 90% reduction versus the price of on demand, and there are some significant trade offs that you need to be aware of.

You should never use the spot purchase option for workloads which can't tolerate interruptions. No matter how well you manage your maximum spot price, there are going to be periods when instances are terminated. If you run workloads where that's a problem, don't use spot. This means that workloads such as domain controllers, mail servers, traditional websites, or even flight control systems are all bad fits for spot instances. The types of scenarios which are good fits for using spot instances are things which are not time critical. Since the spot price changes throughout each day and throughout days of the week, if you're able to process workloads around this, then you can take advantage of the maximum cost benefits for using spot. Anything which can tolerate interruption and just rerun is ideal for spot instances.

So, if you have highly parallel workloads which can be broken into hundreds or thousands of pieces, maybe scientific analysis, and if any parts which fail can be rerun, then spot is ideal. Anything which has a bursty capacity need, maybe media processing, image processing, any cost sensitive workloads which wouldn't be economical to do using normal on-demand instances, assuming they can tolerate interruption, these are ideal for spot. Anything which is stateless where the state of the user session is not stored on the instances themselves, meaning they can handle disruption, again, ideal for using spot. Don't use spot for anything that's long-term, anything that requires consistent, reliable compute, any business critical things, or things which cannot tolerate disruption. For those type of workloads, you should not use spot. It's an anti-pattern.

OK, so this is the end of part one of this lesson. It was getting a little bit on the long side, and I wanted to give you the opportunity to take a small break, maybe stretch your legs or make a coffee. Now, part two will continue immediately from this point, so go ahead, complete this video, and when you're ready, I look forward to you joining me in part two.

Welcome back. In this lesson, now that we've covered virtualization at a high level, I want to focus on the architecture of the EC2 product in more detail. EC2 is one of the services you'll use most often in AWS since one which features on a lot of exam questions, so let's get started.

First thing, let's cover some key, high level architectural points about EC2. EC2 instances are virtual machines, so this means an operating system plus an allocation of resources such as virtual CPU, memory, potential some local storage, maybe some network storage, and access to other hardware such as networking and graphics processing units. EC2 instances run on EC2 hosts, and these are physical servers hardware which AWS manages. These hosts are either shared hosts or dedicated hosts.

Shared hosts are hosts which are shared across different AWS customers, so you don't get any ownership of the hardware and you pay for the individual instances based on how long you run them for and what resources they have allocated. It's important to understand, though, that every customer when using shared hosts are isolated from each other, so there's no visibility of it being shared, there's no interaction between different customers, even if you're using the same shared host, and shared hosts are the default.

With dedicated hosts, you're paying for the entire host, not the instances which run on it. It's yours, it's dedicated to your account, and you don't have to share it with any other customers. So if you pay for a dedicated host, you pay for that entire host, you don't pay for any instances running on it, and you don't share it with other AWS customers.

EC2 is an availability zone resilient service. The reason for this is that hosts themselves run inside a single availability zone, so if that availability zone fails, the hosts inside that availability zone could fail, and any instances running on any hosts that fail will themselves fail. So as a solutions architect, you have to assume if an AZ fails, then at least some and probably all of the instances that are running inside that availability zone will also fail or be heavily impacted.

Now let's look at how this looks visually. So this is a simplification of the US East One region, I've only got two AZs represented, AZA and AZB, and in AZA, I've represented that I've got two subnet, subnet A and subnet B. Now inside each of these availability zones is an EC2 host. Now these EC2 hosts, they run within a single AZ, I'm going to keep repeating that because it's critical for the exam and you're thinking about EC2 in the exam.

Keep thinking about it being an AZ resilient service, if you see EC2 mentioned in an exam, see if you can locate the availability zone details because that might factor into the correct answer. Now EC2 hosts have some local hardware, logically CPU and memory, which you should be aware of, but also they have some local storage called the instance store. The instance store is temporary, if an instance is running on a particular host, depending on the type of the instance, it might be able to utilize this instance store, but if the instance moves off this host to another one, then that storage is lost.

And they also have two types of networking, storage networking and data networking. When instances are provisioned into a specific subnet within a VPC, what's actually happening is that a primary elastic network interface is provisioned in a subnet, which maps to the physical hardware on the EC2 host. Remember, subnets are also in one specific availability zone. Instances can have multiple network interfaces, even in different subnets, as long as they're in the same availability zone. Everything about EC2 is focused around this architecture, the fact that it runs in one specific availability zone.

Now EC2 can make use of remote storage so an EC2 host can connect to the elastic block store, which is known as EBS. The elastic block store service also runs inside a specific availability zone, so the service running inside availability zone A is different than the one running inside availability zone B, and you can't access them cross zone. EBS lets you allocate volumes and volumes of portions of persistent storage, and these can be allocated to instances in the same availability zone, so again, it's another area where the availability zone matters.

What I'm trying to do by keeping repeating availability zone over and over again is to paint a picture of a service which is very reliant on the availability zone that it's running in. The host is in an availability zone, the network is per availability zone, the persistent storage is per availability zone, even availability zone in AWS experiences major issues, it impacts all of those things.

Now an instance runs on a specific host, and if you restart the instance, it will stay on a host. Instances stay on a host until one of two things happen: firstly, the host fails or is taken down for maintenance for some reason by AWS; or secondly, if an instance is stopped and then started, and that's different than just restarting, so I'm focusing on an instance being stopped and then being started, so not just a restart. If either of those things happen, then an instance will be relocated to another host, but that host will also be in the same availability zone.

Instances cannot natively move between availability zones. Everything about them, their hardware, networking and storage is locked inside one specific availability zone. Now there are ways you can do a migration, but it essentially means taking a copy of an instance and creating a brand new one in a different availability zone, and I'll be covering that later in this section where I talk about snapshots and AMIs.

What you can never do is connect network interfaces or EBS storage located in one availability zone to an EC2 instance located in another. EC2 and EBS are both availability zone services, they're isolated, you cannot cross AZs with instances or with EBS volumes. Now instances running on an EC2 host share the resources of that host. And instances of different sizes can share a host, but generally instances of the same type and generation will occupy the same host.

And I'll be talking in much more detail about instance types and sizes and generations in a lesson that's coming up very soon. But when you think about an EC2 host, think that it's from a certain year and includes a certain class of processor and a certain type of memory and a certain type and configuration of storage. And instances are also created with different generations, different versions that you apply specific types of CPU memory and storage, so it's logical that if you provision two different types of instances, they may well end up on two different types of hosts.

So a host generally has lots of different instances from different customers of the same type, but different sizes. So before we finish up this lesson, I want to answer a question. That question is what's EC2 good for? So what types of situations might you use EC2 for? And this is equally valuable when you're evaluating a technical architecture while you're answering questions in the exam.

So first, EC2 is great when you've got a traditional OS and application compute need, so if you've got an application that requires to be running on a certain operating system at a certain runtime with certain configuration, maybe your internal technical staff are used to that configuration, or maybe your vendor has a certain set of support requirements, EC2 is a perfect use case for this type of scenario.

And it's also great for any long running compute needs. There are lots of other services inside AWS that provide compute services, but many of these have got runtime limits, so you can't leave these things running consistently for one year or two years. With EC2, it's designed for persistent, long running compute requirements. So if you have an application that runs constantly 24/7, 365, and needs to be running on a normal operating system, Linux or Windows, then EC2 is the default and obvious choice for this.

If you have any applications, which is server style applications, so traditional applications they expect to be running in an operating system, waiting for incoming connections, then again, EC2 is a perfect service for this. And it's perfect for any applications or services that need burst requirements or steady state requirements. There are different types of EC2 instances, which are suitable for low levels of normal loads with occasional bursts, as well as steady state load.

So again, if your application needs an operating system, and it's not bursty needs or consistent steady state load, then EC2 should be the first thing that you review. EC2 is also great for monolithic application stack, so if your monolithic application requires certain components, a stack, maybe a database, maybe some middleware, maybe other runtime based components, and especially if it needs to be running on a traditional operating system, EC2 should be the first thing that you look at.

And EC2 is also ideally suited for migrating application workloads, so application workloads, which expect a traditional virtual machine or server style environment, or if you're performing disaster recovery. So if you have existing traditional systems which run on virtual servers, and you want to provision a disaster recovery environment, then EC2 is perfect for that.

In general, EC2 tends to be the default compute service within AWS. There are lots of niche requirements that you might have, and if you do have those, there are other compute services such as the elastic container service or Lambda. But generally, if you've got traditional style workloads, or you're looking for something that's consistent, or if it requires an operating system, or if it's monolithic, or if you migrated into AWS, then EC2 is a great default first option.

Now in this section of the course, I'm covering the basic architectural components of EC2, so I'm gonna be introducing the basics and let you get some exposure to it, and I'm gonna be teaching you all the things that you'll need for the exam.

Author response:

The following is the authors’ response to the original reviews

eLife Assessment

Examination of (a)periodic brain activity has gained particular interest in the last few years in the neuroscience fields relating to cognition, disorders, and brain states. Using large EEG/MEG datasets from younger and older adults, the current study provides compelling evidence that age-related differences in aperiodic EEG/MEG signals can be driven by cardiac rather than brain activity. Their findings have important implications for all future research that aims to assess aperiodic neural activity, suggesting control for the influence of cardiac signals is essential.

We want to thank the editors for their assessment of our work and highlighting its importance for the understanding of aperiodic neural activity. Additionally, we want to thank the three present and four former reviewers (at a different journal) whose comments and ideas were critical in shaping this manuscript to its current form. We hope that this paper opens up many more questions that will guide us - as a field - to an improved understanding of how “cortical” and “cardiac” changes in aperiodic activity are linked and want to invite readers to engage with our work through eLife’s comment function.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The present study addresses whether physiological signals influence aperiodic brain activity with a focus on age-related changes. The authors report age effects on aperiodic cardiac activity derived from ECG in low and high-frequency ranges in roughly 2300 participants from four different sites. Slopes of the ECGs were associated with common heart variability measures, which, according to the authors, shows that ECG, even at higher frequencies, conveys meaningful information. Using temporal response functions on concurrent ECG and M/EEG time series, the authors demonstrate that cardiac activity is instantaneously reflected in neural recordings, even after applying ICA analysis to remove cardiac activity. This was more strongly the case for EEG than MEG data. Finally, spectral parameterization was done in large-scale resting-state MEG and ECG data in individuals between 18 and 88 years, and age effects were tested. A steepening of spectral slopes with age was observed particularly for ECG and, to a lesser extent, in cleaned MEG data in most frequency ranges and sensors investigated. The authors conclude that commonly observed age effects on neural aperiodic activity can mainly be explained by cardiac activity.

Strengths:

Compared to previous investigations, the authors demonstrate the effects of aging on the spectral slope in the currently largest MEG dataset with equal age distribution available. Their efforts of replicating observed effects in another large MEG dataset and considering potential confounding by ocular activity, head movements, or preprocessing methods are commendable and valuable to the community. This study also employs a wide range of fitting ranges and two commonly used algorithms for spectral parameterization of neural and cardiac activity, hence providing a comprehensive overview of the impact of methodological choices. Based on their findings, the authors give recommendations for the separation of physiological and neural sources of aperiodic activity.

Weaknesses:

While the aim of the study is well-motivated and analyses rigorously conducted, the overall structure of the manuscript, as it stands now, is partially misleading. Some of the described results are not well-embedded and lack discussion.

We want to thank the reviewer for their comments focussed on improving the overall structure of the manuscript. We agree with their suggestions that some results could be more clearly contextualized and restructured the manuscript accordingly.

Reviewer #2 (Public review):

I previously reviewed this important and timely manuscript at a previous journal where, after two rounds of review, I recommended publication. Because eLife practices an open reviewing format, I will recapitulate some of my previous comments here, for the scientific record.

In that previous review, I revealed my identity to help reassure the authors that I was doing my best to remain unbiased because I work in this area and some of the authors' results directly impact my prior research. I was genuinely excited to see the earlier preprint version of this paper when it first appeared. I get a lot of joy out of trying to - collectively, as a field - really understand the nature of our data, and I continue to commend the authors here for pushing at the sources of aperiodic activity!

In their manuscript, Schmidt and colleagues provide a very compelling, convincing, thorough, and measured set of analyses. Previously I recommended that the push even further, and they added the current Figure 5 analysis of event-related changes in the ECG during working memory. In my opinion this result practically warrants a separate paper its own!

The literature analysis is very clever, and expanded upon from any other prior version I've seen.

In my previous review, the broadest, most high-level comment I wanted to make was that authors are correct. We (in my lab) have tried to be measured in our approach to talking about aperiodic analyses - including adopting measuring ECG when possible now - because there are so many sources of aperiodic activity: neural, ECG, respiration, skin conductance, muscle activity, electrode impedances, room noise, electronics noise, etc. The authors discuss this all very clearly, and I commend them on that. We, as a field, should move more toward a model where we can account for all of those sources of noise together. (This was less of an action item, and more of an inclusion of a comment for the record.)

I also very much appreciate the authors' excellent commentary regarding the physiological effects that pharmacological challenges such as propofol and ketamine also have on non-neural (autonomic) functions such as ECG. Previously I also asked them to discuss the possibility that, while their manuscript focuses on aperiodic activity, it is possible that the wealth of literature regarding age-related changes in "oscillatory" activity might be driven partly by age-related changes in neural (or non-neural, ECG-related) changes in aperiodic activity. They have included a nice discussion on this, and I'm excited about the possibilities for cognitive neuroscience as we move more in this direction.

Finally, I previously asked for recommendations on how to proceed. The authors convinced me that we should care about how the ECG might impact our field potential measures, but how do I, as a relative novice, proceed. They now include three strong recommendations at the end of their manuscript that I find to be very helpful.

As was obvious from previous review, I consider this to be an important and impactful cautionary report, that is incredibly well supported by multiple thorough analyses. The authors have done an excellent job responding to all my previous comments and concerns and, in my estimation, those of the previous reviewers as well.

We want to thank the reviewer for agreeing to review our manuscript again and for recapitulating on their previous comments and the progress the manuscript has made over the course of the last ~2 years. The reviewer's comments have been essential in shaping the manuscript into its current form. Their feedback has made the review process truly feel like a collaborative effort, focused on strengthening the manuscript and refining its conclusions and resulting recommendations.

Reviewer #3 (Public review):

Summary:

Schmidt et al., aimed to provide an extremely comprehensive demonstration of the influence cardiac electromagnetic fields have on the relationship between age and the aperiodic slope measured from electroencephalographic (EEG) and magnetoencephalographic (MEG) data.

Strengths:

Schmidt et al., used a multiverse approach to show that the cardiac influence on this relationship is considerable, by testing a wide range of different analysis parameters (including extensive testing of different frequency ranges assessed to determine the aperiodic fit), algorithms (including different artifact reduction approaches and different aperiodic fitting algorithms), and multiple large datasets to provide conclusions that are robust to the vast majority of potential experimental variations.

The study showed that across these different analytical variations, the cardiac contribution to aperiodic activity measured using EEG and MEG is considerable, and likely influences the relationship between aperiodic activity and age to a greater extent than the influence of neural activity.

Their findings have significant implications for all future research that aims to assess aperiodic neural activity, suggesting control for the influence of cardiac fields is essential.

We want to thank the reviewer for their thorough engagement with our work and the resultant substantive amount of great ideas both mentioned in the section of Weaknesses and Authors Recommendations below. Their suggestions have sparked many ideas in us on how to move forward in better separating peripheral- from neuro-physiological signals that are likely to greatly influence our future attempts to better extract both cardiac and muscle activity from M/EEG recordings. So we want to thank them for their input, time and effort!

Weaknesses:

Figure 4I: The regressions explained here seem to contain a very large number of potential predictors. Based on the way it is currently written, I'm assuming it includes all sensors for both the ECG component and ECG rejected conditions?

I'm not sure about the logic of taking a complete signal, decomposing it with ICA to separate out the ECG and non-ECG signals, then including these latent contributions to the full signal back into the same regression model. It seems that there could be some circularity or redundancy in doing so. Can the authors provide a justification for why this is a valid approach?

After observing significant effects both in the MEG_{ECG component} and MEG_{ECG rejected} conditions in similar frequency bands we wanted to understand whether or not these age-related changes are statistically independent. To test this we added both variables as predictors in a regression model (thereby accounting for the influence of the other in relation to age). The regression models we performed were therefore actually not very complex. They were built using only two predictors, namely the data (in a specific frequency range) averaged over channels on which we noticed significant effects in the ECG rejected and ECG components data respectively (Wilkinson notation: age ~ 1 + ECG rejected + ECG components). This was also described in the results section stating that: “To see if MEG_{ECG rejected} and MEG_{ECG component} explain unique variance in aging at frequency ranges where we noticed shared effects, we averaged the spectral slope across significant channels and calculated a multiple regression model with MEG_{ECG component} and MEG_{ECG rejected} as predictors for age (to statistically control for the effect of MEG_{ECG component}s and MEG_{ECG rejected} on age). This analysis was performed to understand whether the observed shared age-related effects (MEG_{ECG rejected} and MEG_{ECG component}) are in(dependent).”  

We hope this explanation solves the previous misunderstanding.

I'm not sure whether there is good evidence or rationale to support the statement in the discussion that the presence of the ECG signal in reference electrodes makes it more difficult to isolate independent ECG components. The ICA algorithm will still function to detect common voltage shifts from the ECG as statistically independent from other voltage shifts, even if they're spread across all electrodes due to the referencing montage. I would suggest there are other reasons why the ICA might lead to imperfect separation of the ECG component (assumption of the same number of source components as sensors, non-Gaussian assumption, assumption of independence of source activities).

The inclusion of only 32 channels in the EEG data might also have reduced the performance of ICA, increasing the chances of imperfect component separation and the mixing of cardiac artifacts into the neural components, whereas the higher number of sensors in the MEG data would enable better component separation. This could explain the difference between EEG and MEG in the ability to clean the ECG artifact (and perhaps higher-density EEG recordings would not show the same issue).

The reviewer is making a good argument suggesting that our initial assumption that the presence of cardiac activity on the reference electrode influences the performance of the ICA may be wrong. After rereading and rethinking upon the matter we think that the reviewer is correct and that their assumptions for why the ECG signal was not so easily separable from our EEG recordings are more plausible and better grounded in the literature than our initial suggestion. We therefore now highlight their view as a main reason for why the ECG rejection was more challenging in EEG data. However, we also note that understanding the exact reason probably ends up being an empirical question that demands further research stating that:

“Difficulties in removing ECG related components from EEG signals via ICA might be attributable to various reasons such as the number of available sensors or assumptions related to the non-gaussianity of the underlying sources. Further understanding of this matter is highly important given that ICA is the most widely used procedure to separate neural from peripheral physiological sources. ”

In addition to the inability to effectively clean the ECG artifact from EEG data, ICA and other component subtraction methods have also all been shown to distort neural activity in periods that aren't affected by the artifact due to the ubiquitous issue of imperfect component separation (https://doi.org/10.1101/2024.06.06.597688). As such, component subtraction-based (as well as regression-based) removal of the cardiac artifact might also distort the neural contributions to the aperiodic signal, so even methods to adequately address the cardiac artifact might not solve the problem explained in the study. This poses an additional potential confound to the "M/EEG without ECG" conditions.

The reviewer is correct in stating that, if an “artifactual” signal is not always present but appears and disappears (like e.g. eye-blinks) neural activity may be distorted in periods where the “artifactual” signal is absent. However, while this plausibly presents a problem for ocular activity, there is no obvious reason to believe that this applies to cardiac activity. While the ECG signal is non-stationary in nature, it is remarkably more stable than eye-movements in the healthy populations we analyzed (especially at rest). Therefore, the presence of the cardiac “artifact” was consistently present across the entirety of the MEG recordings we visually inspected.

Literature Analysis, Page 23: was there a method applied to address studies that report reducing artifacts in general, but are not specific to a single type of artifact? For example, there are automated methods for cleaning EEG data that use ICLabel (a machine learning algorithm) to delete "artifact" components. Within these studies, the cardiac artifact will not be mentioned specifically, but is included under "artifacts".

The literature analysis was largely performed automatically and solely focussed on ECG related activity as described in the methods section under Literature Analysis, if no ECG related terms were used in the context of artifact rejection a study was flagged as not having removed cardiac activity. This could have been indeed better highlighted by us and we apologize for the oversight on our behalf. We now additionally link to these details stating that:

“However, an analysis of openly accessible M/EEG articles (N_Articles=279; see Methods - Literature Analysis for further details) that investigate aperiodic activity revealed that only 17.1% of EEG studies explicitly mention that cardiac activity was removed and only 16.5% measure ECG (45.9% of MEG studies removed cardiac activity and 31.1% of MEG studies mention that ECG was measured; see Figure 1EF).”

The reviewer makes a fair point that there is some uncertainty here and our results probably present a lower bound of ECG handling in M/EEG research as, when I manually rechecked the studies that were not initially flagged in studies it was often solely mentioned that “artifacts” were rejected. However, this information seemed too ambiguous to assume that cardiac activity was in fact accounted for. However, again this could have been mentioned more clearly in writing and we apologize for this oversight. Now this is included as part of the methods section Literature Analysis stating that:

“All valid word contexts were then manually inspected by scanning the respective word context to ensure that the removal of “artifacts” was related specifically to cardiac and not e.g. ocular activity or the rejection of artifacts in general (without specifying which “artifactual” source was rejected in which case the manuscript was marked as invalid). This means that the results of our literature analysis likely present a lower bound for the rejection of cardiac activity in the M/EEG literature investigating aperiodic activity.”

Statistical inferences, page 23: as far as I can tell, no methods to control for multiple comparisons were implemented. Many of the statistical comparisons were not independent (or even overlapped with similar analyses in the full analysis space to a large extent), so I wouldn't expect strong multiple comparison controls. But addressing this point to some extent would be useful (or clarifying how it has already been addressed if I've missed something).

In the present study we tried to minimize the risk of type 1 errors by several means, such as A) weakly informative priors, B) robust regression models and C) by specifying a region of practical equivalence (ROPE, see Methods Statistical Inference for further Information) to define meaningful effects.

Weakly informative priors can lower the risk of type 1 errors arising from multiple testing by shrinking parameter estimates towards zero (see e.g. Lemoine, 2019). Robust regression models use a Student T distribution to describe the distribution of the data. This distribution features heavier tails, meaning it allocates more probability to extreme values, which in turn minimizes the influence of outliers. The ROPE criterion ensures that only effects exceeding a negligible size are considered meaningful, representing a strict and conservative approach to interpreting our findings (see Kruschke 2018, Cohen, 1988).

Furthermore, and more generally we do not selectively report “significant” effects in the situations in which multiple analyses were conducted on the same family of data (e.g. Figure 2 & 4). Instead we provide joint inference across several plausible analysis options (akin to a specification curve analysis, Simonsohn, Simmons & Nelson 2020) to provide other researchers with an overview of how different analysis choices impact the association between cardiac and neural aperiodic activity.

Lemoine, N. P. (2019). Moving beyond noninformative priors: why and how to choose weakly informative priors in Bayesian analyses. Oikos, 128(7), 912-928.

Simonsohn, U., Simmons, J. P., & Nelson, L. D. (2020). Specification curve analysis. Nature Human Behaviour, 4(11), 1208-1214.

Methods:

Applying ICA components from 1Hz high pass filtered data back to the 0.1Hz filtered data leads to worse artifact cleaning performance, as the contribution of the artifact in the 0.1Hz to 1Hz frequency band is not addressed (see Bailey, N. W., Hill, A. T., Biabani, M., Murphy, O. W., Rogasch, N. C., McQueen, B., ... & Fitzgerald, P. B. (2023). RELAX part 2: A fully automated EEG data cleaning algorithm that is applicable to Event-Related-Potentials. Clinical Neurophysiology, result reported in the supplementary materials). This might explain some of the lower frequency slope results (which include a lower frequency limit <1Hz) in the EEG data - the EEG cleaning method is just not addressing the cardiac artifact in that frequency range (although it certainly wouldn't explain all of the results).

We want to thank the reviewer for suggesting this interesting paper, showing that lower high-pass filters may be preferable to the more commonly used >1Hz high-pass filters for detection of ICA components that largely contain peripheral physiological activity. However, the results presented by Bailey et al. contradict the more commonly reported findings by other researchers that >1Hz high-pass filter is actually preferable (e.g. Winkler et al. 2015; Dimingen, 2020 or Klug & Gramann, 2021) and recommendations in widely used packages for M/EEG analysis (e.g. https://mne.tools/1.8/generated/mne.preprocessing.ICA.html). Yet, the fact that there seems to be a discrepancy suggests that further research is needed to better understand which type of high-pass filtering is preferable in which situation. Furthermore, it is notable that all the findings for high-pass filtering in ICA component detection and removal that we are aware of relate to ocular activity. Given that ocular and cardiac activity have very different temporal and spectral patterns it is probably worth further investigating whether the classic 1Hz high-pass filter is really also the best option for the detection and removal of cardiac activity. However, in our opinion this requires a dedicated investigation on its own..

We therefore highlight this now in our manuscript stating that:

“Additionally, it is worth noting that the effectiveness of an ICA crucially depends on the quality of the extracted components(63,64) and even widely suggested settings e.g. high-pass filtering at 1Hz before fitting an ICA may not be universally applicable (see supplementary material of (64)).

Winkler, S. Debener, K. -R. Müller and M. Tangermann, "On the influence of high-pass filtering on ICA-based artifact reduction in EEG-ERP," 2015 37th Annual International Conference of the IEEE Engineering in Medicine and Biology Society (EMBC), Milan, Italy, 2015, pp. 4101-4105, doi: 10.1109/EMBC.2015.7319296.

Dimigen, O. (2020). Optimizing the ICA-based removal of ocular EEG artifacts from free viewing experiments. NeuroImage, 207, 116117.

Klug, M., & Gramann, K. (2021). Identifying key factors for improving ICA‐based decomposition of EEG data in mobile and stationary experiments. European Journal of Neuroscience, 54(12), 8406-8420.

It looks like no methods were implemented to address muscle artifacts. These can affect the slope of EEG activity at higher frequencies. Perhaps the Riemannian Potato addressed these artifacts, but I suspect it wouldn't eliminate all muscle activity. As such, I would be concerned that remaining muscle artifacts affected some of the results, particularly those that included high frequency ranges in the aperiodic estimate. Perhaps if muscle activity were left in the EEG data, it could have disrupted the ability to detect a relationship between age and 1/f slope in a way that didn't disrupt the same relationship in the cardiac data (although I suspect it wouldn't reverse the overall conclusions given the number of converging results including in lower frequency bands). Is there a quick validity analysis the authors can implement to confirm muscle artifacts haven't negatively affected their results?

I note that an analysis of head movement in the MEG is provided on page 32, but it would be more robust to show that removing ICA components reflecting muscle doesn't change the results. The results/conclusions of the following study might be useful for objectively detecting probable muscle artifact components: Fitzgibbon, S. P., DeLosAngeles, D., Lewis, T. W., Powers, D. M. W., Grummett, T. S., Whitham, E. M., ... & Pope, K. J. (2016). Automatic determination of EMG-contaminated components and validation of independent component analysis using EEG during pharmacologic paralysis. Clinical neurophysiology, 127(3), 1781-1793.

We thank the reviewer for their suggestion. Muscle activity can indeed be a potential concern, for the estimation of the spectral slope. This is precisely why we used head movements (as also noted by the reviewer) as a proxy for muscle activity. We also agree with the reviewer that this is not a perfect estimate. Additionally, also the riemannian potato would probably only capture epochs that contain transient, but not persistent patterns of muscle activity.

The paper recommended by the reviewer contains a clever approach of using the steepness of the spectral slope (or lack thereof) as an indicator whether or not an independent component (IC) is driven by muscle activity. In order to determine an optimal threshold Fitzgibbon et al. compared paralyzed to temporarily non paralyzed subjects. They determined an expected “EMG-free” threshold for their spectral slope on paralyzed subjects and used this as a benchmark to detect IC’s that were contaminated by muscle activity in non paralyzed subjects.

This is a great idea, but unfortunately would go way beyond what we are able to sensibly estimate with our data for the following reasons. The authors estimated their optimal threshold on paralyzed subjects for EEG data and show that this is a feasible threshold to be applied across different recordings. So for EEG data it might be feasible, at least as a first shot, to use their threshold on our data. However, we are measuring MEG and as alluded to in our discussion section under “Differences in aperiodic activity between magnetic and electric field recordings” the spectral slope differs greatly between MEG and EEG recordings for non-trivial reasons. Furthermore, the spectral slope even seems to also differ across different MEG devices. We noticed this when we initially tried to pool the data recorded in Salzburg with the Cambridge dataset. This means we would need to do a complete validation of this procedure for the MEG data recorded in Cambridge and in Salzburg, which is not feasible considering that we A) don’t have direct access to one of the recording sites and B) would even if we had access face substantial hurdles to get ethical approval for the experiment performed by Fitzgibbon et al..

However, we think the approach brought forward by Fitzgibbon and colleagues is a clever way to remove muscle activity from EEG recordings, whenever EMG was not directly recorded. We therefore suggested in the Discussion section that ideally also EMG should be recorded stating that:

“It is worth noting that, apart from cardiac activity, muscle activity can also be captured in (non-)invasive recordings and may drastically influence measures of the spectral slope(72). To ensure that persistent muscle activity does not bias our results we used changes in head movement velocity as a control analysis (see Supplementary Figure S9). However, it should be noted that this is only a proxy for the presence of persistent muscle activity. Ideally, studies investigating aperiodic activity should also be complemented by measurements of EMG. Whenever such measurements are not available creative approaches that use the steepness of the spectral slope (or the lack thereof) as an indicator to detect whether or not e.g. an independent component is driven by muscle activity are promising(72,73). However, these approaches may require further validation to determine how well myographic aperiodic thresholds are transferable across the wide variety of different M/EEG devices.”

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) As outlined above, I recommend rephrasing the last section of the introduction to briefly summarize/introduce all main analysis steps undertaken in the study and why these were done (for example, it is only mentioned that the Cam-CAN dataset was used to study the impact of cardiac on MEG activity although the author used a variety of different datasets). Similarly, I am missing an overview of all main findings in the context of the study goals in the discussion. I believe clarifying the structure of the paper would not only provide a red thread to the reader but also highlight the efforts/strength of the study as described above.

This is a good call! As suggested by the reviewer we now try to give a clearer overview of what was investigated why. We do that both at the end of the introduction stating that: “Using the publicly available Cam-CAN dataset(28,29), we find that the aperiodic signal measured using M/EEG originates from multiple physiological sources. In particular, significant portions of age-related changes in aperiodic activity –normally attributed to neural processes– can be better explained by cardiac activity. This observation holds across a wide range of processing options and control analyses (see Supplementary S1), and was replicable on a separate MEG dataset. However, the extent to which cardiac activity accounts for age-related changes in aperiodic activity varies with the investigated frequency range and recording site. Importantly, in some frequency ranges and sensor locations, age-related changes in neural aperiodic activity still prevail. But does the influence of cardiac activity on the aperiodic spectrum extend beyond age? In a preliminary analysis, we demonstrate that working memory load modulates the aperiodic spectrum of “pure” ECG recordings. The direction of this working memory effect mirrors previous findings on EEG data(5) suggesting that the impact of cardiac activity goes well beyond aging. In sum, our results highlight the complexity of aperiodic activity while cautioning against interpreting it as solely “neural“ without considering physiological influences.”

and at the beginning of the discussion section:

“Difficulties in removing ECG related components from EEG signals via ICA might be attributable to various reasons such as the number of available sensors or assumptions related to the non-gaussianity of the underlying sources. Further understanding of this matter is highly important given that ICA is the most widely used procedure to separate neural from peripheral physiological sources (see Figure 1EF). Additionally, it is worth noting that the effectiveness of an ICA crucially depends on the quality of the extracted components(63,64) and even widely suggested settings e.g. high-pass filtering at 1Hz before fitting an ICA may not be universally applicable (see supplementary material of (64)). “

(2) I found it interesting that the spectral slopes of ECG activity at higher frequency ranges (> 10 Hz) seem mostly related to HRV measures such as fractal and time domain indices and less so with frequency-domain indices. Do the authors have an explanation for why this is the case? Also, the analysis of the HRV measures and their association with aperiodic ECG activity is not explained in any of the method sections.

We apologize for the oversight in not mentioning the HRV analysis in more detail in our methods section. We added a subsection to the Methods section entitled ECG Processing - Heart rate variability analysis to further describe the HRV analyses.

“ECG Processing - Heart rate variability analysis

Heart rate variability (HRV) was computed using the NeuroKit2 toolbox, a high level tool for the analysis of physiological signals. First, the raw electrocardiogram (ECG) data were preprocessed, by highpass filtering the signal at 0.5Hz using an infinite impulse response (IIR) butterworth filter(order=5) and by smoothing the signal with a moving average kernel with the width of one period of 50Hz to remove the powerline noise (default settings of neurokit.ecg.ecg_clean). Afterwards, QRS complexes were detected based on the steepness of the absolute gradient of the ECG signal. Subsequently, R-Peaks were detected as local maxima in the QRS complexes (default settings of neurokit.ecg.ecg_peaks; see (98) for a validation of the algorithm). From the cleaned R-R intervals, 90 HRV indices were derived, encompassing time-domain, frequency-domain, and non-linear measures. Time-domain indices included standard metrics such as the mean and standard deviation of the normalized R-R intervals , the root mean square of successive differences, and other statistical descriptors of interbeat interval variability. Frequency-domain analyses were performed using power spectral density estimation, yielding for instance low frequency (0.04-0.15Hz) and high frequency (0.15-0.4Hz) power components. Additionally, non-linear dynamics were characterized through measures such as sample entropy, detrended fluctuation analysis and various Poincaré plot descriptors. All these measures were then related to the slopes of the low frequency (0.25 – 20 Hz) and high frequency (10 – 145 Hz) aperiodic spectrum of the raw ECG.”

With regards to association of the ECG’s spectral slopes at high frequencies and frequency domain indices of heart rate variability. Common frequency domain indices of heart rate variability fall in the range of 0.01-.4Hz. Which probably explains why we didn’t notice any association at higher frequency ranges (>10Hz).

This is also stated in the related part of the results section:

“In the higher frequency ranges (10 - 145 Hz) spectral slopes were most consistently related to fractal and time domain indices of heart rate variability, but not so much to frequency-domain indices assessing spectral power in frequency ranges < 0.4 Hz.”

(3) Related to the previous point - what is being reflected in the ECG at higher frequency ranges, with regard to biological mechanisms? Results are being mentioned, but not further discussed. However, this point seems crucial because the age effects across the four datasets differ between low and high-frequency slope limits (Figure 2C).

This is a great question that definitely also requires further attention and investigation in general (see also Tereshchenko & Josephson, 2015). We investigated the change of the slope across frequency ranges that are typically captured in common ECG setups for adults (0.05 - 150Hz, Tereshchenko & Josephson, 2015; Kusayama, Wong, Liu et al. 2020). While most of the physiological significant spectral information of an ECG recording rests between 1-50Hz (Clifford & Azuaje, 2006), meaningful information can be extracted at much higher frequencies. For instance, ventricular late potentials have a broader frequency band (~40-250Hz) that falls straight in our spectral analysis window. However, that’s not all, as further meaningful information can be extracted at even higher frequencies (>100Hz). Yet, the exact physiological mechanisms underlying so-called high-frequency QRS remain unclear (HF-QRS; see Tereshchenko & Josephson, 2015; Qiu et al. 2024 for a review discussing possible mechanisms). Yet, at the same time the HF-QRS seems to be highly informative for the early detection of myocardial ischemia and other cardiac abnormalities that may not yet be evident in the standard frequency range (Schlegel et al. 2004; Qiu et al. 2024). All optimism aside, it is also worth noting that ECG recordings at higher frequencies can capture skeletal muscle activity with an overlapping frequency range up to 400Hz (Kusayama, Wong, Liu et al. 2020). We highlight all of this now when introducing this analysis in the results sections as outstanding research question stating that:

“However, substantially less is known about aperiodic activity above 0.4Hz in the ECG. Yet, common ECG setups for adults capture activity at a broad bandwidth of 0.05 - 150Hz(33,34).

Importantly, a lot of the physiological meaningful spectral information rests between 1-50Hz(35), similarly to M/EEG recordings. Furthermore, meaningful information can be extracted at much higher frequencies. For instance, ventricular late potentials have a broader frequency band (~40-250Hz(35)). However, that’s not all, as further meaningful information can be extracted at even higher frequencies (>100Hz). For instance, the so-called high-frequency QRS seems to be highly informative for the early detection of myocardial ischemia and other cardiac abnormalities that may not yet be evident in the standard frequency range(36,37). Yet, the exact physiological mechanisms underlying the high-frequency QRS remain unclear (see (37) for a review discussing possible mechanisms). ”

Tereshchenko, L. G., & Josephson, M. E. (2015). Frequency content and characteristics of ventricular conduction. Journal of electrocardiology, 48(6), 933-937.

Kusayama, T., Wong, J., Liu, X. et al. Simultaneous noninvasive recording of electrocardiogram and skin sympathetic nerve activity (neuECG). Nat Protoc 15, 1853–1877 (2020). https://doi.org/10.1038/s41596-020-0316-6

Clifford, G. D., & Azuaje, F. (2006). Advanced methods and tools for ECG data analysis (Vol. 10). P. McSharry (Ed.). Boston: Artech house.

Qiu, S., Liu, T., Zhan, Z., Li, X., Liu, X., Xin, X., ... & Xiu, J. (2024). Revisiting the diagnostic and prognostic significance of high-frequency QRS analysis in cardiovascular diseases: a comprehensive review. Postgraduate Medical Journal, qgae064.

Schlegel, T. T., Kulecz, W. B., DePalma, J. L., Feiveson, A. H., Wilson, J. S., Rahman, M. A., & Bungo, M. W. (2004, March). Real-time 12-lead high-frequency QRS electrocardiography for enhanced detection of myocardial ischemia and coronary artery disease. In Mayo Clinic Proceedings (Vol. 79, No. 3, pp. 339-350). Elsevier.

(4) Page 10: At first glance, it is not quite clear what is meant by "processing option" in the text. Please clarify.

Thank you for catching this! Upon re-reading this is indeed a bit oblivious. We now swapped “processing options” with “slope fits” to make it clearer that we are talking about the percentage of effects based on the different slope fits.

(5) The authors mention previous findings on age effects on neural 1/f activity (References Nr 5,8,27,39) that seem contrary to their own findings such as e.g., the mostly steepening of the slopes with age. Also, the authors discuss thoroughly why spectral slopes derived from MEG signals may differ from EEG signals. I encourage the authors to have a closer look at these studies and elaborate a bit more on why these studies differ in their conclusions on the age effects. For example, Tröndle et al. (2022, Ref. 39) investigated neural activity in children and young adults, hence, focused on brain maturation, whereas the CamCAN set only considers the adult lifespan. In a similar vein, others report age effects on 1/f activity in much smaller samples as reported here (e.g., Voytek et al., 2015).

I believe taking these points into account by briefly discussing them, would strengthen the authors' claims and provide a more fine-grained perspective on aging effects on 1/f.

The reviewer is making a very important point. As age-related differences in (neuro-)physiological activity are not necessarily strictly comparable and entirely linear across different age-cohorts (e.g. age-related changes in alpha center frequency). We therefore, added the suggested discussion points to the discussion section.

“Differences in electric and magnetic field recordings aside, aperiodic activity may not change strictly linearly as we are ageing and studies looking at younger age groups (e.g. <22; (44) may capture different aspects of aging (e.g. brain maturation), than those looking at older subjects (>18 years; our sample). A recent report even shows some first evidence of an interesting putatively non-linear relationship with age in the sensorimotor cortex for resting recordings(59)”

(6) The analysis of the working memory paradigm as described in the outlook-section of the discussion comes as a bit of a surprise as it has not been introduced before. If the authors want to convey with this study that, in general, aperiodic neural activity could be influenced by aperiodic cardiac activity, I recommend introducing this analysis and the results earlier in the manuscript than only in the discussion to strengthen their message.

The reviewer is correct. This analysis really comes a bit out of the blue. However, this was also exactly the intention for placing this analysis in the discussion. As the reviewer correctly noted, the aim was to suggest “that, in general, aperiodic neural activity could be influenced by aperiodic cardiac activity”. We placed this outlook directly after the discussion of “(neuro-)physiological origins of aperiodic activity”, where we highlight the potential challenges of interpreting drug induced changes to M/EEG recordings. So the aim was to get the reader to think about whether age is the only feature affected by cardiac activity and then directly present some evidence that this might go beyond age.

However, we have been rethinking this approach based on the reviewers comments and moved that paragraph to the end of the results section accordingly and introduce it already at the end of the introduction stating that:

“But does the influence of cardiac activity on the aperiodic spectrum extend beyond age? In a preliminary analysis, we demonstrate that working memory load modulates the aperiodic spectrum of “pure” ECG recordings. The direction of this working memory effect mirrors previous findings on EEG data(5) suggesting that the impact of cardiac activity goes well beyond aging.”

(7) The font in Figure 2 is a bit hard to read (especially in D). I recommend increasing the font sizes where necessary for better readability.

We agree with the Reviewer and increased the font sizes accordingly.

(8) Text in the discussion: Figure 3B on page 10 => shouldn't it be Figure 4?

Thank you for catching this oversight. We have now corrected this mistake.

(9) In the third section on page 10, the Figure labels seem to be confused. For example, Figure 4 E is supposed to show "steepening effects", which should be Figure 4B I believe.

Please check the figure labels in this section to avoid confusion.

Thank you for catching this oversight. We have now corrected this mistake.

(10) Figure Legend 4 I), please check the figure labels in the text

Thank you for catching this oversight. We have now corrected this mistake.

Reviewer #3 (Recommendations for the authors):

I have a number of suggestions for improving the manuscript, which I have divided by section in the following:

ABSTRACT:

I would suggest re-writing the first sentences to make it easier to read for non-expert readers: "The power of electrophysiologically measured cortical activity decays with an approximately 1/fX function. The slope of this decay (i.e. the spectral exponent, X) is modulated..."

Thank you for the suggestion. We adjusted the sentence as suggested to make it easier for less technical readers to understand that “X” refers to the exponent.

Including the age range that was studied in the abstract could be informative.

Done as suggested.

As an optional recommendation, I think it would increase the impact of the article if the authors note in the abstract that the current most commonly applied cardiac artifact reduction approaches don't resolve the issue for EEG data, likely due to an imperfect ability to separate the cardiac artifact from the neural activity with independent component analysis. This would highlight to the reader that they can't just expect to address these concerns by cleaning their data with typical cleaning methods.

I think it would also be useful to convey in the abstract just how comprehensive the included analyses were (in terms of artifact reduction methods tested, different aperiodic algorithms and frequency ranges, and both MEG and EEG). Doing so would let the reader know just how robust the conclusions are likely to be.

This is a brilliant idea! As suggested we added a sentence highlighting that simply performing an ICA may not be sufficient to separate cardiac contributions to M/EEG recordings and refer to the comprehensiveness of the performed analyses.

INTRODUCTION:

I would suggest re-writing the following sentence for readability: "In the past, aperiodic neural activity, other than periodic neural activity (local peaks that rise above the "power-law" distribution), was often treated as noise and simply removed from the signal"

To something like: "In the past, aperiodic neural activity was often treated as noise and simply removed from the signal e.g. via pre-whitening, so that analyses could focus on periodic neural activity (local peaks that rise above the "power-law" distribution, which are typically thought to reflect neural oscillations).

We are happy to follow that suggestion.

Page 3: please provide the number of articles that were included in the examination of the percentage that remove cardiac activity, and note whether the included articles could be considered a comprehensive or nearly comprehensive list, or just a representative sample.

We stated the exact number of articles in the methods section under Literature Analysis. However, we added it to the Introduction on page 3 as suggested by the reviewer. The selection of articles was done automatically, dependent on a list of pre-specified terms and exclusively focussed on articles that had terms related to aperiodic activity in their title (see Literature Analysis). Therefore, I would personally be hesitant in calling it a comprehensive or nearly comprehensive list of the general M/EEG literature as the analysis of aperiodic activity is still relatively niche compared to the more commonly investigated evoked potentials or oscillations. I think whether or not a reader perceives our analysis as comprehensive should be up to them to decide and does not reflect something I want to impose on them. This is exacerbated by the fact that the analysis of neural aperiodic activity has rapidly gained traction over the last years (see Figure 1D orange) and the literature analysis was performed almost 2 years ago and therefore, in my eyes, only represents a glimpse in the rapidly evolving field related to the analysis of aperiodic activity.

Figure 1E-F: It's not completely clear that the "Cleaning Methods" part of the figure indicates just methods to clean the cardiac artifact (rather than any artifact). It also seems that ~40% of EEG studies do not apply any cleaning methods even from within the studies that do clean the cardiac artifact (if I've read the details correctly). This seems unlikely. Perhaps there should be a bar for "other methods", or "unspecified"? Having said that, I'm quite familiar with the EEG artifact reduction literature, and I would be very surprised if ~40% of studies cleaned the cardiac artifact using a different method to the methods listed in the bar graph, so I'm wondering if I've misunderstood the figure, or whether the data capture is incomplete / inaccurate (even though the conclusion that ICA is the most common method is almost certainly accurate).

The cleaning is indeed only focussed on cardiac activity specifically. This was however also mentioned in the caption of Figure 1: “We were further interested in determining which artifact rejection approaches were most commonly used to remove cardiac activity, such as independent component analysis (ICA(22)), singular value decomposition (SVD(23)), signal space separation (SSS(24)), signal space projections (SSP(25)) and denoising source separation (DSS(26)).” and in the methods section under Literature Analysis. However, we adjusted figure 1EF to make it more obvious that the described cleaning methods were only related to the ECG. Aside from using blind source separation techniques such as ICA a good amount of studies mentioned that they cleaned their data based on visual inspection (which was not further considered). Furthermore, it has to be noted that only studies were marked as having separated cardiac from neural activity, when this was mentioned explicitly.

RESULTS:

Page 6: I would delete the "from a neurophysiological perspective" clause, which makes the sentence more difficult to read and isn't so accurate (frequencies 13-25Hz would probably more commonly be considered mid-range rather than low or high). Additionally, both frequency ranges include 15Hz, but the next sentence states that the ranges were selected to avoid the knee at 15Hz, which seems to be a contradiction. Could the authors explain in more detail how the split addresses the 15Hz knee?

We removed the “from a neurophysiological perspective” clause as suggested. With regards to the “knee” at ~15Hz I would like to defer the reviewer to Supplementary Figure S1. The Knee Frequency varies substantially across subjects so splitting the data at only 1 exact Frequency did not seem appropriate. Additionally, we found only spurious significant age-related variations in Knee Frequency (i.e. only one out of the 4 datasets; not shown).

Furthermore, we wanted to better connect our findings to our MEG results in Figure 4 and also give the readers a holistic overview of how different frequency ranges in the aperiodic ECG would be affected by age. So to fulfill all of these objectives we decided to fit slopes with respective upper/lower bounds around a range of 5Hz above and below the average 15Hz Knee Frequency across datasets.

The later parts of this same paragraph refer to a vast amount of different frequency ranges, but only the "low" and "high" frequency ranges were previously mentioned. Perhaps the explanation could be expanded to note that multiple lower and upper bounds were tested within each of these low and high frequency windows?

This is a good catch we adjusted the sentence as suggested. We now write: “.. slopes were fitted individually to each subject's power spectrum in several lower (0.25 – 20 Hz) and higher (10-145 Hz) frequency ranges.”

The following two sentences seem to contradict each other: "Overall, spectral slopes in lower frequency ranges were more consistently related to heart rate variability indices(> 39.4% percent of all investigated indices)" and: "In the lower frequency range (0.25 - 20Hz), spectral slopes were consistently related to most measures of heart rate variability; i.e. significant effects were detected in all 4 datasets (see Figure 2D)." (39.4% is not "most").

The reviewer is correct in stating that 39.4% is not most. However, the 39.4% is the lowest bound and only refers to 1 dataset. In the other 3 datasets the percentage of effects was above 64% which can be categorized as “most” i.e. above 50%. We agree that this was a bit ambiguous in the sentence so we added the other percentages as well as a reference to Figure 2D to make this point clearer.

Figure 2D: it isn't clear what the percentages in the semi-circles reflect, nor why some semi-circles are more full circles while others are only quarter circles.

The percentages in the semi-circles reflect the amount of effects (marked in red) and null effects (marked in green) per dataset, when viewed as average across the different measures of HRV. Sometimes less effects were found for some frequency ranges resulting in quarters instead of semi circles.

Page 8: I think the authors could make it more clear that one of the conditions they were testing was the ECG component of the EEG data (extracted by ICA then projected back into the scalp space for the temporal response function analysis).

As suggested by the reviewer we adjusted our wording and replaced the arguably a bit ambiguous “... projected back separately” with “... projected back into the sensor space”. We thank the reviewer for this recommendation, as it does indeed make it easier to understand the procedure.

“After pre-processing (see Methods) the data was split in three conditions using an ICA(22). Independent components that were correlated (at r > 0.4; see Methods: MEG/EEG Processing - pre-processing) with the ECG electrode were either not removed from the data (Figure 3ABCD - blue), removed from the data (Figure 2ABCD - orange) or projected back into the sensor space (Figure 3ABCD - green).”

Figure 4A: standardized beta coefficients for the relationship between age and spectral slope could be noted to provide improved clarity (if I'm correct in assuming that is what they reflect).

This was indeed shown in Figure 4A and noted in the color bar as “average beta (standardized)”. We do not specifically highlight this in the text, because the exact coefficients would depend on both on the analyzed frequency range and the selected electrodes.

Figure 4I: The regressions explained at this point seems to contain a very large number of potential predictors, as I'm assuming it includes all sensors for both the ECG component and ECG rejected conditions? (if that is not the case, it could be explained in greater detail). I'm also not sure about the logic of taking a complete signal, decomposing it with ICA to separate out the ECG and non-ECG signals, then including them back into the same regression model. It seems that there could be some circularity or redundancy in doing so. However, I'm not confident that this is an issue, so would appreciate the authors explaining why it this is a valid approach (if that is the case).

After observing significant effects both in the MEG_{ECG component} and MEG_{ECG rejected} conditions in similar frequency bands we wanted to understand whether or not these age-related changes are statistically independent. To test this we added both variables as predictors in a regression model (thereby accounting for the influence of the other in relation to age). The regression models we performed were therefore actually not very complex. They were built using only two predictors, namely the data (in a specific frequency range) averaged over channels on which we noticed significant effects in the ECG rejected and ECG components data respectively (Wilkinson notation: age ~ 1 + ECG rejected + ECG components). This was also described in the results section stating that: “To see if MEG_{ECG rejected} and MEG_{ECG component} explain unique variance in aging at frequency ranges where we noticed shared effects, we averaged the spectral slope across significant channels and calculated a multiple regression model with MEG_{ECG component} and MEG_{ECG rejected} as predictors for age (to statistically control for the effect of MEG_{ECG component}s and MEG_{ECG rejected} on age). This analysis was performed to understand whether the observed shared age-related effects (MEG_{ECG rejected} and MEG_{ECG component}) are in(dependent).”  

We hope this explanation solves the previous misunderstanding.

The explanation of results for relationships between spectral slopes and aging reported in Figure 4 refers to clusters of effects, but the statistical inference methods section doesn't explain how these clusters were determined.

The wording of “cluster” was used to describe a “category” of effects e.g. null effects. We changed the wording from “cluster” to “category” to make this clearer stating now that: “This analysis, which is depicted in Figure 4, shows that over a broad amount of individual fitting ranges and sensors, aging resulted in a steepening of spectral slopes across conditions (see Figure 4E) with “steepening effects” observed in 25% of the processing options in MEG_{ECG not rejected} , 0.5% in MEG_{ECG rejected}, and 60% for MEG_{ECG components}. The second largest category of effects were “null effects” in 13% of the options for MEG_{ECG not rejected} , 30% in MEG_{ECG rejected}, and 7% for MEG_{ECG components}. ”

Page 12: can the authors clarify whether these age related steepenings of the spectral slope in the MEG are when the data include the ECG contribution, or when the data exclude the ECG? (clarifying this seems critical to the message the authors are presenting).

We apologize for not making this clearer. We now write: “This analysis also indicates that a vast majority of observed effects irrespective of condition (ECG components, ECG not rejected, ECG rejected) show a steepening of the spectral slope with age across sensors and frequency ranges.”

Page 13: I think it would be useful to describe how much variance was explained by the MEG-ECG rejected vs MEG-ECG component conditions for a range of these analyses, so the reader also has an understanding of how much aperiodic neural activity might be influenced by age (vs if the effects are really driven mostly by changes in the ECG).

With regards to the explained variance I think that the very important question of how strong age influences changes in aperiodic activity is a topic better suited for a meta analysis. As the effect sizes seems to vary largely depending on the sample e.g. for EEG in the literature results were reported at r=-0.08 (Cesnaite et al. 2023), r=-0.26 (Cellier et al. 2021), r=-0.24/r=-0.28/r=-0.35 (Hill et al. 2022) and r=0.5/r=0.7 (Voytek et al. 2015). I would defer the reader/reviewer to the standardized beta coefficients as a measure of effect size in the current study that is depicted in Figure 4A.

Cellier, D., Riddle, J., Petersen, I., & Hwang, K. (2021). The development of theta and alpha neural oscillations from ages 3 to 24 years. Developmental cognitive neuroscience, 50, 100969.

Cesnaite, E., Steinfath, P., Idaji, M. J., Stephani, T., Kumral, D., Haufe, S., ... & Nikulin, V. V. (2023). Alterations in rhythmic and non‐rhythmic resting‐state EEG activity and their link to cognition in older age. NeuroImage, 268, 119810.

Hill, A. T., Clark, G. M., Bigelow, F. J., Lum, J. A., & Enticott, P. G. (2022). Periodic and aperiodic neural activity displays age-dependent changes across early-to-middle childhood. Developmental Cognitive Neuroscience, 54, 101076.

Voytek, B., Kramer, M. A., Case, J., Lepage, K. Q., Tempesta, Z. R., Knight, R. T., & Gazzaley, A. (2015). Age-related changes in 1/f neural electrophysiological noise. Journal of Neuroscience, 35(38), 13257-13265.

Also, if there are specific M/EEG sensors where the 1/f activity does relate strongly to age, it would be worth noting these, so future research could explore those sensors in more detail.

I think it is difficult to make a clear claim about this for MEG data, as the exact location or type of the sensor may differ across manufacturers. Such a statement could be easier made for source projected data or in case EEG electrodes were available, where the location would be normed eg. according to the 10-20 system.

DISCUSSION:

Page 15: Please change the wording of the following sentence, as the way it is currently worded seems to suggest that the authors of the current manuscript have demonstrated this point (which I think is not the case): "The authors demonstrate that EEG typically integrates activity over larger volumes than MEG, resulting in differently shaped spectra across both recording methods."

Apologies for the oversight! The reviewer is correct we in fact did not show this, but the authors of the cited manuscript. We correct the sentence as suggested stating now that:

“Bénar et al. demonstrate that EEG typically integrates activity over larger volumes than MEG, resulting in differently shaped spectra across both recording methods.”

Page 16: The authors mention the results can be sensitive to the application of SSS to clean the MEG data, but not ICA. I think it would be sensitive to the application of either SSS or ICA?

This is correct and actually also supported by Figure S7, as differences in ICA thresholds affect also the detection of age-related effects. We therefore adjusted the related sentences stating now that:

“ In case of the MEG signal this may include the application of Signal-Space-Separation algorithms (SSS(24,55)), different thresholds for ICA component detection (see Figure S7), high and low pass filtering, choices during spectral density estimation (window length/type etc.), different parametrization algorithms (e.g. IRASA vs FOOOF) and selection of frequency ranges for the aperiodic slope estimation.”

It would be worth clarifying that the linked mastoid re-reference alone has been proposed to cancel out the ECG signal, rather than that a linked-mastoid re-reference improves the performance of the ICA separation (which could be inferred by the explanation as it's currently written).

This is correct and we adjusted the sentence accordingly! Stating now that:

“ Previous work(12,56) has shown that a linked mastoid reference alone was particularly effective in reducing the impact of ECG related activity on aperiodic activity measured using EEG. “

The issue of the number of EEG channels could probably just be noted as a potential limitation, as could the issue of neural activity being mixed into the ECG component (although this does pose a potential confound to the M/EEG without ECG condition, I suspect it wouldn't be critical).

This is indeed a very fair point as a higher amount of electrodes would probably make it easier to better isolate ECG components in the EEG, which may be the reason why the separation did not work so well in our case. However, this is ultimately an empirical question so we highlighted it in the discussion section stating that: “Difficulties in removing ECG related components from EEG signals via ICA might be attributable to various reasons such as the number of available sensors or assumptions related to the non-gaussianity of the underlying sources. Further understanding of this matter is highly important given that ICA is the most widely used procedure to separate neural from peripheral physiological sources. ”

OUTLOOK:

Page 19: Although there has been a recent trend to control for 1/f activity when examining oscillatory power, recent research suggests that this should only be implemented in specific circumstances, otherwise the correction causes more of a confound than the issue does. It might be worth considering this point with regards to the final recommendation in the Outlook section: Brake, N., Duc, F., Rokos, A., Arseneau, F., Shahiri, S., Khadra, A., & Plourde, G. (2024). A neurophysiological basis for aperiodic EEG and the background spectral trend. Nature Communications, 15(1), 1514.

We want to thank the reviewer for recommending this very interesting paper! The authors of said paper present compelling evidence showing that, while peak detection above an aperiodic trend using methods like FOOOF or IRASA is a prerequisite to determine the presence of oscillatory activity, it’s not necessarily straightforward to determine which detrending approach should be applied to determine the actual power of an oscillation. Furthermore, the authors suggest that wrongfully detrending may cause larger errors than not detrending at all. We therefore added a sentence stating that: “However, whether or not periodic activity (after detection) should be detrended using approaches like FOOOF or IRASA still remains disputed, as incorrectly detrending the data may cause larger errors than not detrending at all(75).”

RECOMMENDATIONS:

Page 20: "measure and account for" seems like it's missing a word, can this be re-written so the meaning is more clear?

Done as suggested. The sentence now states: “To better disentangle physiological and neural sources of aperiodic activity, we propose the following steps to (1) measure and (2) account for physiological influences.”

I would re-phrase "doing an ICA" to "reducing cardiac artifacts using ICA" (this wording could be changed in other places also).

I do not like to describe cardiac or ocular activity as artifactual per se. This is also why I used hyphens whenever I mention the word “artifact” in association with the ECG or EOG. However, I do understand that the wording of “doing an ICA” is a bit sloppy. We therefore reworded it accordingly throughout the manuscript to e.g. “separating cardiac from neural sources using an ICA” and “separating physiological from neural sources using an ICA”.

I would additionally note that even if components are identified as unambiguously cardiac, it is still likely that neural activity is mixed in, and so either subtracting or leaving the component will both be an issue (https://doi.org/10.1101/2024.06.06.597688). As such, even perfect identification of whether components are cardiac or not would still mean the issue remains (and this issue is also consistent across a considerable range of component based methods). Furthermore, current methods including wavelet transforms on the ICA component still do not provide good separation of the artifact and neural activity.

This is definitely a fair point and we also highlight this in our recommendations under 3 stating that:

“However, separating physiological from neural sources using an ICA is no guarantee that peripheral physiological activity is fully removed from the cortical signal. Even more sophisticated ICA based methods that e.g. apply wavelet transforms on the ICA components may still not provide a good separation of peripheral physiological and neural activity76,77. This turns the process of deciding whether or not an ICA component is e.g. either reflective of cardiac or neural activity into a challenging problem. For instance, when we only extract cardiac components using relatively high detection thresholds (e.g. r > 0.8), we might end up misclassifying residual cardiac activity as neural. In turn, we can’t always be sure that using lower thresholds won’t result in misinterpreting parts of the neural effects as cardiac. Both ways of analyzing the data can potentially result in misconceptions.”

Castellanos, N. P., & Makarov, V. A. (2006). Recovering EEG brain signals: Artifact suppression with wavelet enhanced independent component analysis. Journal of neuroscience methods, 158(2), 300-312.

Bailey, N. W., Hill, A. T., Godfrey, K., Perera, M. P. N., Rogasch, N. C., Fitzgibbon, B. M., & Fitzgerald, P. B. (2024). EEG is better when cleaning effectively targets artifacts. bioRxiv, 2024-06.

METHODS:

Pre-processing, page 24: I assume the symmetric setting of fastica was used (rather than the deflation setting), but this should be specified.

Indeed the reviewer is correct, we used the standard setting of fastICA implemented in MNE python, which is calling the FastICA implementation in sklearn that is per default using the “parallel” or symmetric algorithm to compute an ICA. We added this information to the text accordingly, stating that:

“For extracting physiological “artifacts” from the data, 50 independent components were calculated using the fastica algorithm(22) (implemented in MNE-Python version 1.2; with the parallel/symmetric setting; note: 50 components were selected for MEG for computational reasons for the analysis of EEG data no threshold was applied).”

Temporal response functions, page 26: can the authors please clarify whether the TRF is computed against the ECG signal for each electrode or sensory independently, or if all electrodes/sensors are included in the analysis concurrently? I'm assuming it was computed for each electrode and sensory separately, since the TRF was computed in both the forward and backwards direction (perhaps the meaning of forwards and backwards could be explained in more detail also - i.e. using the ECG to predict the EEG signal, or using the EEG signal to predict the ECG signal?).

A TRF can also be conceptualized as a multiple regression model over time lags. This means that we used all channels to compute the forward and backward models. In the case of the forward model we predicted the signal of the M/EEG channels in a multivariate regression model using the ECG electrode as predictor. In case of the backward model we predicted the ECG electrode based on the signal of all M/EEG channels. The forward model was used to depict the time window at which the ECG signal was encoded in the M/EEG recording, which appears at 0 time lags indicating volume conduction. The backward model was used to see how much information of the ECG was decodable by taking the information of all channels.

We tried to further clarify this approach in the methods section stating that:

“We calculated the same model in the forward direction (encoding model; i.e. predicting M/EEG data in a multivariate model from the ECG signal) and backward direction (decoding model; i.e. predicting the ECG signal using all M/EEG channels as predictors).”

Page 27: the ECG data was fit using a knee, but it seems the EEG and MEG data was not.

Does this different pose any potential confound to the conclusions drawn? (having said this, Figure S4 suggests perhaps a knee was tested in the M/EEG data, which should perhaps be explained in the text also).

This was indeed tested in a previous review round to ensure that our results are not dependent on the presence/absence of a knee in the data. We therefore added figure S4, but forgot to actually add a description in the text. We are sorry for this oversight and added a paragraph to S1 accordingly:

“Using FOOOF(5), we also investigated the impact of different slope fitting options (fixed vs. knee model fits) on the aperiodic age relationship (see Supplementary Figure S4). The results that we obtained from these analyses using FOOOF offer converging evidence with our main analysis using IRASA.”

Page 32: my understanding of the result reported here is that cleaning with ICA provided better sensitivity to the effects of age on 1/f activity than cleaning with SSS. Is this accurate? I think this could also be reported in the main manuscript, as it will be useful to researchers considering how to clean their M/EEG data prior to analyzing 1/f activity.

The reviewer is correct in stating that we overall detected slightly more “significant” effects, when not additionally cleaning the data using SSS. However, I am a bit wary of recommending omitting the use of SSS maxfilter solely based on this information. It can very well be that the higher quantity of effects (when not employing SSS maxfilter) stems from other physiological sources (e.g. muscle activity) that are correlated with age and removed when applying SSS maxfiltering. I think that just conditioning the decision of whether or not maxfilter is applied based on the amount or size of effects may not be the best idea. Instead I think that the applicability of maxfilter for research questions related to aperiodic activity should be the topic of additional methodological research. We therefore now write in Text S1:

“Considering that we detected less and weaker aperiodic effects when using SSS maxfilter is it advisable to omit maxfilter, when analyzing aperiodic signals? We don’t think that we can make such a judgment based on our current results. This is because it's unclear whether or not the reduction of effects stems from an additional removal of peripheral information (e.g. muscle activity; that may be correlated with aging) or is induced by the SSS maxfiltering procedure itself. As the use of maxfilter in detecting changes of aperiodic activity was not subject of analysis that we are aware of, we suggest that this should be the topic of additional methodological research.”

Page 39, Figure S6 and Figure S8: Perhaps the caption could also briefly explain the difference between maxfilter set to false vs true? I might have missed it, but I didn't gain an understanding of what varying maxfilter would mean.

Figure S6 shows the effect of ageing on the spectral slope averaged across all channels. The maxfilter set to false in AB) means that no maxfiltering using SSS was performed vs. in CD) where the data was additionally processed using the SSS maxfilter algorithm. We now describe this more clearly by writing in the caption:

“Supplementary Figure S6: Age-related changes in aperiodic brain activity are most prominent on explained by cardiac components irrespective of maxfiltering the data using signal space separation (SSS) or not AC) Age was used to predict the spectral slope (fitted at 0.1-145Hz) averaged across sensors at rest in three different conditions (ECG components not rejected [blue], ECG components rejected [orange], ECG components only [green].”

Author response:

The following is the authors’ response to the original reviews

Public reviews:

Reviewer #1 (Public Review):

Summary:

In this paper, Weber et al. investigate the role of 4 dopaminergic neurons of the Drosophila larva in mediating the association between an aversive high-salt stimulus and a neutral odor. The 4 DANs belong to the DL1 cluster and innervate non-overlapping compartments of the mushroom body, distinct from those involved in appetitive associative learning. Using specific driver lines, they show that activation of the DAN-g1 is sufficient to mimic an aversive memory and it is also necessary to form a high-salt memory of full strength, although optogenetic silencing of this neuron only partially affects the performance index. The authors use calcium imaging to show that the DAN-g1 is not the only one that responds to salt. DAN-c1 and d1 also respond to salt, but they seem to play no role in the assays tested. DAN-f1, which does not respond to salt, is able to lead to the formation of memory (if optogenetically activated), but it is not necessary for the salt-odor memory formation in normal conditions. However, silencing of DAN-f1 together with DAN-g1, enhances the memory deficit of DAN-g1.

Strengths:

The paper therefore reveals that also in the Drosophila larva as in the adult, rewards and punishments are processed by exclusive sets of DANs and that a complex interaction between a subset of DANs mediates salt-odor association.

Overall, the manuscript contributes valuable results that are useful for understanding the organization and function of the dopaminergic system. The behavioral role of the specific DANs is accessed using specific driver lines which allow for testing of their function individually and in pairs. Moreover, the authors perform calcium imaging to test whether DANs are activated by salt, a prerequisite for inducing a negative association with it. Proper genetic controls are carried across the manuscript.

Weaknesses:

The authors use two different approaches to silence dopaminergic neurons: optogenetics and induction of apoptosis. The results are not always consistent, and the authors could improve the presentation and interpretation of the data. Specifically, optogenetics seems a better approach than apoptosis, which can affect the overall development of the system, but apoptosis experiments are used to set the grounds of the paper.

The physiological data would suggest the role of a certain subset of DANs in salt-odor association, but a different partially overlapping set seems to be necessary. This should be better discussed and integrated into the author's conclusion. The EM data analysis reveals a non-trivial organization of sensory inputs into DANs and it is hard to extrapolate a link to the functional data presented in the paper.

We would like to thank reviewer 1 for the positive evaluation of our work and for the critical suggestions for improvement. In the new version of the manuscript, we have centralized the optogenetic results and moved some of the ablation experiments to the Supplement. We also discuss in detail the experimental differences in the results. In addition, we have softened our interpretation of the specificity of memory for salt. As a result, we now emphasize more the general role of DANs for aversive learning in the larva. These changes are now also summarized and explained more simply and clearly in the Discussion, along with a revised discussion of the EM data.

Reviewer #2 (Public Review):

Summary:

In this work, the authors show that dopaminergic neurons (DANs) from the DL1 cluster in Drosophila larvae are required for the formation of aversive memories. DL1 DANs complement pPAM cluster neurons which are required for the formation of attractive memories. This shows the compartmentalized network organization of how an insect learning center (the mushroom body) encodes memory by integrating olfactory stimuli with aversive or attractive teaching signals. Interestingly, the authors found that the 4 main dopaminergic DL1 neurons act redundantly, and that single-cell ablation did not result in aversive memory defects. However, ablation or silencing of a specific DL1 subset (DAN-f1,g1) resulted in reduced salt aversion learning, which was specific to salt but no other aversive teaching stimuli were tested. Importantly, activation of these DANs using an optogenetic approach was also sufficient to induce aversive learning in the presence of high salt. Together with the functional imaging of salt and fructose responses of the individual DANs and the implemented connectome analysis of sensory (and other) inputs to DL1/pPAM DANs, this represents a very comprehensive study linking the structural, functional, and behavioral role of DL1 DANs. This provides fundamental insight into the function of a simple yet efficiently organized learning center which displays highly conserved features of integrating teaching signals with other sensory cues via dopaminergic signaling.

Strengths:

This is a very careful, precise, and meticulous study identifying the main larval DANs involved in aversive learning using high salt as a teaching signal. This is highly interesting because it allows us to define the cellular substrates and pathways of aversive learning down to the single-cell level in a system without much redundancy. It therefore sets the basis to conduct even more sophisticated experiments and together with the neat connectome analysis opens the possibility of unraveling different sensory processing pathways within the DL1 cluster and integration with the higher-order circuit elements (Kenyon cells and MBONs). The authors' claims are well substantiated by the data and clearly discussed in the appropriate context. The authors also implement neat pathway analyses using the larval connectome data to its full advantage, thus providing network pathways that contribute towards explaining the obtained results.

Weaknesses:

While there is certainly room for further analysis in the future, the study is very complete as it stands. Suggestions for clarification are minor in nature.

We would like to thank reviewer 2 for the positive evaluation of our work. In fact, follow-up work is already underway to further analyze the role of the individual DL1 DANs. We have addressed the constructive and detailed suggestions for improvement in our point-by-point responses in the “Recommendations for the authors” section.

Reviewer #3 (Public Review):

The study of Weber et al. provides a thorough investigation of the roles of four individual dopamine neurons for aversive associative learning in the Drosophila larva. They focus on the neurons of the DL-1 cluster which already have been shown to signal aversive teaching signals. However, the authors go far beyond the previous publications and test whether each of these dopamine neurons responds to salt or sugar, is necessary for learning about salt, bitter, or sugar, and is sufficient to induce a memory when optogenetically activated. In addition, previously published connectomic data is used to analyze the synaptic input to each of these dopamine neurons. The authors conclude that the aversive teaching signal induced by salt is distributed across the four DL-1 dopamine neurons, with two of them, DAN-f1 and DAN-g1, being particularly important. Overall, the experiments are well designed and performed, support the authors' conclusions, and deepen our understanding of the dopaminergic punishment system.

Strengths:

(1) This study provides, at least to my knowledge, the first in vivo imaging of larval dopamine neurons in response to tastants. Although the selection of tastants is limited, the results close an important gap in our understanding of the function of these neurons.

(2) The authors performed a large number of experiments to probe for the necessity of each individual dopamine neuron, as well as combinations of neurons, for associative learning. This includes two different training regimens (1 or 3 trials), three different tastants (salt, quinine, and fructose) and two different effectors, one ablating the neuron, the other one acutely silencing it. This thorough work is highly commendable, and the results prove that it was worth it. The authors find that only one neuron, DAN-g1, is partially necessary for salt learning when acutely silenced, whereas a combination of two neurons, DAN-f1 and DAN-g1, are necessary for salt learning when either being ablated or silenced.

(3) In addition, the authors probe whether any of the DL-1 neurons is sufficient for inducing an aversive memory. They found this to be the case for three of the neurons, largely confirming previous results obtained by a different learning paradigm, parameters, and effector.

(4) This study also takes into account connectomic data to analyze the sensory input that each of the dopamine neurons receives. This analysis provides a welcome addition to previous studies and helps to gain a more complete understanding. The authors find large differences in inputs that each neuron receives, and little overlap in input that the dopamine neurons of the "aversive" DL-1 cluster and the "appetitive" pPAM cluster seem to receive.

(5) Finally, the authors try to link all the gathered information in order to describe an updated working model of how aversive teaching signals are carried by dopamine neurons to the larva's memory center. This includes important comparisons both between two different aversive stimuli (salt and nociception) and between the larval and adult stages.

Weaknesses:

(1) The authors repeatedly claim that they found/proved salt-specific memories. I think this is problematic to some extent.

(1a) With respect to the necessity of the DL-1 neurons for aversive memories, the authors' notion of salt-specificity relies on a significant reduction in salt memory after ablating DAN-f1 and g1, and the lack of such a reduction in quinine memory. However, Fig. 5K shows a quite suspicious trend of an impaired quinine memory which might have been significant with a higher sample size. I therefore think it is not fully clear yet whether DAN-f1 and DAN-g1 are really specifically necessary for salt learning, and the conclusions should be phrased carefully.

(1b) With respect to the results of the optogenetic activation of DL-1 neurons, the authors conclude that specific salt memories were established because the aversive memories were observed in the presence of salt. However, this does not prove that the established memory is specific to salt - it could be an unspecific aversive memory that potentially could be observed in the presence of any other aversive stimuli. In the case of DAN-f1, the authors show that the neuron does not even get activated by salt, but is inhibited by sugar. Why should activation of such a neuron establish a specific salt memory? At the current state, the authors clearly showed that optogenetic activation of the neurons does induce aversive memories - the "content" of those memories, however, remains unknown.

(2) In many figures (e.g. figures 4, 5, 6, supplementary figures S2, S3, S5), the same behavioural data of the effector control is plotted in several sub-figures. Were these experiments done in parallel? If not, the data should not be presented together with results not gathered in parallel. If yes, this should be clearly stated in the figure legends.

We would also like to thank reviewer 3 for his positive assessment of our work. As already mentioned by reviewer 1, we understand the criticism that the salt specificity for which the individual DANs are coded is not fully always supported by the results of the work. We have therefore rewritten the relevant passages, which are also cited by the reviewer. We have also included the second point of criticism and incorporated it into our manuscript. As the control groups were always measured in parallel with the experimental animals, we can also present the data together in a sub-figure. We clearly state this now in the revised figure legends.

Summary of recommendations to authors:

Overall, the study is commendable for its systematic approach and solid methodology. Several weaknesses were identified, prompting the need for careful revisions of the manuscript:

We thank the reviewers for the careful revision of our manuscript. In the subsequent sections, we aim to address their concerns as thoroughly as possible. A comprehensive one-to-one listing can be found below.

(1) The authors should reconsider their assertion of uncovering a salt-specific memory, as the evidence does not conclusively demonstrate the exclusive necessity of DAN-f1 and DAN-g1 for salt learning. In particular, the optogenetic activation of DAN-f1 leads to plasticity but this might not be salt-specific. The precise nature of the memory content remains elusive, warranting a nuanced rephrasing of the conclusions.

We only partially agree – optogenetic activation of DANs does not really allow to comment on its salt-specificity, true. However, we used high-salt concentrations during test. Over the years, the Gerber lab nicely demonstrated in several papers that larvae recall an aversive odor-salt memory only if salt is present during test (Gerber and Hendel, 2006; Niewalda et al 2008; Schleyer et al. 2011; Schleyer et al. 2015). The used US has to be present during test. Even at the same concentration other aversive stimuli (e.g. bitter quinine) are not able to allow the larvae to recall this particular type of memory. So, if the optogenetic activation of DAN-f1 establishes a memory that can be recalled on salt, we argue that it has to encode aspects of the salt information. On the other hand, only for DAN-g1 we see the necessity for salt learning. And – although (based on the current literature) very unlikely, we cannot fully exclude that the activation of DAN-f1 establishes a yet unknown type of memory that can be also recalled on a salt plate. Therefore, we partially agree and accordingly have rephrased the entire manuscript to avoid an over-interpretation of our data. Throughout the manuscript we avoid now to use the term salt-specific memory but rather describe the type of memory as aversive memory.

(2) A thorough examination or discussion about the potential influence of blue light aversion on behavioral observations is necessary to ensure a balanced interpretation of the findings.

To address this point every single behavioral experiment that uses optogenetic blue light activation runs with appropriate and mandatory controls. For blue light activation experiments, two genetic controls are used that either get the same blue light treatment (effector control, w1118>UAS-ChR2XXL) or no blue light treatment (dark control, XY-split-Gal4>UAS-ChR2XXL). For blue light inactivation experiments one group is added that has exactly the same genotype but did not receive food containing retinal. These experiments show that blue light exposure itself does not induce an aversive nor positive memory and blue light exposure does not impair the establishment of odor-high salt memory. In addition, we used the latest established transgenes available. ChR2^XXL is very sensitive to blue light. Only 220 lux (60 µW/cm^²) were necessary to obtain stable results. In our hands – short term exposure for up to 5 minutes with such low intensities does not induce a blue light aversion. Following the advice of the reviewer, we also address this concern by adding several sentences into the related results and methods sections.

(3) The authors should address the limitations associated with the use of rpr/hid for neuronal ablations, such as the effects of potential developmental compensation.

We agree with this concern. It is well possible that the ablation experiments induce compensatory effects during larval development. Such an effect may be the reason for differences in phenotypes when comparing hid,rpr ablation with optogenetic inhibition. This is now part of the discussion. In addition, we evaluated if the ablation worked in our experiments. So far controls were missing that show that the expression of hid,rpr really leads to the ablation of DANs. We now added these experiments and clearly show anatomically that the DANs are ablated (related to figure 4-figure supplement 6).

(4) While the connectome analysis offers valuable insights into the observed functions of specific DANs in relation to their extrinsic (sensory) and intrinsic (state) inputs, integrating this data more cohesively within the manuscript through careful rewriting would enhance the coherence of the study.

We understand this concern. Therefore, the new version of our manuscript is now intensifying the inclusion of the EM data in our interpretation of the results. Throughout the entire manuscript we have now rewritten the related parts. We have also completely revised the corresponding section in the results chapter.

(5) More generally, the authors are encouraged to discuss internal discrepancies in the results of their functional manipulation experiments.

Thank you for this suggestion. We do of course understand that we have not given the different results enough space in the discussion. We have now changed this and have been happy to comprehensively address the concern. 

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Here are some suggestions for clarification and improvement of the manuscript:

(1) The authors should discuss why the silencing experiment with TH-GAL4 (Fig. 1) does not abolish memory formation (I assume that the PI should go to zero). Does it mean that other non-TH neurons are involved in salt-odor memory formation? Are there other lines that completely abolish this type of learning?

Thank you very much for highlighting this crucial point. Indeed, the functional intervention does not completely eliminate the memory. There could be several reasons, or a combination thereof, for this outcome. For instance, it's plausible that the UAS-GtACR2 effector doesn't entirely suppress the activity of dopaminergic neurons. Additionally, the memory may comprise different types, not all of which are linked to dopamine function. It's also noteworthy that TH-Gal4 doesn't encompass all dopaminergic neurons – even a neuron from the DL1 cluster is absent (as previously reported in Selcho et al., 2009). Considering we're utilizing high salt concentrations in this experiment, it's conceivable that non gustatory-driven memories are formed based solely on the systemic effects of salt (e.g., increased osmotic pressure). These possibilities are now acknowledged in the text.

(2) The Rpr experiments in Fig. 4 do not lead to any phenotype and there is a general assumption that the system compensates during development. However, there is no demonstration that Rpr worked or that development compensated for that. What do we learn from these data? Would it make sense to move it to supplement to make the story more compact? In addition: the conclusion at L 236 "DL1.... Are not individually necessary" is later disproved by optogenetic silencing. Similarly, optogenetic silencing of f1+g1 is affecting 1X and 3X learning, but not when using Rpr. Moreover, Rpr wdid not give any phenotype in other data in the supplementary material. I'm not sure how valid these results are.

We acknowledge this concern and have actively deliberated various options for restructuring the presented ablation data. Ultimately, we reached a consensus that relocating Figure 4 to the supplement is warranted. Furthermore, corresponding adjustments have been made in the text. This decision amplifies the significance of the optogenetic results. In addition, we also addressed the other part of the concern. We examined the efficacy of hid and rpr in our experiments. Indeed, we successfully ablated specific DANs, as illustrated in the new anatomical data presented in Figure 4- figure supplement 6, which strengthens the interpretation of the hid,rpr experiments.

(3) In most figures that show data for 1X and 3X training, there is no difference between these two conditions (I would suggest moving one set as a supplement). When a difference appears (Fig.5A-D) the implications are not discussed properly. Is it known that some circuits are necessary for the 1X but not for the 3X protocol? Is that a reasonable finding? I would expect the opposite, but I might lack of knowledge here. However, the optogenetic silencing of the same neurons in Figure 7 shows the same phenotype for 1X and 3X. Again, the validity of the Rpr experiments seems debatable.

Different training protocols lead to different memory phases (STM and STM+ARM). We have shown that in the past in Widmann et al. 2016. Therefore, we are convinced that it makes sense to keep both data sets in the main manuscript. However, we agree that this was not properly introduced and discussed and therefore made the respective changes in the manuscript.

(4) In Figure 3, it is unclear what the responses were tested against. Since they are so small and noisy there would be a need for a control. Moreover, in some cases, it looks like the DF/F is normalized to the wrong value: e.g. in DAN-c1 100mM, the activity in 0-10s is always above zero, and in pPAM with fructose is always below zero. This might not have any consequence on the results but should be adjusted.

Thank you very much for your criticism, which we greatly appreciate. We have carefully re-examined the data and found that there was a mistake for the normalization of the values. We made the necessary adjustments to the evaluation, as per your suggestions. The updated figures, figure legends, and results have been incorporated into the new version of the manuscript. As noted by the reviewer, these corrections have not altered the interpretation of the data or the primary responses of the various DANs.

(5) In the abstract: "Optogenetic activation of DAN-f1 and DAN-g1 alone suffices to substitute for salt punishment... Each DAN encodes a different aspect of salt punishment". These sentences might be misleading and an overstatement: only DAN-g1 shows a clear role, while the function of the other DANs in the context of salt-odor learning remains obscure.

We have refined the respective part of the abstract accordingly. Consequently, we have reworded the related section, aiming to avoid any exaggeration.

(6) The physiology is done in L1 larvae but behavior is tested in L3 larvae. There could be a change in this time that could explain the salt responses in c1 and d1 but no role in salt-odor learning?

While we cannot dismiss the possibility of a developmental change from L1 to L3, a comparison of the anatomical data of the DL1 DANs from electron microscopy (EM) and light microscopy (LM) data indicates that their overall morphology remains consistent. However, it's important to note that this observation does not analyse the physiological aspects of these cells. Consequently, we have incorporated this concern into the discussion of the revised version of the manuscript.

(7) The introduction needs some editing starting at L 129, as it ends with a discussion of a previously published EM data analysis. I would rather suggest stating which questions are addressed in this paper and which methods will be used and perhaps a hint on the results obtained.

We understand the concern. We have added a concise paragraph to the conclusion of the introduction, highlighting the biological question, technical details, and a short hint on the acquired findings.

(8) It is clear to me that the presentation of salt during the test is necessary for recall, however in L 166 I don't understand the explanation: how is the memory used in a beneficial way in the test? The salt is present everywhere and the odor cue is actually useless to escape it.

Extensive research, exemplified by studies such as Schleyer et al. (2015) published in Elife, clearly demonstrates that the recall of odor-high salt memory occurs exclusively when tested on a high salt plate. Even when tested on a bitter quinine plate, the aversive memory is not recalled. This phenomenon is attributed to the triggering of motivation to recall the memory by the omnipresent abundance of the unconditioned stimulus (US) during the test, which in our case is high salt. Furthermore, the concentration of the stimulus plays a crucial role (Schleyer et al. 2011). The odor cue indicates where the situation could potentially be improved; however, if high salt is absent, this motivational drive diminishes as there is no memory present to enhance the already favorable situation. Additionally, the motivation to evade the omnipresent and unpleasant high salt stimulus persists throughout the entire 5-minute test period.

(9) L288: the fact that f1 shows a phenotype in this experiment does not mean that it encodes a salt signal, indeed it does not respond to salt. It perhaps induces a plasticity that can be recalled by salt, but not necessarily linked to salt. The synergy between f1 and g1 in the salt assay was postulated based on exp with Rpr, but the validity of these experiments is dubious. I'm not sure there is sufficient evidence from Figures 6 and 7 to support a synergistic action between f1 and g1.

It is true that DAN-f1 alone is not necessary for mediating a high salt teaching signal based on ablation, optogenetic inhibition and even physiology. However, optogenetic activation alone shows a memory tested on a salt plate. Given the logic explained above that is accepted by several publications, we would like to keep the statement. Especially as the joined activation with DAN-g1 gives rise to significant higher or lower values after joined optogenetic activation or inactivation (Figure 5E and F, Figure 6E and F in the new version). Nevertheless, we have modified the sentence. In the text we describe these effects now as “these results may suggest that DAN-f1 and DAN-g1 encode aspects of the natural aversive high salt teaching signal under the conditions that we tested”. We think that this is an appropriate and three-fold restricted statement. Therefore, we would like to keep it in this restricted version. However, we are happy to reconsider this if the reviewer thinks it is critical. 

(10) I find the EM analysis hard to read. First of all, because of the two different graphical representations used in Fig. 8, wouldn't one be sufficient to make the point? Secondly, I could not grasp a take-home-message: what do we learn from the EM data? Do they explain any of the results? It seems to me that they don't provide an explanation of why some DL1 neurons respond to salt and others don't.

We understand that the EM analysis is hard to read and have now carefully rewritten this part of the manuscript. See also general concern 4 above. The main take home message is not to explain why some DL1 neurons respond to salt and other do not. This cannot be resolved due to the missing information on the salt perceiving receptor cells. Unfortunately, we miss the peripheral nervous system in the EM - the first layer of salt information processing. However, our analysis shows clearly that the 4 DANs have their own identity based on their connectivity. None of them is the same – but to a certain extent similarities exist. This nicely reflects the physiological and behavioral results. We have now clarified that in the result to ease the understanding for the readership. In addition, we also clearly state that we don’t address the point why some DL1 neurons respond to salt and why others don’t respond.

(11) Do the manipulations (activation and silencing) affect odor preference in the presence of salt? Did the authors test that the two odors do not drive different behaviors on the salty plate? Or did they only test the odor preference on plain agarose? Can we exclude a role for the DAN in driving multisensory-driven innate behavior?

Innate odor preferences are not changed by the presence of salt or even other tastants (this work but see also Schleyer et al 2015, Figure 3, Elife). Even the naïve choice between two odors is the same if tested in the presence of different tastants (Schleyer et al 2015, Figure 3, Elife). This shows – at least for the tested stimuli and conditions – that are similar to the ones that we use – that there is no multisensory-driven innate odor-taste behavior. Therefore – at least to our knowledge - experiments as the ones suggested by the reviewer were never done in larval odor-taste learning studies. Therefore, we suggest that DAN activation has no effect on innate larval behavior. However, we are happy to reconsider this if the reviewer thinks it is critical. 

(12) L 280: the authors generalize the conclusion to all DL1-DANs, but it does not apply to c1 and d1.

Thanks for this comment. We deleted that sentence as suggested and thus do not anymore generalize the conclusion to all DL-DANs.

(13) L345: I do not see the described differences in Fig. 8F, presynaptic sites of both types seem to appear in rather broad regions: could the author try to clarify this?

We understand that the anatomical description of the data is often hard to read. Especially to readers that are not used to these kind of figures. We have therefore modified the text to ease the understanding and clarify the difference in the labeled brain regions for the broad readership.

(14) L373: the conclusion on c1 is unsupported by data: this neuron responds to both salt and fructose (Figure 3 ) while the conclusion is purely based on EM data analysis.

The sentence is not a conclusion but a speculation and we also list the cell's response to positive and negative gustatory stimuli. Therefore, we do not understand exactly what the reviewer means here. However, we have tried to address the criticism and have revised the sentences.

(15) L385: the data on d1 seem to be inconsistent with Eschbach 2020, but the authors do not discuss if this is due to the differential vs absolute training, or perhaps the presence of the US during the test (which does not seem to be there in Eschbach, 2020) - is the training protocol really responsible for this inconsistency? For f1 the data seem to be consistent across these studies. The authors should clarify how the exp in Fig 6 differs from Eschbach, 2020 and how one could interpret the differences.

True. This concern is correct. We now discuss the difference in more detail. Eschbach et al. used Cs-Crimson as a genetic tool, a one odor paradigm with 3 training cycles, and no gustatory cues in their approach. These differences are now discussed in the new version of the manuscript.

(16) L460-475 A long part of this paragraph discusses the similarities between c1 and d1 and corresponding PPL1 neurons in the adult fly. However, c1 and d1 do not really show any phenotype in this paper, I'm not sure what we learn from this discussion and how much this paper can contribute to it. I would have wished for a discussion of how one could possibly reconcile the observed inconsistencies.

Based on the comments of the different reviewers several paragraphs in the discussion were modified. We agree that the part on the larval-adult comparison is quite long. Thus we have shortened it as suggested by the reviewer.

Minor corrections:

L28 "resultant association" maybe resulting instead.

L55 "animals derive benefit": remove derive.

L78 "composing 12,000 neurons": composed of.

L79 what is stable in a "stable behavioral assay"?

L104: 2 times cluste.

L122: "DL1 DANs are involved" in what?

Fig. 1 please check subpanels labels, D repeats.

L 362: "But how do individual neurons contribute to the teaching signal of the complete cluster?" I don't understand the question.

L364 I did not hear before about the "labeled line hypothesis" in this context - could the author clarify?

L368: edit "combinatorically".

L390: "current suppression" maybe acute suppression.

L 400 I'm not sure what is meant by "judicious functional configuration" and "redundancy". The functions of these cells are not redundant, and no straightforward prediction of their function can be done from their physiological response to salt.

Thanks a lot for your in detail review of our manuscript. We welcome your well-taken concerns and have made the requested changes for all points that you have raised.

Reviewer #2 (Recommendations For The Authors):

(1) In Figure 1 the reconstruction of pPAM and DL1 DANs shows the compartmentalized innervation of the larval MB. However, the images are a bit low in color contrast to appreciate the innervation well. In particular in panel B, it is hard to identify the innervated MB body structure. A schematic model of the larval MB and DAN innervation domains like in Fig. 2A would help to clarify the innervation pattern to the non-specialist.

We understand this concern and have changed figure 1 as suggested by the reviewer. A schematic model of the MB and DANs is now presented already in figure 1 as well as the according supplemental figure.

(2) Blue light itself can be aversive for larvae and thus interfere with the aversive learning paradigm. Does the given Illuminance (220 lux) used in these experiments affect the behavior and learning outcome?

Yes, in former times high intensities of blue light were necessary to trigger the first generation optogenetic tools. The high intensity blue light itself was able to establish an aversive memory (e.g. Rohwedder et al. 2016). Usage of the second generation optogenetic tools allowed us to strongly reduce the applied light intensity. Now we use 220 lux (equal to 60 µW/cm²). Please note that all Gal4 and UAS controls in the manuscript are nonsignificant different from zero. The mild blue light stimulation therefore does not serve as a teaching signal and has neither an aversive nor an appetitive effect. Furthermore, we use this mild light intensity for several other behavioral paradigms (locomotion, feeding, naïve preferences) and have never seen an effect on the behavior.

(3) Fig.2: Except for MB054B-Gal4 only the MB expression pattern is shown for other lines. Is there any additional expression in other cells of the brain? In the legend in line 761, the reporter does not show endogenous expression, rather it is a fluorescent reporter signal labeling the mushroom body.

The lines were initially identified by a screen on larval MB neurons done together with Jim Truman, Marta Zlatic and Bertram Gerber. Here full brain scans were always analyzed. These images can be seen in Eschbach et al. 2020, extended figure 1. Neither in their evaluation nor in our anatomical evaluation (using a different protocol) additional expression in brain cells was detectable. We also modified the figure legend as suggested.

(4) Fig.3: Precise n numbers per experiment should be stated in the figure legend.

True, we now present n numbers per experiment whenever necessary.

(5) Fig.4: Have the authors confirmed complete ablation of the targeted neuron using rpr/hid? Ablations can be highly incomplete depending on the onset and strength of Gal4 expression, leaving some functionality intact. While the ablation experiments are largely in line with the acute silencing of single DANs during high salt learning performed later on (Fig.7), there is potentially an interesting aspect of developmental compensation hidden in this data. Not a major point, but potentially interesting to check.

We agree with this criticism. We have not tested if the expression of hid,rpr in DL1 DANs does really ablate them. Therefore we did an additional experiment to show that. The new data is now present as a supplemental figure (Figure 4- figure supplement 6). The result shows that expression of hid,rpr ablates also DL1 DANs similar to earlier experiments where we used the same effectors to ablate serotoniergic neurons (Huser et al., 2012, figure 5).

(6) The performance index in Fig. 4 and 5 sometimes seems lower and the variability is higher than in some of the other experiments shown. Is this due to the high intrinsic variability of these particular experiments, or the background effects of the rpr/hid or splitGal4 lines?

The general variability of these experiments is within the expected and known borders. In these kind of experiments there is always some variation due to several external factors (e.g. experimental time over the year). Therefore it is always important to measure controls and experimental animals at the same time. Of course that’s what we did and we only compare directly results of individual datasets. But not between different datasets. This is further hampered given that the experiments of Figure 4 (now Figure 4- figure supplement 1) and Figure 5 (now Figure 4) differ in several parameters from other learning experiments presented later in the text. Optogenetic activation uses blue light stimulation instead of “real world” high salt. Most often direct activation of specific DANs in the brain is more stable than the external high salt stimulation. Also optogenetic inactivation uses blue light stimulation and also retinal supplemented food. Both factors can affect the measurement. We thus want to argue that it is for each experiment most often the particular parameters that affect the variability of the results rather than background effects of the rpr/hid and split-Gal4 lines.

(7) Fig.7: This is a neat experiment showing the effects of acute silencing of individual DL1 DANs. As silencing DAN-f1/g1 does not result in complete suppression of aversive learning, it would be highly interesting to test (or speculate about) additive or modulatory effects by the other DANs. Dan-c-1/d-1 also responds to high salt but does not show function on its own in these assays. I am aware that this is currently genetically not feasible. It would however be a nice future experiment.

True, we were intensively screening for DL1 cluster specific driver lines that cover all 4 DL1 neurons or other combinations than the ones we tested. Unfortunately, we did not succeed in identifying them. Nevertheless, we will further screen new genetic resources (e.g. Meissner et al., 2024, bioRxiv) to expand our approach in future experiments. Please also see our comment on concern 1 of reviewer 1 for further technical limitations and biological questions that can also potentially explain the absence of complete suppression of high salt learning and memory. Some of these limitations are now also mentioned and discussed in the new version of the manuscript.

(8) The discussion is excellent. I would just amend that it is likely that larval DAN-c1, which has high interconnectivity within the larval CNS, is likely integrating state-dependent network changes, similar to the role of some DANs in innate and state-dependent preference behavior. This might contribute to modulating learned behavior depending on the present (acute) and previous environmental conditions.

Thanks a lot for bringing this up. We rewrote this part and added a discussion on recent work on DAN-c1 function in larvae as well as results on DAN function in innate and state-dependent preference behavior.

(9) Citation in line 1115 missing access information: "Schnitzer M, Huang C, Luo J, Je Woo S, Roitman L, et al. 2023. Dopamine signals integrate innate and learned valences to regulate memory dynamics. Research Square".

Unfortunately this escaped our notice. The paper is now published in Nature: Huang, C., Luo, J., Woo, S.J. et al. Dopamine-mediated interactions between short- and long-term memory dynamics. Nature 634, 1141–1149 (2024). https://doi.org/10.1038/s41586-024-07819-w. We have now changed the citation. The new citation includes the missing access information.

Reviewer #3 (Recommendations For The Authors):

Regarding my issue about salt specificity in the public review, I want to make clear that I do not suggest additional experiments, but to be very careful in phrasing the conclusions, in particular whenever referring to the experiments with optogenetic activation. This includes presenting these experiments as "(salt) substitution" experiments - inferring that the optogenetic activation would substitute for a natural salt punishment. As important and interesting as the experiments are, they simply do not allow such an interpretation at this point.

Results, line 140ff: When presenting the results regarding TH-Gal4 crossed to ChR2-XXL, please cite Schroll et al. 2006 who demonstrated the same results for the first time.

Thanks for mentioning this. We now cite Schroll et al. 2006 here in the text of the manuscript.

Figure 3: The subfigure labels (ABC) are missing.

Unfortunately this escaped our notice. Thanks a lot – we have now corrected this mistake.

Figure 5: For I and L, it reads "salt replaced with fru", but the sketch on the left shows salt in the test. I assume that fructose was not actually present in the test, and therefore the figure can be misleading. I suggest separate sketches. Also, I and L are not mentioned in the figure legend.

True, this is rather confusing. Based on the well taken concern we have changed the figure by adding a new and correct scheme for sugar reward learning that does not symbolize fructose during test.

Figure S1: The experimental sketches for E,F and G,H seem to be mixed up.

We thank the reviewer for bringing this up. In the new version we corrected this mistake.

Figure S5: There are three sub-figures labelled with B. Please correct.

Again, thanks a lot. We made the suggested correction in Figure S5.

Discussion, line 353ff: this and the following sentences can be read as if the authors have discovered the DL-1 neurons as aversive teaching mediators in this study. However, Eschbach et al. 2020 already demonstrated very similar results regarding the optogenetic activation of single DL-1 DANs. I suggest to rephrase and cite Eschbach et al. 2020 at this point.

That is correct. Our focus was on the gustatory pathway. The original discovery was made by Eschbach et al. We have now corrected this in the discussion and clarified our contribution. It was never our intention to hide this work, as the laboratory was also involved. Nevertheless, this is an annoying omission on our side.

Line 385-387: this sentence is only correct with respect to Eschbach et al. 2020. Weiglein et al. 2021 used ChR2-XXL as an effector, but another training regimen.

We understand this criticism. Therefore, we changed the sentence as suggested by the reviewer. See also our response on concern 15 of reviewer 1.

Line 389ff: I do not understand this sentence. What is meant by persistent and current suppression of activity? If this refers to the behavioural experiments, it is misleading as in the hid, reaper experiments neurons are ablated and not suppressed in activity.

We made the requested changes in the text. It is true that the ablation of a neuron throughout larval life is different from constantly blocking the output of a persisting neuron.

Methods, line 615 ff: the performance index is said to be calculated as the difference between the two preferences, but the equation shows the average of the preferences.

Thanks a lot. We are sorry for the confusion. We have carefully rewritten this part of the methods section to avoid any misunderstanding.

When discussing the organization of the DL1 cluster, on several occasions I have the impression the authors use the terms "redundant" and "combinatorial" synonymously. I suggest to be more careful here. Redundancy implies that each DAN in principle can "do the job", whereas combinatorial coding implies that only a combination of DANs together can "do the job". If "the job" is establishing an aversive salt memory, the authors' results point to redundancy: no experimental manipulation totally abolished salt learning, implying that the non-manipulated neurons in each experiment sufficed to establish a memory; and several DANs, when individually activated, can establish an aversive memory, implying that each of them indeed can "do the job".

Based on this concern we have rewritten the discussion as suggested to be more precise when talking about redundancy or combinatorial coding of the aversive teaching signal. Basically, we have removed all the combinatorial terms and replaced them by the term “redundancy”.

The authors mix parametric and non-parametric statistical tests across the experiments dependent on whether the distribution of the data is normal or not. It would help readers if the authors would clearly state for which data which tests were used.

We understand the criticism and now have added an additional supplemental file that includes all the information on the statistical tests applied and the distribution of the data.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public Review):

Summary

In this study, the authors build upon previous research that utilized non-invasive EEG and MEG by analyzing intracranial human ECoG data with high spatial resolution. They employed a receptive field mapping task to infer the retinotopic organization of the human visual system. The results present compelling evidence that the spatial distribution of human alpha oscillations is highly specific and functionally relevant, as it provides information about the position of a stimulus within the visual field.

Using state-of-the-art modeling approaches, the authors not only strengthen the existing evidence for the spatial specificity of the human dominant rhythm but also provide new quantification of its functional utility, specifically in terms of the size of the receptive field relative to the one estimated based on broad band activity.

We thank the reviewer for their positive summary.

Weakness 1.1

The present manuscript currently omits the complementary view that the retinotopic map of the visual system might be related to eye movement control. Previous research in non-human primates using microelectrode stimulation has clearly shown that neuronal circuits in the visual system possess motor properties (e.g. Schiller and Styker 1972, Schiller and Tehovnik 2001). More recent work utilizing Utah arrays, receptive field mapping, and electrical stimulation further supports this perspective, demonstrating that the retinotopic map functions as a motor map. In other words, neurons within a specific area responding to a particular stimulus location also trigger eye movements towards that location when electrically stimulated (e.g. Chen et al. 2020).

Similarly, recent studies in humans have established a link between the retinotopic variation of human alpha oscillations and eye movements (e.g., Quax et al. 2019, Popov et al. 2021, Celli et al. 2022, Liu et al. 2023, Popov et al. 2023). Therefore, it would be valuable to discuss and acknowledge this complementary perspective on the functional relevance of the presented evidence in the discussion section.

The reviewer notes that we do not discuss the oculomotor system and alpha oscillations. We agree that the literature relating eye movements and alpha oscillations are relevant.

At the Reviewer’s suggestion, we added a paragraph on this topic to the first section of the Discussion (section 3.1, “Other studies have proposed … “).

Reviewer #2 (Public Review):

Summary:

In this work, Yuasa et al. aimed to study the spatial resolution of modulations in alpha frequency oscillations (~10Hz) within the human occipital lobe. Specifically, the authors examined the receptive field (RF) tuning properties of alpha oscillations, using retinotopic mapping and invasive electroencephalogram (iEEG) recordings. The authors employ established approaches for population RF mapping, together with a careful approach to isolating and dissociating overlapping, but distinct, activities in the frequency domain. Whereby, the authors dissociate genuine changes in alpha oscillation amplitude from other superimposed changes occurring over a broadband range of the power spectrum. Together, the authors used this approach to test how spatially tuned estimated RFs were when based on alpha range activity, vs. broadband activities (focused on 70-180Hz). Consistent with a large body of work, the authors report clear evidence of spatially precise RFs based on changes in alpha range activity. However, the size of these RFs were far larger than those reliably estimated using broadband range activity at the same recording site. Overall, the work reflects a rigorous approach to a previously examined question, for which improved characterization leads to improved consistency in findings and some advance of prior work.

We thank the reviewer for the summary.

Strengths:

Overall, the authors take a careful and well-motivated approach to data analyses. The authors successfully test a clear question with a rigorous approach and provide strong supportive findings. Firstly, well-established methods are used for modeling population RFs. Secondly, the authors employ contemporary methods for dissociating unique changes in alpha power from superimposed and concomitant broadband frequency range changes. This is an important confound in estimating changes in alpha power not employed in prior studies. The authors show this approach produces more consistent and robust findings than standard band-filtering approaches. As noted below, this approach may also account for more subtle differences when compared to prior work studying similar effects.

We thank the reviewer for the positive comments.

Weaknesses:

Weakness 2.1 Theoretical framing:

The authors frame their study as testing between two alternative views on the organization, and putative functions, of occipital alpha oscillations: i) alpha oscillation amplitude reflects broad shifts in arousal state, with large spatial coherence and uniformity across cortex; ii) alpha oscillation amplitude reflects more specific perceptual processes and can be modulated at local spatial scales. However, in the introduction this framing seems mostly focused on comparing some of the first observations of alpha with more contemporary observations. Therefore, I read their introduction to more reflect the progress in studying alpha oscillations from Berger's initial observations to the present. I am not aware of a modern alternative in the literature that posits alpha to lack spatially specific modulations. I also note this framing isn't particularly returned to in the discussion.

This was helpful feedback. We have rewritten nearly the entire Introduction to frame the study differently. The emphasis is now on the fact that several intracranial studies of spatial tuning of alpha (in both human and macaque) tend to show increases in alpha due to visual stimulation, in contrast to a century of MEG/EEG studies, from Berger to the present, showing decreases. We believe that the discrepancy is due to an interaction between measurement type and brain signals. Specifically, intracranial measurements sum decreases in alpha oscillations and increases in broadband power on the same trials, and both signals can be large. In contrast, extracranial measures are less sensitive to the broadband signals and mostly just measure the alpha oscillation. Our study reconciles this discrepancy by removing the baseline broadband power increases, thereby isolating the alpha oscillation, and showing that with iEEG spatial analyses, the alpha oscillation decreases with visual stimulation, consistent with EEG and MEG results.

Weakness 2.2 A second important variable here is the spatial scale of measurement.

It follows that EEG based studies will capture changes in alpha activity up to the limits of spatial resolution of the method (i.e. limited in ability to map RFs). This methodological distinction isn't as clearly mentioned in the introduction, but is part of the author's motivation. Finally, as noted below, there are several studies in the literature specifically addressing the authors question, but they are not discussed in the introduction.

The new Introduction now explicitly contrasts EEG/MEG with intracranial studies and refers to the studies below.

Weakness 2.3 Prior studies:

There are important findings in the literature preceding the author's work that are not sufficiently highlighted or cited. In general terms, the spatio-temporal properties of the EEG/iEEG spectrum are well known (i.e. that changes in high frequency activity are more focal than changes in lower frequencies). Therefore, the observations of spatially larger RFs for alpha activities is highly predicted. Specifically, prior work has examined the impact of using different frequency ranges to estimate RF properties, for example ECoG studies in the macaque by Takura et al. NeuroImage (2016) [PubMed: 26363347], as well as prior ECoG work by the author's team of collaborators (Harvey et al., NeuroImage (2013) [PubMed: 23085107]), as well as more recent findings from other groups (Luo et al., (2022) BioRxiv: https://doi.org/10.1101/2022.08.28.505627). Also, a related literature exists for invasively examining RF mapping in the time-voltage domain, which provides some insight into the author's findings (as this signal will be dominated by low-frequency effects). The authors should provide a more modern framing of our current understanding of the spatial organization of the EEG/iEEG spectrum, including prior studies examining these properties within the context of visual cortex and RF mapping. Finally, I do note that the author's approach to these questions do reflect an important test of prior findings, via an improved approach to RF characterization and iEEG frequency isolation, which suggests some important differences with prior work.

Thank you for these references and suggestions. Some of the references were already included, and the others have been added.

There is one issue where we disagree with the Reviewer, namely that “the observations of spatially larger RFs for alpha activities is highly predicted”. We agree that alpha oscillations and other low frequency rhythms tend to be less focal than high frequency responses, but there are also low frequency non-rhythmic signals, and these can be spatially focal. We show this by demonstrating that pRFs solved using low frequency responses outside the alpha band (both below and above the alpha frequency) are small, similar to high frequency broadband pRFs, but differing from the large pRFs associated with alpha oscillations. Hence we believe the degree to which signals are focal is more related to the degree of rhythmicity than to the temporal frequency per se. While some of these results were already in the supplement, we now address the issue more directly in the main text in a new section called, “2.5 The difference in pRF size is not due to a difference in temporal frequency.”

We incorporated additional references into the Introduction, added a new section on low frequency broadband responses to the Results (section 2.5), and expanded the Discussion (section 3.2) to address these new references.

Weakness 2.4 Statistical testing:

The authors employ many important controls in their processing of data. However, for many results there is only a qualitative description or summary metric. It appears very little statistical testing was performed to establish reported differences. Related to this point, the iEEG data is highly nested, with multiple electrodes (observations) coming from each subject, how was this nesting addressed to avoid bias?

We reviewed the primary claims made in the manuscript and for each claim, we specify the supporting analyses and, where appropriate, how we address the issue of nesting. Although some of these analyses were already in the manuscript, many of them are new, including all of the analyses concerning nesting. We believe that putting this information in one place will be useful to the reader, and we now include this text as a new section in supplement, Graphical and statistical support for primary claims.

Reviewer #2 (Recommendations For The Authors):

Recommendation 2.1:

Data presentation: In several places, the authors discuss important features of cortical responses as measured with iEEG that need to be carefully considered. This is totally appropriate and a strength of the author's work, however, I feel the reader would benefit from more depiction of the time-domain responses, to help better understand the authors frequency domain approach. For example, Figure 1 would benefit from showing some form of voltage trace (ERP) and spectrogram, not just the power spectra. In addition, part (a) of Figure 1 could convey some basic information about the timing of the experimental paradigm.

We changed panel A of Figure 1 to include the timing of the experimental paradigm, and we added panels C and D to show the electrode time series before and after regression out of the ERP.

Recommendation 2.2

Update introduction to include references to prior EEG/iEEG work on spatial distribution across frequency spectrum, and importantly, prior work mapping RFs with different frequencies.

We have addressed this issue and re-written our introduction. Please refer to our response in Public Review for further details.

Recommendation 2.3

Figure 3 has several panels and should be labeled to make it easier to follow.The dashed line in lower power spectra isn't defined in a legend and is missing from the upper panel - please clarify.

We updated Figure 3 and reordered the panels to clarify how we computed the summary metrics in broadband and alpha for each stimulus location (i.e., the “ratio” values plotted in panel B). We also simplified the plot of the alpha power spectrum. It now shows a dashed line representing a baseline-corrected response to the mapping stimulus, which is defined in the legend and explained in the caption.

Recommendation 2.4

Power spectra are always shown without error shading, but they are mean estimates.

We added error shading to Figures 1, 2 and 3.

Recommendation 2.5

The authors deal with voltage transients in response to visual stimulation, by subtracting out the trail averaged mean (commonly performed). However, the efficacy of this approach depends on signal quality and so some form of depiction for this processing step is needed.

We added a depiction of the processing steps for regressing out the averaged responses in Figure 1 in an example electrode (panels C and D). We also show in the supplement the effect of regressing out the ERP on all the electrode pRFs. We have added Supplementary Figure 1-2.

Recommendation 2.6

I have a similar request for the authors latency correction of their data, where they identified a timing error and re-aligned the data without ground truth. Again, this is appropriate, but some depiction of the success of this correction is very critical for confirming the integrity of the data.

We now report more detail on the latency correction, and also point out that any small error in the estimate would not affect our conclusions (4.6 ECoG data analysis | Data epoching). The correction was important for a prior paper on temporal dynamics (Groen et al, 2022), which used data from the same participants and estimated the latency of responses. In this paper, our analyses are in the spectral domain (and discard phase), so small temporal shifts are not critical. We now also link to the public code associated with that paper, which implemented the adjustment and quantified the uncertainty in the latency adjustment.

More details on latency adjustment provided in section 4.6.

Recommendation 2.7

In many places the authors report their data shows a 'summary' value, please clarify if this means averaging or summation over a range.

For both broadband and alpha, we derive one summary value (a scalar) for trial for each stimulus. For broadband, the summary metric is the ratio of power during a given trial and power during blanks, where power in a trial is the geometric mean of the power at each frequency within the defined band). This is equation 3 in the methods, which is now referred to the first time that summary metrics are mentioned in the results.  For alpha, the summary metric is the height of the Gaussian from our model-based approach. This is in equations 1 and 2, and is also now referred to the first time summary metrics are mentioned in the results.

We added explanation of the summary metrics in the figure captions and results where they are first used, and also referred to the equations in the methods where they are defined.

Recommendation 2.8

The authors conclude: "we have discovered that spectral power changes in the alpha range reflect both suppression of alpha oscillations and elevation of broadband power." It might not have been the intention, but 'discovered' seems overstated.

We agree and changed this sentence.

Recommendation 2.9

Supp Fig 9 is a great effort by the authors to convey their findings to the reader, it should be a main figure.

We are glad you found Supplementary Figure 9 valuable. We moved this figure to the main text.

Reviewer #3 (Public Review):

Summary:

This study tackles the important subject of sensory driven suppression of alpha oscillations using a unique intracranial dataset in human patients. Using a model-based approach to separate changes in alpha oscillations from broadband power changes, the authors try to demonstrate that alpha suppression is spatially tuned, with similar center location as high broadband power changes, but much larger receptive field. They also point to interesting differences between low-order (V1-V3) and higher-order (dorsolateral) visual cortex. While I find some of the methodology convincing, I also find significant parts of the data analysis, statistics and their presentation incomplete. Thus, I find that some of the main claims are not sufficiently supported. If these aspects could be improved upon, this study could potentially serve as an important contribution to the literature with implications for invasive and non-invasive electrophysiological studies in humans.

We thank the reviewer for the summary.

Strengths:

The study utilizes a unique dataset (ECOG & high-density ECOG) to elucidate an important phenomenon of visually driven alpha suppression. The central question is important and the general approach is sound. The manuscript is clearly written and the methods are generally described transparently (and with reference to the corresponding code used to generate them). The model-based approach for separating alpha from broadband power changes is especially convincing and well-motivated. The link to exogenous attention behavioral findings (figure 8) is also very interesting. Overall, the main claims are potentially important, but they need to be further substantiated (see weaknesses).

We thank the reviewer for the positive comments.

Weaknesses:

I have three major concerns:

Weakness 3.1. Low N / no single subject results/statistics:

The crucial results of Figure 4,5 hang on 53 electrodes from four patients (Table 2). Almost half of these electrodes (25/53) are from a single subject. Data and statistical analysis seem to just pool all electrodes, as if these were statistically independent, and without taking into account subject-specific variability. The mean effect per each patient was not described in text or presented in figures. Therefore, it is impossible to know if the results could be skewed by a single unrepresentative patient. This is crucial for readers to be able to assess the robustness of the results. N of subjects should also be explicitly specified next to each result.

We have added substantial changes to deal with subject specific effects, including new results and new figures.

• Figure 4 now shows variance explained by the alpha pRF broken down by each participant for electrodes in V1 to V3. We also now show a similar figure for dorsolateral electrodes in Supplementary Figure 4-2.

• Figure 5, which shows results from individual electrodes in V1 to V3, now includes color coding of electrodes by participant to make it clear how the electrodes group with participant. Similarly, for dorsolateral electrodes, we show electrodes grouped by participant in Supplementary Figure 5-1. Same for Supplementary Figure 6-2.

• Supplementary Figure 7-2 now shows the benefits of our model-based approach for estimating alpha broken down by individual participants.

• We also now include a new section in the supplement that summarizes for every major claim, what the supporting data are and how we addressed the issue of nesting electrodes by participant, section Graphical and statistical support for primary claims.

Weakness 3.2. Separation between V1-V3 and dorsolateral electrodes:

Out of 53 electrodes, 27 were doubly assigned as both V1-V3 and dorsolateral (Table 2, Figures 4,5). That means that out of 35 V1-V3 electrodes, 27 might actually be dorsolateral. This problem is exasperated by the low N. for example all the 20 electrodes in patient 8 assigned as V1-V3 might as well be dorsolateral. This double assignment didn't make sense to me and I wasn't convinced by the authors' reasoning. I think it needlessly inflates the N for comparing the two groups and casts doubts on the robustness of these analyses.

Electrode assignment was probabilistic to reflect uncertainty in the mapping between location and retinotopic map. The probabilistic assignment is handled in two ways.

(1) For visualizing results of single electrodes, we simply go with the maximum probability, so no electrode is visualized for both groups of data. For example, Figure 5a (V1-V3) and supplementary Figure 5-1a (dorsolateral electrodes) have no electrodes in common: no electrode is in both plots.

(2) For quantitative summaries, we sample the electrodes probabilistically (for example Figures 4, 5c). So, if for example, an electrode has a 20% chance of being in V1 to V3, and 30% chance of being in dorsolateral maps, and a 50% chance of being in neither, the data from that electrode is used in only 20% of V1-V3 calculations and 30% of dorsolateral calculations. In 50% of calculations, it is not used at all. This process ensures that an electrode with uncertain assignment makes no more contribution to the results than an electrode with certain assignment. An electrode with a low probability of being in, say, V1-V3, makes little contribution to any reported results about V1-V3. This procedure is essentially a weighted mean, which the reviewer suggests in the recommendations. Thus, we believe there is not a problem of “double counting”.

The alternative would have been to use maximum probability for all calculations. However, we think that doing so would be misleading, since it would not take into account uncertainty of assignment, and would thus overstate differences in results between the maps.

We now clarify in the Results that for probabilistic calculations, the contribution of an electrode is limited by the likelihood of assignment (Section 2.3). We also now explain in the methods why we think probabilistic sampling is important.

Weakness 3.3. Alpha pRFs are larger than broadband pRFs:

First, as broadband pRF models were on average better fit to the data than alpha pRF models (dark bars in Supp Fig 3. Top row), I wonder if this could entirely explain the larger Alpha pRF (i.e. worse fits lead to larger pRFs). There was no anlaysis to rule out this possibility.

We addressed this question in a new paragraph in Discussion section 3.1 (“What is the function of the large alpha pRFs?”, paragraph beginning… “Another possible interpretation is that the poorer model fit in the alpha pRF is due to lower signal-to-noise”). This paragraph both refers to prior work on the relationship between noise and pRF size and to our own control analyses (Supplementary Figure 5-2).

Weakness 3.4 Statistics

Second, examining closely the entire 2.4 section there wasn't any formal statistical test to back up any of the claims (not a single p-value is mentioned). It is crucial in my opinion to support each of the main claims of the paper with formal statistical testing.

We agree that it is important for the reader to be able to link specific results and analyses to specific claims. We are not convinced that null hypothesis statistical testing is always the best approach. This is a topic of active debate in the scientific community.

We added a new section that concisely states each major claim and explicitly annotates the supporting evidence. (Section 4.7). Please also refer to our responses to Reviewer #2 regarding statistical testing (Reviewer weakness 2.4 “Statistical testing”)

Weakness 3.5 Summary

While I judge these issues as crucial, I can also appreciate the considerable effort and thoughtfulness that went into this study. I think that addressing these concerns will substantially raise the confidence of the readership in the study's findings, which are potentially important and interesting.

We again thank the reviewer for the positive comments.

Reviewer #3 (Recommendations For The Authors):

Suggestions for how to address the three major concerns:

Suggestion 3.1.

I am very well aware that it's very hard to have n=30 in a visual cortex ECOG study. That's fine. Best practice would be to have a linear mixed effects model with patients as a random effect. However, for some figures with just 3-4 patients (Figure 4,5) the sample size might be too small even for that. At the very minimum, I would expect to show in figures/describe in text all results per patient (perhaps one can do statistics within each patient, and show for each patient that the effect is significant). Even in primate studies with just two subjects it is expected to show that the results replicate for subject A and B. It is necessary to show that your results don't depend on a single unrepresentative subject. And if they do, at least be transparent about it.

We have addressed this thoroughly. Please see response to Weakness 3.1 (“Low N / no single subject results/statistics”).

Suggestion 3.2.

I just don't get it. I would simply assign an electrode to V1-V3 or dorsolateral cortex based on which area has the highest probability. It doesn't make sense to me that an electrode that has 60% of being in dorsolateral cortex and only 10% to be in V1-V3 would be assigned as both V1-V3 and dorsolateral. Also, what's the rationale to include such electrode in the analysis for let's say V1-V3 (we have weak evidence to believe it's there)? I would either assign electrodes based on the highest probability, or alternatively do a weighted mean based on the probability of each electrode belonging to each region group (e.g. electrode with 40% to be in V1-V3, will get twice the weight as an electrode who has 20% to be in V1-V3) but this is more complicated.

We have addressed this issue. Please refer to our response in Public Review (“Weakness 3.2 Separation between V1-V3 and dorsolateral”) for details.

Suggestion 3.3.

First, to exclude the possibility that alpha pRF are larger simply because they have a worse fit to the neural data, I would show if there is a correlation between the goodnessof-fit and pRF size (for alpha and broadband signals, separately). No [negative] correlation between goodness-of-fit and pRF size would be a good sign. I would also compare alpha & broadband receptive field size when controlling for the goodness-of-fit (selecting electrodes with similar goodness-of-fit for both signals). If the results replicate this way it would be convincing.

Second, there are no statistical tests in section 2.4, possibly also in others. Even if you employ bootstrap / Monte-Carlo resampling methods you can extract a p-value.

We have addressed this issue. Please refer to our response in Public Review Point 3.3 (“Alpha pRFs are larger than broadband pRFs”) for further details.

Suggestion 3.4.

Also, I don't understand the resampling procedure described in lines 652-660: "17.7 electrodes were assigned to V1-V3, 23.2 to dorsolateral, and 53 to either " - but 17.7 + 23.2 doesn't add up to 53. It also seems as if you assign visual areas differently in this resampling procedure than in the real data - "and randomly assigned each electrode to a visual area according to the Wang full probability distributions". If you assign in your actual data 27 electrodes to both visual areas, the same should be done in the resampling procedure (I would expect exactly 35 V1-V3 and 45 dorsolateral electrodes in every resampling, just the pRFs will be shuffled across electrodes).

We apologize for the confusion.

We fixed the sentence above, clarified the caption to Table 2, and also explained the overall strategy of probabilistic resampling better. See response to Public Review point 3.2 for details.

Suggestion 3.5.

These are rather technical comments but I believe they are crucial points to address in order to support your claims. I genuinely think your results are potentially interesting and important but these issues need to be first addressed in a revision. I also think your study may carry implications beyond just the visual domain, as alpha suppression is observed for different sensory modalities and cortical regions. Might be useful to discuss this in the discussion section.

Agree. We added a paragraph on this point to the Discussion (very end of 3.2).

Author response:

The following is the authors’ response to the original reviews

We thank the reviewers for their thoughtful feedback. We have made substantial revisions to the manuscript to address each of their comments, as we detail below. We want to highlight one major change in particular that addresses a concern raised by both reviewers: the role of the drift rate in our models. Motivated by their astute comments, we went back through our models and realized that we had made a particular assumption that deserved more scrutiny. We previously assumed that the process of encoding the observations made correct use of the objective, generative correlation, but then the process of calculating the weight of evidence used a mis-scaled, subjective version of the correlation. These assumptions led us to scale the drift rate in the model by a term that quantified how the standard deviation of the observation distribution was affected by the objective correlation (encoding), but to scale the bound height by the subjective estimate of the correlation (evidence weighing). However, we realized that encoding may also depend on the subjective correlation experienced by the participant. We have now tested several alternative models and found that the best-fitting model assumes that a single, subjective estimate of the correlation governs both encoding and evidence weighing. An important consequence of updating our models in this way is that we can now account for the behavioral data without needing the additional correlation-dependent drift terms (which, as reviewer #2 pointed out, were difficult to explain).

We also note that we changed the title slightly, replacing “weighting” with “weighing” for consistency with our usage throughout the manuscript.

Please see below for more details about this important point and our responses to the reviewers’ specific concerns. 

Public Reviews:

Reviewer #1 (Public review):

Summary:

The behavioral strategies underlying decisions based on perceptual evidence are often studied in the lab with stimuli whose elements provide independent pieces of decision-related evidence that can thus be equally weighted to form a decision. In more natural scenarios, in contrast, the information provided by these pieces is often correlated, which impacts how they should be weighted. Tardiff, Kang & Gold set out to study decisions based on correlated evidence and compare the observed behavior of human decision-makers to normative decision strategies. To do so, they presented participants with visual sequences of pairs of localized cues whose location was either uncorrelated, or positively or negatively correlated, and whose mean location across a sequence determined the correct choice. Importantly, they adjusted this mean location such that, when correctly weighted, each pair of cues was equally informative, irrespective of how correlated it was. Thus, if participants follow the normative decision strategy, their choices and reaction times should not be impacted by these correlations. While Tardiff and colleagues found no impact of correlations on choices, they did find them to impact reaction times, suggesting that participants deviated from the normative decision strategy. To assess the degree of this deviation, Tardiff et al. adjusted drift-diffusion models (DDMs) for decision-making to process correlated decision evidence. Fitting these models to the behavior of individual participants revealed that participants considered correlations when weighing evidence, but did so with a slight underestimation of the magnitude of this correlation. This finding made Tardiff et al. conclude that participants followed a close-to-normative decision strategy that adequately took into account correlated evidence.

Strengths:

The authors adjust a previously used experimental design to include correlated evidence in a simple, yet powerful way. The way it does so is easy to understand and intuitive, such that participants don't need extensive training to perform the task. Limited training makes it more likely that the observed behavior is natural and reflective of everyday decision-making. Furthermore, the design allowed the authors to make the amount of decision-related evidence equal across different correlation magnitudes, which makes it easy to assess whether participants correctly take account of these correlations when weighing evidence: if they do, their behavior should not be impacted by the correlation magnitude.

The relative simplicity with which correlated evidence is introduced also allowed the authors to fall back to the well-established DDM for perceptual decisions, which has few parameters, is known to implement the normative decision strategy in certain circumstances, and enjoys a great deal of empirical support. The authors show how correlations ought to impact these parameters, and which changes in parameters one would expect to see if participants misestimate these correlations or ignore them altogether (i.e., estimate correlations to be zero). This allowed them to assess the degree to which participants took into account correlations on the full continuum from perfect evidence weighting to complete ignorance. With this, they could show that participants in fact performed rational evidence weighting if one assumed that they slightly underestimated the correlation magnitude.

Weaknesses:

The experiment varies the correlation magnitude across trials such that participants need to estimate this magnitude within individual trials. This has several consequences:

(1) Given that correlation magnitudes are estimated from limited data, the (subjective) estimates might be biased towards their average. This implies that, while the amount of evidence provided by each 'sample' is objectively independent of the correlation magnitude, it might subjectively depend on the correlation magnitude. As a result, the normative strategy might differ across correlation magnitudes, unlike what is suggested in the paper. In fact, it might be the case that the observed correlation magnitude underestimates corresponds to the normative strategy.

We thank the reviewer for raising this interesting point, which we now address directly with new analyses including model fits (pp. 15–24). These analyses show that the participants were computing correlation-dependent weights of evidence from observation distributions that reflected suboptimal misestimates of correlation magnitudes. This strategy is normative in the sense that it is the best that they can do, given the encoding suboptimality. However, as we note in the manuscript, we do not know the source of the encoding suboptimality (pp. 23–24). We thus do not know if there might be a strategy they could have used to make the encoding more optimal.

(2) The authors link the normative decision strategy to putting a bound on the log-likelihood ratio (logLR), as implemented by the two decision boundaries in DDMs. However, as the authors also highlight in their discussion, the 'particle location' in DDMs ceases to correspond to the logLR as soon as the strength of evidence varies across trials and isn't known by the decision maker before the start of each trial. In fact, in the used experiment, the strength of evidence is modulated in two ways:

(i) by the (uncorrected) distance of the cue location mean from the decision boundary (what the authors call the evidence strength) and

(ii) by the correlation magnitude. Both vary pseudo-randomly across trials, and are unknown to the decision-maker at the start of each trial. As previous work has shown (e.g. Kiani & Shadlen (2009), Drugowitsch et al. (2012)), the normative strategy then requires averaging over different evidence strength magnitudes while forming one's belief. This averaging causes the 'particle location' to deviate from the logLR. This deviation makes it unclear if the DDM used in the paper indeed implements the normative strategy, or is even a good approximation to it.

We appreciate this subtle, but important, point. We now clarify that the DDM we use includes degrees of freedom that are consistent with normative decision processes that rely on the imperfect knowledge that participants have about the generative process on each trial, specifically: 1) a single drift-rate parameter that is fit to data across different values of the mean of the generative distribution, which is based on the standard assumption for these kinds of task conditions in which stimulus strength is varied randomly from trial-to-trial and thus prevents the use of exact logLR (which would require stimulus strength-specific scale factors; Gold and Shadlen, 2001); 2) the use of a collapsing bound, which in certain cases (including our task) is thought to support a stimulus strength-dependent calibration of the decision variable to optimize decisions (Drugowitsch et al, 2012); and 3) free parameters (one per correlation) to account for subjective estimates of the correlation, which affected the encoding of the observations that are otherwise weighed in a normative manner in the best-fitting model.

Also, to clarify our terminology, we define the objective evidence strength as the expected logLR in a given condition, which for our task is dependent on both the distance of the mean from the decision boundary and the correlation (p. 7). 

Given that participants observe 5 evidence samples per second and on average require multiple seconds to form their decisions, it might be that they are able to form a fairly precise estimate of the correlation magnitude within individual trials. However, whether this is indeed the case is not clear from the paper.

These points are now addressed directly in Results (pp. 23–24) and Figure 7 supplemental figures 1–3. Specifically, we show that, as the reviewer correctly surmised above, empirical correlations computed on each trial tended to be biased towards zero (Fig 7–figure supplement 1). However, two other analyses were not consistent with the idea that participants’ decisions were based on trial-by-trial estimates of the empirical correlations: 1) those with the shortest RTs did not have the most-biased estimates (Fig 7–figure supplement 2), and 2) there was no systematic relationship between objective and subjective fit correlations across participants (Fig 7–figure supplement 3).

Furthermore, the authors capture any underestimation of the correlation magnitude by an adjustment to the DDM bound parameter. They justify this adjustment by asking how this bound parameter needs to be set to achieve correlation-independent psychometric curves (as observed in their experiments) even if participants use a 'wrong' correlation magnitude to process the provided evidence. Curiously, however, the drift rate, which is the second critical DDM parameter, is not adjusted in the same way. If participants use the 'wrong' correlation magnitude, then wouldn't this lead to a mis-weighting of the evidence that would also impact the drift rate? The current model does not account for this, such that the provided estimates of the mis-estimated correlation magnitudes might be biased.

We appreciate this valuable comment, and we agree that we previously neglected the potential impact of correlation misestimates on evidence strength. As we now clarify, the correlation enters these models in two ways: 1) via its effect on how the observations are encoded, which involves scaling both the drift and the bound; and 2) via its effect on evidence weighing, which involves scaling only the bound (pp. 15–18). We previously assumed that only the second form of scaling might involve a subjective (mis-)estimate of the correlation. We now examine several models that also include the possibility of either or both forms using subjective correlation estimates. We show that a model that assumes that the same subjective estimate drives both encoding and weighing (the “full-rho-hat” model) best accounts for the data. This model provides better fits (after accounting for differences in numbers of parameters) than models with: 1) no correlation-dependent adjustments (“base” model), 2) separate drift parameters for each correlation condition (“drift” model), 3) optimal (correlation-dependent) encoding but suboptimal weighing (“bound-rho-hat” model, which was our previous formulation), 4) suboptimal encoding and weighing (“scaled-rho-hat” model), and 5) optimal encoding but suboptimal weighing and separate correlation-dependent adjustments to the drift rate (“boundrho-hat plus drift” model). We have substantially revised Figures 5–7 and the associated text to address these points.

Lastly, the paper makes it hard to assess how much better the participants' choices would be if they used the correct correlation magnitudes rather than underestimates thereof. This is important to know, as it only makes sense to strictly follow the normative strategy if it comes with a significant performance gain.

We now include new analyses in Fig. 7 that demonstrate how much participants' choices and RT deviate from: 1) an ideal observer using the objective correlations, and 2) an observer who failed to adjust for the fit subjective correlation when weighing the evidence (i.e., using the subjective correlation for encoding but a correlation of zero for weighing). We now indicate that participants’ performance was quite close to that predicted by the ideal observer (using the true, objective correlation) for many conditions. Thus, we agree that they might not have had the impetus to optimize the decision process further, assuming it were possible under these task conditions.

Reviewer #2 (Public review):

Summary:

This study by Tardiff, Kang & Gold seeks to: i) develop a normative account of how observers should adapt their decision-making across environments with different levels of correlation between successive pairs of observations, and ii) assess whether human decisions in such environments are consistent with this normative model.

The authors first demonstrate that, in the range of environments under consideration here, an observer with full knowledge of the generative statistics should take both the magnitude and sign of the underlying correlation into account when assigning weight in their decisions to new observations: stronger negative correlations should translate into stronger weighting (due to the greater information furnished by an anticorrelated generative source), while stronger positive correlations should translate into weaker weighting (due to the greater redundancy of information provided by a positively correlated generative source). The authors then report an empirical study in which human participants performed a perceptual decision-making task requiring accumulation of information provided by pairs of perceptual samples, under different levels of pairwise correlation. They describe a nuanced pattern of results with effects of correlation being largely restricted to response times and not choice accuracy, which could partly be captured through fits of their normative model (in this implementation, an extension of the well-known drift-diffusion model) to the participants' behaviour while allowing for misestimation of the underlying correlations.

Strengths:

As the authors point out in their very well-written paper, appropriate weighting of information gathered in correlated environments has important consequences for real-world decisionmaking. Yet, while this function has been well studied for 'high-level' (e.g. economic) decisions, how we account for correlations when making simple perceptual decisions on well-controlled behavioural tasks has not been investigated. As such, this study addresses an important and timely question that will be of broad interest to psychologists and neuroscientists. The computational approach to arrive at normative principles for evidence weighting across environments with different levels of correlation is very elegant, makes strong connections with prior work in different decision-making contexts, and should serve as a valuable reference point for future studies in this domain. The empirical study is well designed and executed, and the modelling approach applied to these data showcases a deep understanding of relationships between different parameters of the drift-diffusion model and its application to this setting. Another strength of the study is that it is preregistered.

Weaknesses:

In my view, the major weaknesses of the study center on the narrow focus and subsequent interpretation of the modelling applied to the empirical data. I elaborate on each below:

Modelling interpretation: the authors' preference for fitting and interpreting the observed behavioural effects primarily in terms of raising or lowering the decision bound is not well motivated and will potentially be confusing for readers, for several reasons. First, the entire study is conceived, in the Introduction and first part of the Results at least, as an investigation of appropriate adjustments of evidence weighting in the face of varying correlations. The authors do describe how changes in the scaling of the evidence in the drift-diffusion model are mathematically equivalent to changes in the decision bound - but this comes amidst a lengthy treatment of the interaction between different parameters of the model and aspects of the current task which I must admit to finding challenging to follow, and the motivation behind shifting the focus to bound adjustments remained quite opaque. 

We appreciate this valuable feedback. We have revised the text in several places to make these important points more clearly. For example, in the Introduction we now clarify that “The weight of evidence is computed as a scaled version of each observation (the scaling can be applied to the observations or to the bound, which are mathematically equivalent; Green and Swets, 1966) to form the logLR” (p. 3). We also provide more details and intuition in the Results section for how and why we implemented the DDM the way we did. In particular, we now emphasize that the correlation enters these models in two ways: 1) via its effect on encoding the observations, which scales both the drift and the bound; and 2) via its effect on evidence weighing, which scales only the bound (pp. 15–18).

Second, and more seriously, bound adjustments of the form modelled here do not seem to be a viable candidate for producing behavioural effects of varying correlations on this task. As the authors state toward the end of the Introduction, the decision bound is typically conceived of as being "predefined" - that is, set before a trial begins, at a level that should strike an appropriate balance between producing fast and accurate decisions. There is an abundance of evidence now that bounds can change over the course of a trial - but typically these changes are considered to be consistently applied in response to learned, predictable constraints imposed by a particular task (e.g. response deadlines, varying evidence strengths). In the present case, however, the critical consideration is that the correlation conditions were randomly interleaved across trials and were not signaled to participants in advance of each trial - and as such, what correlation the participant would encounter on an upcoming trial could not be predicted. It is unclear, then, how participants are meant to have implemented the bound adjustments prescribed by the model fits. At best, participants needed to form estimates of the correlation strength/direction (only possible by observing several pairs of samples in sequence) as each trial unfolded, and they might have dynamically adjusted their bounds (e.g. collapsing at a different rate across correlation conditions) in the process. But this is very different from the modelling approach that was taken. In general, then, I view the emphasis on bound adjustment as the candidate mechanism for producing the observed behavioural effects to be unjustified (see also next point).

We again appreciate this valuable feedback and have made a number of revisions to try to clarify these points. In addition to addressing the equivalence of scaling the evidence and the bound in the Introduction, we have added the following section to Results (Results, p.18):

“Note that scaling the bound in these formulations follows conventions of the DDM, as detailed above, to facilitate interpretation of the parameters. These formulations also raise an apparent contradiction: the “predefined” bound is scaled by subjective estimates of the correlation, but the correlation was randomized from trial to trial and thus could not be known in advance. However, scaling the bound in these ways is mathematically equivalent to using a fixed bound on each trial and scaling the observations to approximate logLR (see Methods). This equivalence implies that in the brain, effectively scaling a “predefined” bound could occur when assigning a weight of evidence to the observations as they are presented.”

We also note in Methods (pp. 40–41):

“In the DDM, this scaling of the evidence is equivalent to assuming that the decision variable accumulates momentary evidence of the form (x1 + x2) and then dividing the bound height by the appropriate scale factor. An alternative approach would be to scale both the signal and noise components of the DDM by the scale factor. However, scaling the bound is both simpler and maintains the conventional interpretation of the DDM parameters in which the bound reflects the decision-related components of the evidence accumulation process, and the drift rate represents sensory-related components.”

We believe we provide strong evidence that participants adjust their evidence weighing to account for the correlations (see response below), but we remain agnostic as to how exactly this weighing is implemented in the brain.

Modelling focus: Related to the previous point, it is stated that participants' choice and RT patterns across correlation conditions were qualitatively consistent with bound adjustments (p.20), but evidence for this claim is limited. Bound adjustments imply effects on both accuracy and RTs, but the data here show either only effects on RTs, or RT effects mixed with accuracy trends that are in the opposite direction to what would be expected from bound adjustment (i.e. slower RT with a trend toward diminished accuracy in the strong negative correlation condition; Figure 3b). Allowing both drift rate and bound to vary with correlation conditions allowed the model to provide a better account of the data in the strong correlation conditions - but from what I can tell this is not consistent with the authors' preregistered hypotheses, and they rely on a posthoc explanation that is necessarily speculative and cannot presently be tested (that the diminished drift rates for higher negative correlations are due to imperfect mapping between subjective evidence strength and the experimenter-controlled adjustment to objective evidence strengths to account for effects of correlations). In my opinion, there are other candidate explanations for the observed effects that could be tested but lie outside of the relatively narrow focus of the current modelling efforts. Both explanations arise from aspects of the task, which are not mutually exclusive. The first is that an interesting aspect of this task, which contrasts with most common 'univariate' perceptual decision-making tasks, is that participants need to integrate two pieces of information at a time, which may or may not require an additional computational step (e.g. averaging of two spatial locations before adding a single quantum of evidence to the building decision variable). There is abundant evidence that such intermediate computations on the evidence can give rise to certain forms of bias in the way that evidence is accumulated (e.g. 'selective integration' as outlined in Usher et al., 2019, Current Directions in Psychological Science; Luyckx et al., 2020, Cerebral Cortex) which may affect RTs and/or accuracy on the current task. The second candidate explanation is that participants in the current study were only given 200 ms to process and accumulate each pair of evidence samples, which may create a processing bottleneck causing certain pairs or individual samples to be missed (and which, assuming fixed decision bounds, would presumably selectively affect RT and not accuracy). If I were to speculate, I would say that both factors could be exacerbated in the negative correlation conditions, where pairs of samples will on average be more 'conflicting' (i.e. further apart) and, speculatively, more challenging to process in the limited time available here to participants. Such possibilities could be tested through, for example, an interrogation paradigm version of the current task which would allow the impact of individual pairs of evidence samples to be more straightforwardly assessed; and by assessing the impact of varying inter-sample intervals on the behavioural effects reported presently.

We thank the reviewer for this thoughtful and valuable feedback. We have thoroughly updated the modeling section to include new analysis and clearer descriptions and interpretations of our findings (including Figs. 5–7 and additional references to the Usher, Luyckx, and other studies that identified decision suboptimalities). The comment about “an additional computational step” in converting the observations to evidence was particularly useful, in that it made us realize that we were making what we now consider to be a faulty assumption in our version of the DDM. Specifically, we assumed that subjective misestimates of the correlation affected how observations were converted to evidence (logLR) to form the decision (implemented as a scaling of the bound height), but we neglected to consider how suboptimalities in encoding the observations could also lead to misestimates of the correlation. We have retained the previous best-fitting models in the text, for comparison (the “bound-rho-hat” and “bound-rho-hat + drift” models). In addition, we now include a “full-rho-hat” model that assumes that misestimates of rho affect both the encoding of the observations, which affects the drift rate and bound height, and the weighing of the evidence, which affects only the bound height. This was the best-fitting model for most participants (after accounting for different numbers of parameters associated with the different models we tested). Note that the full-rho-hat model predicts the lack of correlation-dependent choice effects and the substantial correlation-dependent RT effects that we observed, without requiring any additional adjustments to the drift rate (as we resorted to previously).

In summary, we believe that we now have a much more parsimonious account of our data, in terms of a model in which subjective estimates of the correlation are alone able to account for our patterns of choice and RT data. We fully agree that more work is needed to better understand the source of these misestimates but also think those questions are outside the scope of the present study.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

A few minor comments:

(1) Evidence can be correlated in multiple ways. It could be correlated within individual pieces of evidence in a sequence, or across elements in that sequence (e.g., across time). This distinction is important, as it determines how evidence ought to be accumulated across time. In particular, if evidence is correlated across time, simply summing it up might be the wrong thing to do. Thus, it would be beneficial to make this distinction in the Introduction, and to mention that this paper is only concerned with the first type of correlation.

We now clarify this point in the Introduction (p. 5–6).

(2) It is unclear without reading the Methods how the blue dashed line in Figure 4c is generated. To my understanding, it is a prediction of the naive DDM model. Is this correct?

We now specify the models used to make the predictions shown in Fig. 4c (which now includes an additional model that uses unscaled observations as evidence).

(3) In Methods, given the importance of the distribution of x1 + x2, it would be useful to write it out explicitly, e.g., x1 + x2 ~ N(2 mu_g, ..), specifying its mean and its variance.

Excellent suggestion, added to p. 38.

(4) From Methods and the caption of Figure 6 - Supplement 1 it becomes clear that the fitted DDM features a bound that collapses over time. I think that this should also be mentioned in the main text, as it is a not-too-unimportant feature of the model.

Excellent suggestion, added to p. 15, with reference to Fig. 6-supplement 1 on p. 20.

(5) The functional form of the bound is 2 (B - tb t). To my understanding, the effective B changes as a function of the correlation magnitude. Does tb as well? If not, wouldn't it be better if it does, to ensure that 2 (B - tb t) = 0 independent of the correlation magnitude?

In our initial modeling, we also considered whether the correlation-dependent adjustment, which is a function of both correlation sign and magnitude, should be applied to the initial bound or to the instantaneous bound (i.e., after collapse, affecting tb as well). In a pilot analysis of data from 22 participants in the 0.6 correlation-magnitude group, we found that this choice had a negligible effect on the goodness-of-fit (deltaAIC = -0.9, protected exceedance probability = 0.63, in favor of the instantaneous bound scaling). We therefore used the instantaneous bound version in the analyses reported in the manuscript but doubt this choice was critical based on these results. We have clarified our implementation of the bound in Methods (p. 43–44).

Reviewer #2 (Recommendations for the authors):

In addition to the points raised above, I have some minor suggestions/open questions that arose from my reading of the manuscript:

(1) Are the predictions outlined in the paper specific to cases where the two sources are symmetric around zero? If distributions are allowed to be asymmetric then one can imagine cases (i.e. when distribution means are sufficiently offset from one another) where positive correlations can increase evidence strength and negative correlations decrease evidence strength. There's absolutely still value and much elegance in what the authors are showing with this work, but if my intuition is correct, it should ideally be acknowledged that the predictions are restricted to a specific set of generative circumstances.

We agree that there are a lot of ways to manipulate correlations and their effect on the weight of evidence. At the end of the Discussion, we emphasize that our results apply to this particular form of correlation (p. 32).

(2) Isn't Figure 4C misleading in the sense that it collapses across the asymmetry in the effect of negative vs positive correlations on RT, which is clearly there in the data and which simply adjusting the correlation-dependent scale factor will not reproduce?

We agree that this analysis does not address any asymmetries in suboptimal estimates of positive versus negative correlations. We believe that those effects are much better addressed using the model fitting, which we present later in the Results section. We have now simplified the analyses in Fig. 4c, reporting the difference in RT between positive and negative correlation conditions instead of a linear regression.

(3) I found the transition on p.17 of the Results section from the scaling of drift rate by correlation to scaling of bound height to be quite abrupt and unclear. I suspect that many readers coming from a typical DDM modelling background will be operating under the assumption that drift rate and bound height are independent, and I think more could be done here to explain why scaling one parameter by correlation in the present case is in fact directly equivalent to scaling the other.

Thank you for the very useful feedback, we have substantially revised this text to make these points more clearly.

(4) P.3, typo: Alan *Turing*

That’s embarrassing. Fixed.

(5) P.27, typo: "participants adopt a *fixed* bound"

Fixed.

Author response:

The following is the authors’ response to the original reviews

eLife Assessment

This study presents valuable findings related to seasonal brain size plasticity in the Eurasian common shrew (Sorex araneus), which is an excellent model system for these studies. The evidence supporting the authors' claims is convincing. However, the authors should be careful when applying the term adaptive to the gene expression changes they observe; it would be challenging to demonstrate the differential fitness effects of these gene expression changes. The work will be of interest to biologists working on neuroscience, plasticity, and evolution.

We appreciate the reviewers’ suggestions and comments. For the phylogenetic ANOVA we used (EVE), which tests for a separate RNA expression optimum specific to the shrew lineage consistent with expectations for adaptive evolution of gene expression. But, as you noted, while this analysis highlights many candidate genes evolving in a manner consistent with positive selection, further functional validation is required to confirm if and how these genes contribute to Dehnel’s phenomenon. In the discussion, we now emphasize that inferred adaptive expression of these genes is putative and outline that future studies are needed to test the function of proposed adaptations. For example, cell line validations of BCL2L1 on apoptosis is a case study that tests the function of a putatively adaptive change in gene expression, and it illuminates this limitation. We also have refined our discussion to focus more on pathway-level analyses rather than on individual genes, and have addressed other issues presented, including clarity of methods and using sex as a covariate in our analyses.

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this paper, Thomas et al. set out to study seasonal brain gene expression changes in the Eurasian common shrew. This mammalian species is unusual in that it does not hibernate or migrate but instead stays active all winter while shrinking and then regrowing its brain and other organs. The authors previously examined gene expression changes in two brain regions and the liver. Here, they added data from the hypothalamus, a brain region involved in the regulation of metabolism and homeostasis. The specific goals were to identify genes and gene groups that change expression with the seasons and to identify genes with unusual expression compared to other mammalian species. The reason for this second goal is that genes that change with the season could be due to plastic gene regulation, where the organism simply reacts to environmental change using processes available to all mammals. Such changes are not necessarily indicative of adaptation in the shrew. However, if the same genes are also expression outliers compared to other species that do not show this overwintering strategy, it is more likely that they reflect adaptive changes that contribute to the shrew's unique traits.

The authors succeeded in implementing their experimental design and identified significant genes in each of their specific goals. There was an overlap between these gene lists. The authors provide extensive discussion of the genes they found.

The scope of this paper is quite narrow, as it adds gene expression data for only one additional tissue compared to the authors' previous work in a 2023 preprint. The two papers even use the same animals, which had been collected for that earlier work. As a consequence, the current paper is limited in the results it can present. This is somewhat compensated by an expansive interpretation of the results in the discussion section, but I felt that much of this was too speculative. More importantly, there are several limitations to the design, making it hard to draw stronger conclusions from the data. The main contribution of this work lies in the generated data and the formulation of hypotheses to be tested by future work.

Thank you for your interest in our manuscript and for your insights. We addressed your comments below: we now highlight the limitations of our study design in the discussion and emphasize that, while a second optimum of gene expression in shrews is consistent with adaptive evolution, we recognize that not all sources of variation in gene expression can be fully accounted for. We highlight the putative nature of these results in our revisions, especially in our new limitations section (lines 541-555).

Strengths:

The unique biological model system under study is fascinating. The data were collected in a technically sound manner, and the analyses were done well. The paper is overall very clear, well-written, and easy to follow. It does a thorough job of exploring patterns and enrichments in the various gene sets that are identified.

I specifically applaud the authors for doing a functional follow-up experiment on one of the differentially expressed genes (BCL2L1), even if the results did not support the hypothesis. It is important to report experiments like this and it is terrific to see it done here.

We are glad to hear that you found our manuscript fascinating and clearly written. While we hoped to see an effect of BCL2L1 on apoptosis as proposed, we agree that reporting null results is valuable when validating evolutionary inferences.

Weaknesses:

While the paper successfully identifies differentially expressed seasonal genes, the real question is (as explained by the authors) whether these are evolved adaptations in the shrews or whether they reflect plastic changes that also exist in other species. This question was the motivation for the inter-species analyses in the paper, but in my view, these cannot rigorously address this question. Presumably, the data from the other species were not collected in comparable environments as those experienced by the shrews studied here. Instead, they likely (it is not specified, and might not be knowable for the public data) reflect baseline gene expression. To see why this is problematic, consider this analogy: if we were to compare gene expression in the immune system of an individual undergoing an acute infection to other, uninfected individuals, we would see many, strong expression differences. However, it would not be appropriate to claim that the infected individual has unique features - the relevant physiological changes are simply not triggered in the other individuals. The same applies here: it is hard to draw conclusions from seasonal expression data in the shrews to non-seasonal data in the other species, as shrew outlier genes might still reflect physiological changes that weren't active in the other species.

There is no solution for this design flaw given the public data available to the authors except for creating matched data in the other species, which is of course not feasible. The authors should acknowledge and discuss this shortcoming in the paper.

Thank you for taking the time to provide such insightful feedback. As you noted, whiles shrews experience seasonal size changes, their environments may differ from the other species used in this experiment, leading to increased or decreased expression of certain genes and reducing our ability accurately detect selection across the phylogeny. Although we sought to control for as many sources of variation as possible, such as using only post-pubescent, wild, or non-domesticated individuals when feasible, we recognize that not all sources of variation can be fully accounted for within a practical experiment. We agree that these sources of variation can introduce both false positives and negatives into our results, and we have now highlighted this limitation within our discussion (lines 538-552).

Related to the point above: in the section "Evolutionary Divergence in Expression" it is not clear which of the shrew samples were used. Was it all of them, or only those from winter, fall, etc? One might expect different results depending on this. E.g., there could be fewer genes with inferred adaptive change when using only summer samples. The authors should specify which samples were included in these analyses, and, if all samples were used, conduct a robustness analysis to see which of their detected genes survive the exclusion of certain time points.

Thank you for this attention to detail. We used spring adults for this analysis. This decision was made as only used post pubescent individuals for all species in the analysis, and this was the only season where adult shrews were going through Dehnel’s phenomenon. We have now clarified this in both the methods and results (line 247 and line 667)

In the same section, were there also genes with lower shrew expression? None are mentioned in the text, so did the authors not test for this direction, or did they test and there were no significant hits?

We did test for decreased shrew expression compared to the rest of the species, but there were no significant genes with significant decreases. We hypothesize that there are two potential reasons for this results; 1) If a gene were to be selected for decreased expression, selection for constitutive expression of the gene across all species may be weak, and thus found in other lineages as well, or 2) decreased or no expression may relax selection on the coding regions, and thus these genes are not pulled out as we identify 1:1 orthologs. This is consistent with results provided from the original methods manuscript. Thank you for pointing out that we did not discuss this information in the text, and we now include it in our results (lines 250-251).

The Discussion is too long and detailed, given that it can ultimately only speculate about what the various expression changes might mean. Many of the specific points made (e.g. about the blood-brain-barrier being more permissive to sensing metabolic state, about cross-organ communication, the paragraphs on single, specific genes) are a stretch based on the available data. Illustrating this point, the one follow-up experiment the authors did (on BCL2L1) did not give the expected result. I really applaud the authors for having done this experiment, which goes beyond typical studies in this space. At the same time, its result highlights the dangers of reading too much into differential expression analyses.

We agree with your point, while our extensive discussion is useful for testing future hypotheses, ultimately some of the discussion may be too speculative for our readers. To amend this, we have reduced some portions of our discussion and focused more on pathways than individual genes, including removing mechanisms related to HRH2, FAM57B, GPR3, and GABAergic neurons. We hope that this highlights to the reader the speculative nature of many of our results.

There is no test of whether the five genes observed in both analyses (seasonal change and inter-species) exceed the number expected by chance. When two gene sets are drawn at random, some overlap is expected randomly. The expected overlap can be computed by repeated draws of pairs of random sets of the same size as seen in real data and by noting the overlap between the random pairs. If this random distribution often includes sets of five genes, this weakens the conclusions that can be drawn from the genes observed in the real data.

Thank you for highlighting this approach, it is greatly needed. After running this test, we found that observed overlapping genes were more than the expected overlap, yet not significant. We now show this in our methods (lines 277-278) and results (lines 719-720).

Reviewer #2 (Public review):

Summary:

Shrews go through winter by shrinking their brain and most organs, then regrow them in the spring. The gene expression changes underlying this unusual brain size plasticity were unknown. Here, the authors looked for potential adaptations underlying this trait by looking at differential expression in the hypothalamus. They found enrichments for DE in genes related to the blood-brain barrier and calcium signaling, as well as used comparative data to look at gene expression differences that are unique in shrews. This study leverages a fascinating organismal trait to understand plasticity and what might be driving it at the level of gene expression. This manuscript also lays the groundwork for further developing this interesting system.

We are glad you found our manuscript interesting and thank and thank you for your feedback. We hope that we have addressed all of your concerns as described below.

Strengths:

One strength is that the authors used OU models to look for adaptation in gene expression. The authors also added cell culture work to bolster their findings.

Weaknesses:

I think that there should be a bit more of an introduction to Dehnel's phenomenon, given how much it is used throughout.

Thank you for this insight. With a lengthy introduction and discussion, we agree that the importance of Dehnel’s phenomenon may have been overshadowed. We have shortened both sections and emphasized the background on Dehnel’s phenomenon in the first two paragraphs of the introduction, allowing this extraordinary seasonal size plasticity to stand out.

Reviewer #3 (Public review):

Summary:

In their study, the authors combine developmental and comparative transcriptomics to identify candidate genes with plastic, canalized, or lineage-specific (i.e., divergent) expression patterns associated with an unusual overwintering phenomenon (Dehnel's phenomenon - seasonal size plasticity) in the Eurasian shrew. Their focus is on the shrinkage and regrowth of the hypothalamus, a brain region that undergoes significant seasonal size changes in shrews and plays a key role in regulating metabolic homeostasis. Through combined transcriptomic analysis, they identify genes showing derived (lineage-specific), plastic (seasonally regulated), and canalized (both lineage-specific and plastic) expression patterns. The authors hypothesize that genes involved in pathways such as the blood-brain barrier, metabolic state sensing, and ion-dependent signaling will be enriched among those with notable transcriptomic patterns. They complement their transcriptomic findings with a cell culture-based functional assessment of a candidate gene believed to reduce apoptosis.

Strengths:

The study's rationale and its integration of developmental and comparative transcriptomics are well-articulated and represent an advancement in the field. The transcriptome, known for its dynamic and plastic nature, is also influenced by evolutionary history. The authors effectively demonstrate how multiple signals-evolutionary, constitutive, and plastic-can be extracted, quantified, and interpreted. The chosen phenotype and study system are particularly compelling, as it not only exemplifies an extreme case of Dehnel's phenotype, but the metabolic requirements of the shrew suggest that genes regulating metabolic homeostasis are under strong selection.

Weaknesses:

(1) In a number of places (described in detail below), the motivation for the experimental, analytical, or visualization approach is unclear and may obscure or prevent discoveries.

Thank you for finding our research and manuscript compelling, as well as the valuable feedback that will drastically improve our manuscript. We hope that we have alleviated your concerns below by following your instructions below.

(2) Temporal Expression - Figure 1 and Supplemental Figure 2 and associated text:

- It is unclear whether quantitative criteria were used to distinguish "developmental shift" clusters from "season shift" clusters. A visual inspection of Supplemental Figure 2 suggests that some clusters (e.g., clusters 2, 8, and to a lesser extent 12) show seasonal variation, not just developmental differences between stages 1 and 2. While clustering helps to visualize expression patterns, it may not be the most appropriate filter in this case, particularly since all "season shift" clusters are later combined in KEGG pathway and GO analyses (Figure 1B).

- The authors do not indicate whether they perform cluster-specific GO or KEGG pathway enrichment analyses. The current analysis picks up relevant pathways for hypothalamic control of homeostasis, which is a useful validation, but this approach might not fully address the study's key hypotheses.

Thank you for this valuable feedback. We did not want to include clusters we deemed to be related to development, as this should not be attributed to changes associated with Dehnel’s phenomenon. We did this through qualitative, visual inspection, which we realize can differ between parties (i.e., clusters 2, 8, and 12 appeared to be seasonal). Qualitatively, we were looking for extreme divergence between Stage 1 and Stage 5 individuals, as expression was related to season and not development, then the average of these stages within cluster should be relatively similar. We have now quantified this as large differences in z-score (abs(summer juvenile-summer adult)>1.25) without meaningful interseason variations determined by a second local maximum (abs(autumn-winter)<0.5 and abs(winter-summer)<0.5)), and added it both our methods (lines 699-702) and results (line 192).

Regarding the combination of clusters for pathway enrichment compared to individual pathways, we agree that combining clusters may be more informative for overall homeostasis, compared to individual clusters which may inform us on processes directly related to Dehnel’s phenomenon. Initially, we were tentative to conduct this analysis, as clusters contain small gene sets, reducing the ability to detect pathway enrichments. We have now included this analysis, which is reported in our methods (lines 703-704), results (lines 203-204)., and new supplemental table.

(3) Differential expression between shrinkage (stage 2) and regrowth (stage 4) and cell culture targets

- The rationale for selecting BCL2L1 for cell culture experiments should be clarified. While it is part of the apoptosis pathway, several other apoptosis-related genes were identified in the differential gene expression (DGE) analysis, some showing stronger differential expression or shrew-specific branch shifts. Why was BCL2L1 prioritized over these other candidates?

We agree that our rationale for validating BCL2L1 function in neural cell lines was not clearly explained in the manuscript. We selected BCL2L1 because it is the furthest downstream gene in the apoptotic pathway, thus making it the most directly involved gene in programmed cell death, whereas upstream genes could influence additional genes or alternative processes. We have clarified this choice in the revised methods section (lines 748-750).

- The authors mention maintaining (or at least attempting to maintain) a 1:1 sex ratio for the comparative analysis, but it is unclear if this was also done for the S. araneus analysis. If not, why? If so, was sex included as a covariate (e.g., a random effect) in the differential expression analysis? Sex-specific expression elevates with group variation and could impact the discovery of differentially expressed genes.

Regarding the use of sex as a covariate, we acknowledge the concerns raised. In our evolutionary analyses, we maintained a balanced sex ratio within species when possible. EVE models handle the effect of sex on gene expression as intraspecific variation. In shrews, however, we used males exclusively, as females were only found among juvenile individuals. Including those juvenile females would have introduced age effects, with perhaps a larger effect on our results. For the seasonal data, we have now included sex as a covariate in differential expression analyses. However, our design is imbalanced in relation to sex, which we have now discussed in our methods (lines 713-714) and discussion limitations (lines 544-548).

(4) Discussion: The term "adaptive" is used frequently and liberally throughout the discussion. The interpretation of seasonal changes in gene expression as indicators of adaptive evolution should be done cautiously as such changes do not necessarily imply causal or adaptive associations.

Thank you for this insight. We have reviewed our discussion and clarified that adaptations are putative (i.e. lines 146, 285, and 332), and highlighted this in our limitations section.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) I would recommend always spelling out "Dehnel's phenomenon" or even replacing this term (after crediting the DP term) with the more informative "seasonal size plasticity". Every time I saw "DP", I had to remind myself what this referred to. If the authors choose not to do so, please use the acronym consistently (e.g. line 186 has it spelled out).

We have replaced the acronym DP with either the full term or the more informative “seasonal size plasticity” throughout the text.

(2) Line 202: "DEG" has not been defined. Simply add to the line before.

Thank you for this attention to detail. We have added this to the line above (210).

(3) Please add a reference for the "AnAge" tool that was used to determine if samples were pubescent.

Thank you for identifying this oversight. We have now cited the proper paper in line 634.

(4) In the BCL2L1 section in the results, add a callout to Figure 2D.

We have now added a callout to Figure 2D within the results (line 234).

Reviewer #2 (Recommendations for the authors):

(1) Line 122: is associated? These adaptations?

Thank you for identifying that we were missing the words “associated with” here. We have fixed this in the revision.

(2) The first paragraph of the Results should be moved to the methods, except maybe the number of orthologs.

Thank you for this insight. We have removed this portion from the results section.

(3) Why a Bonferroni correction on line 188? That seems too strict.

We agree the Bonferroni correction is strict. Results when using other less strict methods for controlling false discovery rate are also not significant after correction. These corrections can be found within the data, however, we only report on the Bonferroni correction.

(4) Line 427: "is a novel candidate gene for several neurological disorders" needs some references. I see them a couple of sentences later, but that's quite a sentence with no references at the end.

We have added the proper citations for this sentence (line 524).

Reviewer #3 (Recommendations for the authors):

(1) Temporal Expression - Figure 1 and Supplemental Figure 2 and associated text Line176-193:

- The authors report the total number of genes meeting inclusion criteria (>0.5-fold change between any two stages and 2 samples >10 normalized reads), but it would be more informative to also provide the number of genes within each temporal cluster. This would offer a clearer understanding of how gene expression patterns are distributed over time.

Unfortunately, this information is difficult to depict on our figure and would use too much space in the text. We have thus added a description of the range of genes in a new supplemental table depicting this information.

- It is unclear whether quantitative criteria were used to distinguish "developmental shift" clusters from "season shift" clusters. A visual inspection of Supplemental Figure 2 suggests that some clusters (e.g., clusters 2, 8, and to a lesser extent 12) show seasonal variation, not just developmental differences between stages 1 and 2. While clustering helps to visualize expression patterns, it may not be the most appropriate filter in this case, particularly since all "season shift" clusters are later combined in KEGG pathway and GO analyses (Fig. 1B). Using a differential gene expression criterion might be more suitable. For example, do excluded genes show significant log-fold differences between late-stage comparisons?

As previously mentioned, we have now quantified seasonal shifts as large differences in z-score (abs(summer juveniles-summer adults)>1.25) without meaningful interseason variations determined by a second local maximum (abs(autumn-winter)<0.5 and abs(winter-summer)<0.5)), and added it to our methods (lines 699-702).  We then follow this up with differential expression analyses as described in Figure 2.

- Did the authors perform cluster-specific GO or KEGG pathway enrichment analyses instead of focusing on the combined set of genes across the season shift clusters? While I understand that the small number of genes in each cluster may be limiting, if pathways emerge from cluster-specific analysis, they could provide more detailed insights into the functional significance of these temporal expression patterns. The current analysis picks up relevant pathways for hypothalamic control of homeostasis, which is a useful validation, but this approach might not fully address the study's key hypotheses. Additionally, no corrections for multiple hypothesis testing were applied, as noted in the results. A more refined gene set (e.g., using differential expression criteria, described above) could be more appropriate for these analyses.

We have now included cluster-specific KEGG enrichments as previously described.

(2) Differential expression between shrinkage (stage 2) and regrowth (stage 4) and cell culture targets - Figure 2 and lines195-227:

- The rationale for selecting BCL2L1 for cell culture experiments should be clarified. While it is part of the apoptosis pathway, several other apoptosis-related genes were identified in the differential gene expression (DGE) analysis, some showing stronger differential expression or shrew-specific branch shifts. Why was BCL2L1 prioritized over these other candidates?

We have now included the reasoning for further validation of BCL2L1 as described above.

- The relevance of the "higher degree" differentially expressed genes needs more explanation. Although this group of genes is highlighted in the results, they are not featured in any subsequent analyses, leaving their importance unclear.

Thank you for this insight. We have removed this from the methods as it is not relevant to subsequent analyses or conclusions.

- The authors mention maintaining (or at least attempting to maintain) a 1:1 sex ratio for the comparative analysis (Line 525), but it is unclear if this was also done for the S. araneus analysis. If so, was sex included as a covariate (e.g., a random effect) in the differential expression analysis?

We have now incorporated information on sex as described above.

(3) Discussion:

The term "adaptive" is used frequently and liberally throughout the discussion, but the authors should be cautious in interpreting seasonal changes in gene expression as indicators of adaptive evolution. Such changes do not necessarily imply causal or adaptive associations, and this distinction should be clearly stated when discussing the results.

Thank you for this feedback and we agree with your conclusion, while a second expression optimum in the shrew lineage is indicative of adaptive expression, we cannot fully determine whether these are caused by genetic or environmental factors, despite careful attention to experimental design. We have highlighted this as a limitation in the discussion.

(4) Minor Editorial Comment:

Line 105: "... maintenance of an energy budgets..." delete "an"

We have removed this grammatical error.

Author response:

(This author response relates to the first round of peer review by Biophysics Colab. Reviews and responses to both rounds of review are available here: https://sciety.org/articles/activity/10.1101/2023.10.23.563601.)

General Assessment:

Pannexin (Panx) hemichannels are a family of heptameric membrane proteins that form pores in the plasma membrane through which ions and relatively large organic molecules can permeate. ATP release through Panx channels during the process of apoptosis is one established biological role of these proteins in the immune system, but they are widely expressed in many cells throughout the body, including the nervous system, and likely play many interesting and important roles that are yet to be defined. Although several structures have now been solved of different Panx subtypes from different species, their biophysical mechanisms remain poorly understood, including what physiological signals control their activation. Electrophysiological measurements of ionic currents flowing in response to Panx channel activation have shown that some subtypes can be activated by strong membrane depolarization or caspase cleavage of the C-terminus. Here, Henze and colleagues set out to identify endogenous activators of Panx channels, focusing on the Panx1 and Panx2 subtypes, by fractionating mouse liver extracts and screening for activation of Panx channels expressed in mammalian cells using whole-cell patch clamp recordings. The authors present a comprehensive examination with robust methodologies and supporting data that demonstrate that lysophospholipids (LPCs) directly Panx-1 and 2 channels. These methodologies include channel mutagenesis, electrophysiology, ATP release and fluorescence assays, molecular modelling, and cryogenic electron microscopy (cryo-EM). Mouse liver extracts were initially used to identify LPC activators, but the authors go on to individually evaluate many different types of LPCs to determine those that are more specific for Panx channel activation. Importantly, the enzymes that endogenously regulate the production of these LPCs were also assessed along with other by-products that were shown not to promote pannexin channel activation. In addition, the authors used synovial fluid from canine patients, which is enriched in LPCs, to highlight the importance of the findings in pathology. Overall, we think this is likely to be a landmark study because it provides strong evidence that LPCs can function as activators of Panx1 and Panx2 channels, linking two established mediators of inflammatory responses and opening an entirely new area for exploring the biological roles of Panx channels. Although the mechanism of LPC activation of Panx channels remains unresolved, this study provides an excellent foundation for future studies and importantly provides clinical relevance.

We thank the reviewers for their time and effort in reviewing our manuscript. Based on their valuable comments and suggestions, we have made substantial revisions. The updated manuscript now includes two new experiments supporting that lysophospholipid-triggered channel activation promotes the release of signaling molecules critical for immune response and demonstrates that this novel class of agonist activates the inflammasome in human macrophages through endogenously expressed Panx1. To better highlight the significance of our findings, we have excluded the cryo-EM panel from this manuscript. We believe these changes address the main concerns raised by the reviewers and enhance the overall clarity and impact of our findings. Below, we provide a point-by-point response to each of the reviewers’ comments.

Recommendations:

(1) The authors present a tremendous amount of data using different approaches, cells and assays along with a written presentation that is quite abbreviated, which may make comprehension challenging for some readers. We would encourage the authors to expand the written presentation to more fully describe the experiments that were done and how the data were analysed so that the 2 key conclusions can be more fully appreciated by readers. A lot of data is also presented in supplemental figures that could be brought into the main figures and more thoroughly presented and discussed.

We appreciate and agree with the reviewers’ observation. Our initial manuscript may have been challenging to follow due to our use of both wild-type and GS-tagged versions of Panx1 from human and frog origins, combined with different fluorescence techniques across cell types. In this revision, we used only human wild-type Panx1 expressed in HEK293S GnTI- cells, except for activity-guided fractionation experiments, where we used GS-tagged Panx1 expressed in HEK293 cells (Fig. 1). For functional reconstitution studies, we employed YO-PRO-1 uptake assays, as optimizing the Venus-based assay was challenging. We have clarified these exceptions in the main text. We think these adjustments simplify the narrative and ensure an appropriate balance between main and supplemental figures.

(2) It would also be useful to present data on the ion selectivity of Panx channels activated by LPC. How does this compare to data obtained when the channel is activated by depolarization? If the two stimuli activate related open states then the ion selectivity may be quite similar, but perhaps not if the two stimuli activate different open states. The authors earlier work in eLife shows interesting shifts in reversal potentials (Vrev) when substituting external chloride with gluconate but not when substituting external sodium with N-methyl-D-glucamine, and these changed with mutations within the external pore of Panx channels. Related measurements comparing channels activated by LPC with membrane depolarization would be valuable for assessing whether similar or distinct open states are activated by LPC and voltage. It would be ideal to make Vrev measurements using a fixed step depolarization to open the channel and then various steps to more negative voltages to measure tail currents in pinpointing Vrev (a so called instantaneous IV).

We fully agree with the reviewer on the importance of ion selectivity experiments. However, comparing the properties of LPC-activated channels with those activated by membrane depolarization presented technical challenges, as LPC appears to stimulate Panx1 in synergy with voltage. Prolonged LPC exposure destabilizes patches, complicating G-V curve acquisition and kinetic analyses. While such experiments could provide mechanistic insights, we think they are beyond the scope of current study.

(3) Data is presented for expression of Panx channels in different cell types (HEK vs HEKS GnTI-) and different constructs (Panx1 vs Panx1-GS vs other engineered constructs). The authors have tried to be clear about what was done in each experiment, but it can be challenging for the reader to keep everything straight. The labelling in Fig 1E helps a lot, and we encourage the authors to use that approach systematically throughout. It would also help to clearly identify the cell type and channel construct whenever showing traces, like those in Fig 1D. Doing this systematically throughout all the figures would also make it clear where a control is missing. For example, if labelling for the type of cell was included in Fig 1D it would be immediately clear that a GnTI- vector alone control for WT Panx1 is missing as the vector control shown is for HEK cells and formally that is only a control for Panx2 and 3. Can the authors explain why PLC activates Panx1 overexpressed in HEK293 GnTl- cells but not in HEK293 cells? Is this purely a function of expression levels? If so, it would be good to provide that supporting information.

As mentioned above, we believe our revised version is more straightforward to digest. We have improved labeling and provided explanations where necessary to clarify the manuscript. While Panx1 expression levels are indeed higher in GnTI- than in HEK293 cells, we are uncertain whether the absence of detectable currents in HEK293 cells is solely due to expression levels. Some post-translational modifications that inhibit Panx1, such as lysine acetylation, may also impact activity. Future studies are needed to explore these mechanisms further.

(4) The mVenus quenching experiments are somewhat confusing in the way data are presented. In Fig 2B the y axis is labelled fluorescence (%) but when the channel is closed at time = 0 the value of fluorescence is 0 rather than 100 %, and as the channel opens when LPC is added the values grow towards 100 instead of towards 0 as iodide permeates and quenches. It would be helpful if these types of data could be presented more intuitively. Also, how was the initial rate calculated that is plotted in Fig 2C? It would be helpful to show how this is done in a figure panel somewhere. Why was the initial rate expressed as a percent maximum, what is the maximum and why are the values so low? Why is the effect of CBX so weak in these quenching experiments with Panx1 compared to other assays? This assay is used in a lot of experiments so anything that could be done to bolster confidence is what it reports on would be valuable to readers. Bringing in as many control experiments that have been done, including any that are already published, would be helpful.

We modified the Y-axis in Figure 2 to “Quench (%)” for clarity. The data reflects fluorescence reduction over time, starting from LPC addition, normalized to the maximal decrease observed after Triton-X100 addition (3 minutes), enabling consistent quenching value comparisons. Although the quenching value appears small, normalization against complete cell solubilization provides reproducible comparisons. We do not fully understand why CBX effects vary in Venus quenching experiments, but we speculate that its steroid-like pentacyclic structure may influence the lysophospholipid agonistic effects. As noted in prior studies (DOI: 10.1085/jgp.201511505; DOI: 10.7554/eLife.54670), CBX likely acts as an allosteric modulator rather than a simple pore blocker, potentially contributing to these variations.

(5) Could provide more information to help rationalize how Yo-Pro-1, which has a charge of +2, can permeate what are thought to be anion favouring Panx channels? We appreciate that the biophysical properties of Panx channel remain mysterious, but it would help to hear how a bit more about the authors thinking. It might also help to cite other papers that have measured Yo-Pro-1 uptake through Panx channels. Was the Strep-tagged construct of Panx1 expressed in GnTI- cells and shown to be functional using electrophysiology?

Our recent study suggest that the electrostatic landscape along the permeation pathway may influence its ion selectivity (DOI: 10.1101/2024.06.13.598903). However, we have not yet fully elucidated how Panx1 permeates both anions and cations. Based on our findings, ion selectivity may vary with activation stimulus intensity and duration. Cation permeation through Panx1 is often demonstrated with YO-PRO-1, which measures uptake over minutes, unlike electrophysiological measurements conducted over milliseconds to seconds. We referenced two representative studies employing YO-PRO-1 to assess Panx1 activity. Whole-cell current measurements from a similar construct with an intracellular loop insertion indicate that our STREP-tagged construct likely retains functional capacity.

(6) In Fig 5 panel C, data is presented as the ratio of LPC induced current at -60 mV to that measured at +110 mV in the absence of LPC. What is the rationale for analysing the data this way? It would be helpful to also plot the two values separately for all of the constructs presented so the reader can see whether any of the mutants disproportionately alter LPC induced current relative to depolarization activated current. Also, for all currents shown in the figures, the authors should include a dashed coloured line at zero current, both for the LPC activated currents and the voltage steps.

We used the ratio of LPC-induced current to the current measured at +110 mV to determine whether any of the mutants disproportionately affect LPC-induced current relative to depolarization-activated current. Since the mutants that did not respond to LPC also exhibited smaller voltage-stimulated currents than those that did respond, we reasoned that using this ratio would better capture the information the reviewer is suggesting to gauge. Showing the zero current level may be helpful if the goal was to compare basal currents, which in our experience vary significantly from patch to patch. However, since we are comparing LPC- and voltage-induced currents within the same patch, we believe that including basal current measurements would not add useful information to our study.

Given that new experiments included to further highlight the significance of the discovery of Panx1 agonists, we opted to separate structure-based mechanistic studies from this manuscript and removed this experiment along with the docking and cryo-EM studies.

(7) The fragmented NTD density shown in Fig S8 panel A may resemble either lipid density or the average density of both NTD and lipid. For example, Class7 and Class8 in Fig.S8 panel D displayed split densities, which may resemble a phosphate head group and two tails of lipid. A protomer mask may not be the ideal approach to separate different classes of NTD because as shown in Fig S8 panel D, most high-resolution features are located on TM1-4, suggesting that the classification was focused on TM1-4. A more suitable approach would involve using a smaller mask including NTD, TM1, and the neighbouring TM2 region to separate different NTD classes.

We agree with the reviewer and attempted 3D classification using multiple smaller masks including the suggested region. However, the maps remained poorly defined, and we were unable to confidently assign the NTD.

(8) The authors don’t discuss whether the LPC-bound structures display changes in the external part of the pore, which is the anion-selective filter and the narrower part of the pore. If there are no conformational changes there, then the present structures cannot explain permeability to large molecules like ATP. In this context, a plot for the pore dimension will be helpful to see differences along the pore between their different structures. It would also be clearer if the authors overlaid maps of protomers to illustrate differences at the NTD and the "selectivity filter."

Both maps show that the narrowest constriction, formed by W74, has a diameter of approximately 9 Å. Previous steered molecular dynamics simulations suggest that ATP can permeate through such a constriction, implying an ion selection mechanism distinct from a simple steric barrier.

(9) The time between the addition of LPC to the nanodisc-reconstituted protein and grid preparation is not mentioned. Dynamic diffusion of LPC could result in equal probabilities for the bound and unbound forms. This raises the possibility of finding the Primed state in the LPC-bound state as well. Additionally, can the authors rationalize how LPC might reach the pore region when the channel is in the closed state before the application of LPC?

We appreciate the reviewer’s insight. We incubated LPC and nanodisc-reconstituted protein for 30 minutes, speculating that LPC approaches the pore similarly to other lipids in prior structures. In separate studies, we are optimizing conditions to capture more defined conformations.

(10) In the cryo-EM map of the “resting” state (EMDB-21150), a part of the density was interpreted as NTD flipped to the intracellular side. This density, however, is poorly defined, and not connected to the S1 helix, raising concerns about whether this density corresponds to the NTD as seen in the “resting” state structure (PDB-ID: 6VD7). In addition, some residues in the C-terminus (after K333 in frog PANX1) are missing from the atomic model. Some of these residues are predicted by AlphaFold2 to form a short alpha helix and are shown to form a short alpha helix in some published PANX1 structures. Interestingly, in both the AF2 model and 6WBF, this short alpha helix is located approximately in the weak density that the authors suggest represents the “flipped” NTD. We encourage the authors to be cautious in interpreting this part as the “flipped” NTD without further validation or justification.

We agree that the density corresponding the extended NTD into the cytoplasm is relatively weak. In our recent study, we compared two Panx1 structures with or without the mentioned C-terminal helix and found evidence suggesting the likelihood of NTD extension (DOI: 10.1101/2024.06.13.598903). Nevertheless, to prevent potential confusion, we have removed the cryo-EM panel from this manuscript.

(11) Since the authors did not observe densities of bound PLC in the cryo-EM map, it is important to acknowledge in the text the inherent limitations of using docking and mutagenesis methods to locate where PLC binds.

Thank you for the suggestion. We have removed this section to avoid potential confusion.

Optional suggestions:

(1) The authors used MeOH to extract mouse liver for reversed-phase chromatography. Was the study designed to focus on hydrophobic compounds that likely bind to the TMD? Panx1 has both ECD and ICD with substantial sizes that could interact with water soluble compounds? Also, the use of whole-cell recordings to screen fractions would not likely identify polar compounds that interact with the cytoplasmic part of the TMD? It would be useful for the authors to comment on these aspects of their screen and provide their rationale for fractionating liver rather than other tissues.

We have added a rationale in line 90, stating: “The soluble fractions were excluded from this study, as the most polar fraction induced strong channel activities in the absence of exogenously expressed pannexins.” Additionally, we have included a figure to support this rationale (Fig. S1A).

(2) The authors show that LPCs reversibly increase inward currents at a holding voltage of -60 mV (not always specified in legends) in cells expressing Panx1 and 2, and then show families of currents activated by depolarizing voltage steps in the absence of LPC without asking what happens when you depolarize the membrane after LPC activation? If LPCs can be applied for long enough without disrupting recordings, it would be valuable to obtain both I-V relations and G-V relations before and after LPC activation of Panx channels. Does LPC disproportionately increase current at some voltages compared to others? Is the outward rectification reduced by LPC? Does Vrev remain unchanged (see point above)? Its hard to predict what would be observed, but almost any outcome from these experiments would suggest additional experiments to explore the extent to which the open states activated by LPC and depolarization are similar or distinct.

Unfortunately, in our hands, the prolonged application of lysolipids at concentrations necessary to achieve significant currents tends to destabilize the patch. This makes it challenging to obtain G-V curves or perform the previously mentioned kinetic analyses. We believe this destabilization may be due to lysolipids’ surfactant-like qualities, which can disrupt the giga seal. Additionally, prolonged exposure seems to cause channel desensitization, which could be another confounding factor.

(3) From the results presented, the authors cannot rule out that mutagenesis-induced insensitivity of Panx channels to LPCs results from allosteric perturbations in the channels rather than direct binding/gating by LPCs. In Fig 5 panel A-C, the authors introduced double mutants on TM1 and TM2 to interfere with LPC binding, however, the double mutants may also disrupt the interaction network formed within NTD, TM1, and TM2. This disruption could potentially rearrange the conformation of NTD, favouring the resting closed state. Three double Asn mutants, which abolished LPC induced current, also exhibited lower currents through voltage activation in Fig 5S, raising the possibility the mutant channels fail to activate in response to LPC due to an increased energy barrier. One way to gain further insight would be to mutate residues in NTD that interact with those substituted by the three double Asn mutants and to measuring currents from both voltage activation and LPC activation. Such results might help to elucidate whether the three double Asn mutants interfere with LPC binding. It would also be important to show that the voltage-activated currents in Fig. S5 are sensitive to CBX?

Thank you for the comment, with which we agree. Our initial intention was to use the mutagenesis studies to experimentally support the docking study. Due to uncertainties associated with the presented cryo-EM maps, we have decided to remove this study from the current manuscript. We will consider the proposed experiments in a future study.

(4) Could the authors elaborate on how LPC opens Panx1 by altering the conformation of the NTDs in an uncoordinated manner, going from “primed” state to the “active” state. In the “primed” state, the NTDs seem to be ordered by forming interactions with the TMD, thus resulting in the largest (possible?) pore size around the NTDs. In contrast, in the “active” state, the authors suggest that the NTDs are fragmented as a result of uncoordinated rearrangement, which conceivably will lead to a reduction in pore size around NTDs (isn’t it?). It is therefore not intuitive to understand why a conformation with a smaller pore size represents an “active” state.

We believe the uncoordinated arrangement of NTDs is dynamic, allowing for potential variations in pore size during the activated conformation. Alternatively, NTD movement may be coupled with conformational changes in TM1 and the extracellular domain, which in turn could alter the electrostatic properties of the permeation pathway. We believe a functional study exploring this mechanism would be more appropriately presented as a separate study.

(5) Can the authors provide a positive control for these negative results presented in Fig S1B and C?

The positive results are presented in Fig. 1D and E.

(6) Raw images in Fig S6 and Fig S7 should contain units of measurement.

Thank you for pointing this out.

(7) It may be beneficial to show the superposition between primed state and activated state in both protomer and overall structure. In addition, superposition between primed state and PDB 7F8J.

We attempted to superimpose the cryo-EM maps; however, visually highlighting the differences in figure format proved challenging. Higher-resolution maps would allow for model building, which would more effectively convey these distinctions.

(8) Including particles number in each class in Fig S8 panel C and D would help in evaluating the quality of classification.

Noted.

(9) A table for cryo-EM statistics should be included.

Thanks, noted.

(10) n values are often provided as a range within legends but it would be better to provide individual values for each dataset. In many figures you can see most of the data points, which is great, but it would be easy to add n values to the plots themselves, perhaps in parentheses above the data points.

While we agree that transparency is essential, adding n-values to each graph would make some figures less clear and potentially harder to interpret in this case. We believe that the dot plots, n-value range, and statistical analysis provide adequate support for our claims.

(11) The way caspase activation of Panx channels is presented in the introduction could be viewed as dismissive or inflammatory for those who have studied that mechanism. We think the caspase activation literature is quite convincing and there is no need to be dismissive when pointing out that there are good reasons to believe that other mechanisms of activation likely exist. We encourage you to revise the introduction accordingly.

Thank you for this comment. Although we intended to support the caspase activation mechanism in our introduction, we understand that the reviewer’s interpretation indicates a need for clarification. We hope the revised introduction removes any perception of dismissiveness.

(12) Why is the patient data in Fig 4F normalized differently than everything else? Once the above issues with mVenus quenching data are clarified, it would be good to be systematic and use the same approach here.

For Fig. 4F, we used a distinct normalization method to account for substantial day-to-day variation in experiments involving body fluids. Notably, we did not apply this normalization to other experimental panels due to their considerably lower day-to-day variation.

(13) What was the rational for using the structure from ref 35 in the docking task?

The docking task utilized the human orthologue with a flipped-up NTD. We believe that this flipped-up conformation is likely the active form that responds to lysolipids. As our functional experiments primarily use the human orthologue for biological relevance, this structure choice is consistent. Our docking data shows that LPC does not dock at this site when using a construct with the downward-flipped NTD.

(14) Perhaps better to refer to double Asn ‘substitutions’ rather than as ‘mutations’ because that makes one think they are Asn in the wt protein.

Done.

(15) From Fig S1, we gather that Panx2 is much larger than Panx1 and 3. If that is the case, its worth noting that to readers somewhere.

We have added the molecular weight of each subtype in the figure legend.

(16) Please provide holding voltages and zero current levels in all figures presenting currents.

We provided holding voltages. However, the zero current levels vary among the examples presented, making direct comparisons difficult. Since we are comparing currents with and without LPC, we believe that indicating zero current levels is unnecessary for this study.

(17) While the authors successfully establish lysophospholipid-gating of Panx1 and Panx2, Panx3 appears unaffected. It may be advisable to be more specific in the title of the article.

We are uncertain whether Panx3 is unaffected by lysophospholipids, as we have not observed activation of this subtype under any tested conditions.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors investigate ligand and protein-binding processes in GPCRs (including dimerization) by the multiple walker supervised molecular dynamics method. The paper is interesting and it is very well written.

Strengths:

The authors' method is a powerful tool to gain insight on the structural basis for the pharmacology of G protein-coupled receptors.

We thank the Reviewer for the positive comment on the manuscript and the proposed methods.

Reviewer #2 (Public review):

The study by Deganutti and co-workers is a methodological report on an adaptive sampling approach, multiple walker supervised molecular dynamics (mwSuMD), which represents an improved version of the previous SuMD.

Case-studies concern complex conformational transitions in a number of G protein Coupled Receptors (GPCRs) involving long time-scale motions such as binding-unbinding and collective motions of domains or portions. GPCRs are specialized GEFs (guanine nucleotide exchange factors) of heterotrimeric Gα proteins of the Ras GTPase superfamily. They constitute the largest superfamily of membrane proteins and are of central biomedical relevance as privileged targets of currently marketed drugs.

MwSuMD was exploited to address:

a) binding and unbinding of the arginine-vasopressin (AVP) cyclic peptide agonist to the V2 vasopressin receptor (V2R);

b) molecular recognition of the β2-adrenergic receptor (β2-AR) and heterotrimeric GDPbound Gs protein;

c) molecular recognition of the A1-adenosine receptor (A1R) and palmotoylated and geranylgeranylated membrane-anchored heterotrimeric GDP-bound Gi protein;

d) the whole process of GDP release from membrane-anchored heterotrimeric Gs following interaction with the glucagon-like peptide 1 receptor (GLP1R), converted to the active state following interaction with the orthosteric non-peptide agonist danuglipron.

The revised version has improved clarity and rigor compared to the original also thanks to the reduction in the number of complex case studies treated superficially.

The mwSuMD method is solid and valuable, has wide applicability and is compatible with the most world-widely used MD engines. It may be of interest to the computational structural biology community.

The huge amount of high-resolution data on GPCRs makes those systems suitable, although challenging, for method validation and development.

While the approach is less energy-biased than other enhanced sampling methods, knowledge, at the atomic detail, of binding sites/interfaces and conformational states is needed to define the supervised metrics, the higher the resolution of such metrics is the more accurate the outcome is expected to be. Definition of the metrics is a user- and system-dependent process.

We thank the Reviewer for the positive comment on the revised manuscript and mwSuMD. We agree that the choice of supervised metrics is user- and systemdependent. We aim to improve this aspect in the future with the aid of interpretable machine learning.

Reviewer #3 (Public review):

Summary:

In the present work Deganutti et al. report a structural study on GPCR functional dynamics using a computational approach called supervised molecular dynamics.

Strengths:

The study has potential to provide novel insight into GPCR functionality. Example is the interaction between D344 and R385 identified during the Gs coupling by GLP-1R. However, validation of the findings, even computationally through for instance in silico mutagenesis study, is advisable.

Weaknesses:

No significant advance of the existing structural data on GPCR and GPCR/G protein coupling is provided. Most of the results are reproductions of the previously reported structures.

The method focus of our study (mwSuMD) is an enhancement of the supervised molecular dynamics that allows supervising two metrics at the same time and uses a score, rather than a tabù-like algorithm, for handing the simulation. Further changes are the seeding of parallel short replicas (walkers) rather than a series of short simulations, and the software implementation on different MD engines (e.g. Acemd, OpenMM, NAMD, Gromacs).

We agree with the Reviewer that experimental validation of the findings would be advisable, in line with any computational prediction. We are positive that future studies from our group employing mwSuMD will inform mutagenesis and BRET-based experiments.

Reviewer #2 (Recommendations for the authors):

As for GLP1R, I remain convinced that the 7LCI would have been better as a reference for all simulations than 7LCJ, also because 7LCI holds a slightly more complete ECD.

We agree that 7LCJ would have been a better starting point than 7LCI for simulations because it presents the stalk region, contrary to 7LCJ. However, we do not think it might have influenced the output because the stalk is the most flexible segment of GLP1R, and any initial conformation is usually not retained during MD simulations.

Please, correct everywhere the definition of the 6LN2 structure of GPL1R as a ligand-free or apo, because that structure is indeed bound to a negative allosteric modulator docked on the cytosolic end of helix-6

We thank the reviewer for this precision. The text has been modified accordingly.

As for the beta2-AR, the "full-length" AlphaFold model downloaded from the GPCRdb is not an intermediate active state because it is very similar to the receptor in the 3SN6 complex with Gs. Please, eliminate the inappropriate and speculative adjective "intermediate".

We have changed “intermediate” to “not fully active”, which is less speculative since full activation can be achieved only in the presence of the G protein.

Incidentally, in that model, the C-tail, eliminated by the authors, is completely wrong and occupies the G protein binding site. It is not clear to me the reason why the authors preferred to used an AlphaFold model as an input of simulations rather than a high resolution structural model, e.g. 4LDO. Perhaps, the reason is that all ICL regions, including ICL3, were modeled by AlphaFold even if with low confidence. I disagree with that choice.

We understand the reviewer’s point of view. Should we have simulated an “equilibrium” receptor-ligand complex, we would have made the same choice. However, the conformational changes occurring during a G protein binding are so consistent that the starting conformation of the receptor becomes almost irrelevant as long as a sensate structure is used.  

Reviewer #3 (Recommendations for the authors):

The revised version of the manuscript is more concise, focusing only on two systems. However, the authors have responded superficially to the reviewers' comments, merely deleting sections of text, making minor corrections, or adding small additions to the text. In particular, the authors have not addressed the main critical points raised by both Reviewer 2 and Reviewer 3. 

For example, the RMSD values for the binding of PF06882961 to GLP-1R remain high, raising doubts about the predictive capabilities of the method, at least for this type of system.

What is the RMSD of the ligand relative to the experimental pose obtained in the simulations? This value must be included in the text.

We have added this piece of information about PF06882961 RMSD in the text, which on page 6 now reads “We simulated the binding of PF06882961, reaching an RMSD to its bound conformation in 7LCJ of 3.79 +- 0.83 Å (computed on the second half of the merged trajectory, superimposing on GLP-1R Ca atoms of TMD residues 150 to 390), using multistep supervision on different system metrics (Figure 2) to model the structural hallmark of GLP-1R activation (Video S5, Video S6).”

Similarly, the activation mechanism of GLP-1R is only partially simulated.

Furthermore, it is not particularly meaningful to justify the high RMSD values of the SuMD simulations for the binding of Gs to GLP-1R by comparing them with those reported under unbiased MD conditions. "Replica 2, in particular, well reproduced the cryo-EM GLP-1R complex as suggested by RMSDs to 7LCI of 7.59{plus minus}1.58Å, 12.15{plus minus}2.13Å, and 13.73{plus minus}2.24Å for Gα, Gβ, and Gγ respectively. Such values are not far from the RMSDs measured in our previous simulations of GLP-1R in complex with Gs and GLP-149 (Gα = 6.18 {plus minus} 2.40 Å; Gβ = 7.22 {plus minus} 3.12 Å; Gγ = 9.30 {plus minus} 3.65 Å), which indicates overall higher flexibility of Gβ and Gγ compared to Gα, which acts as a sort of fulcrum bound to GLP-1R."

Without delving into the accuracy of the various calculations, the authors should acknowledge that comparing protein structures with such high RMSD values has no meaningful significance in terms of convergence toward the same three-dimensional structure.

The text has been edited to accommodate the reviewer’s suggestion and still give the readers the measure of the high flexibility of Gs bound to GLP-1R. It now reads “Such values do not support convergence with the static experimental structure but are not far from the RMSDs measured in our previous simulations of GLP-1R in complex with G_s and GLP-1 (G_α = 6.18 ± 2.40 Å; G_b = 7.22 ± 3.12 Å; G_g = 9.30 ± 3.65 Å), which indicates overall higher flexibility of G_b and G_g compared to G_α, which acts as a sort of fulcrum bound to GLP-1R.”

Have the authors simulated the binding of the Gs protein using the experimentally active structure of GLP-1R in complex with the ligand PF06882961 (PDB ID 7LCJ)? Such a simulation would be useful to assess the quality of the binding simulation of Gs to the GLP1R/PF06882961 complex obtained from the previous SuMD.

We considered performing the Gs binding simulation to the active structure of GLP-1R.

However, the GLP-1R (and other class B receptors) fully active state, as reported in 7LCJ, depends on the presence of the Gs and can be reached only upon effector coupling. Since it is unlikely that the unbound receptor is already in the fully active state, we reasoned that considering it as a starting point for Gs binding simulations would have been an artifact.

An example of the insufficient depth of the authors' replies can be seen in their response: "We note that among the suggested references, only Mafi et al report about a simulated G protein (in a pre-formed complex) and none of the work sampled TM6 rotation without input of energy."

This statement is inaccurate. For instance, D'Amore et al. (Chem 2024, doi: 10.1016/j.chempr.2024.08.004) simulated Gs coupling to A2A as well as TM6 rotation, as did Maria-Solano and Choi (eLife 2023, doi: 10.7554/eLife.90773.1). The former employed path collective variables metadynamics, which is not cited in the introduction or the discussion, despite its relevance to the methodologies mentioned.

Respectfully, our previous reply is correct, as all of the mentioned articles used enhanced (energy-biased) approaches, so the claim “none of the work sampled TM6 rotation without input of energy” stands. The reference to D’Amore et al. (published after the previous round of reviews of this manuscript) has been added to the introduction; we thank the reviewer for pointing it out. 

Additionally, SuMD employs a tabu algorithm that applies geometric supervision to the simulation, serving as an alternative approach to enhancing sampling compared to the "input of energy" techniques as called by the authors. A fair discussion should clearly acknowledge this aspect of the SuMD methodology.

We have now specified in the Methods that a tabù-like algorithm is part of SuMD, which, despite being the parent technique of mwSuMD, is not the focus of the present work. We provide extended references for readers interested in SuMD. mwSuMD, on the other hand, does not use a tabù-like algorithm but rather a continuative approach based on a score to select the best walker for each batch, as described in the Methods.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

This paper contains what could be described as a "classic" approach towards evaluating a novel taste stimuli in an animal model, including standard behavioral tests (some with nerve transections), taste nerve physiology, and immunocytochemistry of taste cells of the tongue. The stimulus being tested is ornithine, from a class of stimuli called "kokumi" (in terms of human taste); these kokumi stimuli appear to enhance other canonical tastes, increasing what are essentially hedonic attributes of other stimuli. The mechanism for ornithine detection is thought to be GPRC6A receptors expressed in taste cells. The authors showed evidence for this in an earlier paper with mice; this paper evaluates ornithine taste in a rat model, and comes to a similar conclusion, albeit with some small differences between the two rodent species.

Strengths:

The data show effects of ornithine on taste/intake in laboratory rats: In two-bottle and briefer intake tests, adding ornithine results in higher intake of most, but all not all stimuli tested. Bilateral chorda tympani (CT) nerve cuts or the addition of GPRC6A antagonists decreased or eliminated these effects. Ornithine also evoked responses by itself in the CT nerve, but mainly at higher concentrations; at lower concentrations it potentiated the response to monosodium glutamate. Finally, immunocytochemistry of taste cell expression indicated that GPRC6A was expressed predominantly in the anterior tongue, and co-localized (to a small extent) with only IP3R3, indicative of expression in a subset of type II taste receptor cells.

Weaknesses:

As the authors are aware, it is difficult to assess a complex human taste with complex attributes, such as kokumi, in an animal model. In these experiments they attempt to uncover mechanistic insights about how ornithine potentiates other stimuli by using a variety of established experimental approaches in rats. They partially succeed by finding evidence that GPRC6A may mediate effects of ornithine when it is used at lower concentrations. In the revision they have scaled back their interpretations accordingly. A supplementary experiment measuring certain aspects of the effects of ornithine added to Miso soup in human subjects is included for the express purpose of establishing that the kokumi sensation of a complex solution is enhanced by ornithine; however, they do not use any such complex solutions in the rat studies. Moreover, the sample size of the human experiment is (still) small - it really doesn't belong in the same manuscript with the rat studies.

Despite the reviewer’s suggestion, we would like to include the human sensory experiment. Our rationale is that we must first demonstrate that the kokumi of miso soup is enhanced by the addition of ornithine, which is then followed by basic animal experiments to investigate the underlying mechanisms of kokumi in humans.

We did not present the additive effects of ornithine on miso soup in the present rat study because our previous companion paper (Fig. 1B in Mizuta et al., 2021, Ref. #26) already confirmed that miso soup supplemented with 3 mM L-ornithine (but not D-ornithine) was statistically significantly (P < 0.001) preferred to plain miso soup by mice.

Furthermore, we believe that our sample size (n = 22) is comparable to those employed in other studies. For example, the representative kokumi studies by Ohsu et al. (Ref. #9), Ueda et al. (Ref. #10), Shibata et al. (Ref. #20), Dunkel et al. (Ref. #37), and Yang et al. (Ref. #44) used sample sizes of 20, 19, 17, 9, and 15, respectively.

Reviewer #2 (Public review):

Summary:

The authors used rats to determine the receptor for a food-related perception (kokumi) that has been characterized in humans. They employ a combination of behavioral, electrophysiological, and immunohistochemical results to support their conclusion that ornithine-mediated kokumi effects are mediated by the GPRC6A receptor. They complemented the rat data with some human psychophysical data. I find the results intriguing, but believe that the authors overinterpret their data.

Strengths:

The authors provide compelling evidence that ornithine enhances the palatability of several chemical stimuli (i.e., IMP, MSG, MPG, Intralipos, sucrose, NaCl, quinine). Ornithine also increases CT nerve responses to MSG. Additionally, the authors provide evidence that the effects of ornithine are mediated by GPRC6A, a G-protein-coupled receptor family C group 6 subtype A, and that this receptor is expressed primarily in fungiform taste buds. Taken together, these results indicate that ornithine enhances the palatability of multiple taste stimuli in rats and that the enhancement is mediated, at least in part, within fungiform taste buds. This is an important finding that could stand on its own. The question of whether ornithine produces these effects by eliciting kokumi-like perceptions (see below) should be presented as speculation in the Discussion section.

Weaknesses:

I am still unconvinced that the measurements in rats reflect the "kokumi" taste percept described in humans. The authors conducted long-term preference tests, 10-min avidity tests and whole chorda tympani (CT) nerve recordings. None of these procedures specifically model features of "kokumi" perception in humans, which (according to the authors) include increasing "intensity of whole complex tastes (rich flavor with complex tastes), mouthfulness (spread of taste and flavor throughout the oral cavity), and persistence of taste (lingering flavor)." While it may be possible to develop behavioral assays in rats (or mice) that effectively model kokumi taste perception in humans, the authors have not made any effort to do so. As a result, I do not think that the rat data provide support for the main conclusion of the study--that "ornithine is a kokumi substance and GPRC6A is a novel kokumi receptor."

Kokumi can be assessed in humans, as demonstrated by the enhanced kokumi perception observed when miso soup is supplemented with ornithine (Fig. S1). Currently, we do not have a method to measure the same kokumi perception in animals. However, in the two-bottle preference test, our previous companion paper (Fig. 1B in Mizuta et al. 2021, Ref. #26) confirmed that miso soup supplemented with 3 mM L-ornithine (but not D-ornithine) was statistically significantly (P < 0.001) preferred over plain miso soup by mice.

Of the three attributes of kokumi perception in humans, the “intensity of whole complex tastes (rich flavor with complex tastes)” was partly demonstrated in the present rat study. In contrast, “mouthfulness (the spread of taste and flavor throughout the oral cavity)” could not be directly detected in animals and had to be inferred in the Discussion. “Persistence of taste (lingering flavor)” was evident at least in the chorda tympani responses; however, because the tongue was rinsed 30 seconds after the onset of stimulation, the duration of the response was not fully recorded.

It is well accepted in sensory physiology that the stronger the stimulus, the larger the tonic response—and consequently, the longer it takes for the response to return to baseline. For example, Kawasaki et al. (2016, Ref. #45) clearly showed that the duration of sensation increased proportionally with the concentration of MSG, lactic acid, and NaCl in human sensory tests. The essence of this explanation has been incorporated into the Discussion (p. 12).

Why are the authors hypothesizing that the primary impacts of ornithine are on the peripheral taste system? While the CT recordings provide support for peripheral taste enhancement, they do not rule out the possibility of additional central enhancement. Indeed, based on the definition of human kokumi described above, it is likely that the effects of kokumi stimuli in humans are mediated at least in part by the central flavor system.

We agree with the reviewer’s comment. Our CT recordings indicate that the effects of kokumi stimuli on taste enhancement occur primarily at the peripheral taste organs. The resulting sensory signals are then transmitted to the brain, where they are processed by the central gustatory and flavor systems, ultimately giving rise to kokumi attributes. This central involvement in kokumi perception is discussed on page 12. Although kokumi substances exert their effects at low concentrations—levels at which the substance itself (e.g., ornithine) does not become more favorable or (in the case of γ-Glu-Val-Gly) exhibits no distinct taste—we cannot rule out the possibility that even faint taste signals from these substances are transmitted to the brain and interact with other taste modalities.

The authors include (in the supplemental data section) a pilot study that examined the impact of ornithine on variety of subjective measures of flavor perception in humans. The presence of this pilot study within the larger rat study does not really mice sense. While I agree with the authors that there is value in conducting parallel tests in both humans and rodents, I think that this can only be done effectively when the measurements in both species are the same. For this reason, I recommend that the human data be published in a separate article.

Despite the reviewer’s suggestion, we intend to include the human sensory experiment. Our rationale is that we must first demonstrate that the kokumi of miso soup is enhanced by the addition of ornithine, and then follow up with basic animal experiments to investigate the potential underlying mechanisms of kokumi in humans.

In our previous companion paper (Fig. 1B in Mizuta et al., 2021, Ref. #26), we confirmed with statistical significance (P < 0.001) that mice preferred miso soup supplemented with 3 mM L-ornithine (but not D-ornithine) over plain miso soup. However, as explained in our response to Reviewer #2’s first concern (in the Public review), it is difficult to measure two of the three kokumi attributes—aside from the “intensity of whole complex tastes (rich flavor with complex tastes)”—in animal models.

The authors indicated on several occasions (e.g., see Abstract) that ornithine produced "synergistic" effects on the CT nerve response to chemical stimuli. "Synergy" is used to describe a situation where two stimuli produce an effect that is greater than the sum of the response to each stimulus alone (i.e., 2 + 2 = 5). As far as I can tell, the CT recordings in Fig. 3 do not reflect a synergism.